{"http:\/\/dx.doi.org\/10.14288\/1.0416484":{"http:\/\/vivoweb.org\/ontology\/core#departmentOrSchool":[{"value":"Arts, Faculty of","type":"literal","lang":"en"},{"value":"Vancouver School of Economics","type":"literal","lang":"en"}],"http:\/\/www.europeana.eu\/schemas\/edm\/dataProvider":[{"value":"DSpace","type":"literal","lang":"en"}],"https:\/\/open.library.ubc.ca\/terms#degreeCampus":[{"value":"UBCV","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/creator":[{"value":"Ghosh, Arkadev","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/issued":[{"value":"2022-07-29T16:13:14Z","type":"literal","lang":"en"},{"value":"2022","type":"literal","lang":"en"}],"http:\/\/vivoweb.org\/ontology\/core#relatedDegree":[{"value":"Doctor of Philosophy - PhD","type":"literal","lang":"en"}],"https:\/\/open.library.ubc.ca\/terms#degreeGrantor":[{"value":"University of British Columbia","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/description":[{"value":"The first chapter implements a field experiment in India to understand whether the effects of religious diversity on team productivity and worker attitudes depend on a firm's production technology. I randomly assigned Hindu and Muslim workers at a manufacturing plant in West Bengal to religiously mixed or homogeneous teams. Production tasks are categorized as high- or low-dependency based on the degree of continuous coordination required for production. I find that mixed teams are less productive than homogeneous teams in high-dependency tasks, but this effect attenuates completely in four months. In low-dependency tasks, diversity does not affect productivity. Despite lowering short-run productivity, mixing improves out-group attitudes for Hindu workers in high-dependency tasks - but there are little or no effects in low-dependency tasks. Overall, this pattern of results suggests that technology that incentivizes individuals to learn to work together is important in overcoming existing intergroup differences - and leads to improved relations and team performance. \r\n\r\n The second chapter shows that close-kin marriage, by sustaining tightly-knit family structures, impedes development. We use US state-level bans on cousin marriage for identification. Our measure of cousin marriage comes from the excess frequency of same-surname marriages, a method borrowed from population genetics that we apply to millions of marriage records from 1800 to 1940. We show that state bans on first-cousin marriage did reduce rates of in-marriage, and that affected descendants therefore have higher incomes and more schooling. Our results are consistent with this effect being driven by weakening family ties rather than a genetic channel.\r\n  \r\nThe third chapter studies mining activity in Indian states and districts between 1960-2015, and finds that mining intensity gradually decreases as elections approach. This pattern is manifested in output, mining accidents, and mineral licensing. The magnitude of these cycles are determined primarily by two factors: electoral competition and the intensity of Naxalite conflict, an ongoing left-wing insurgency against the Indian government. While mining fatalities are costly during elections, I show that cycles in conflict prone areas are exacerbated in order to minimize the tax base of rebel groups, who thrive on extortion of mining revenues and target elections with violence.","type":"literal","lang":"en"}],"http:\/\/www.europeana.eu\/schemas\/edm\/aggregatedCHO":[{"value":"https:\/\/circle.library.ubc.ca\/rest\/handle\/2429\/82217?expand=metadata","type":"literal","lang":"en"}],"http:\/\/www.w3.org\/2009\/08\/skos-reference\/skos.html#note":[{"value":"Essays in Development EconomicsbyArkadev GhoshMA (Hons)., The University of Edinburgh, 2015M.Sc., The London School of Economics and Political Science, 2016A THESIS SUBMITTED IN PARTIAL FULFILLMENT OFTHE REQUIREMENTS FOR THE DEGREE OFDOCTOR OF PHILOSOPHYinThe Faculty of Graduate and Postdoctoral Studies(Economics)THE UNIVERSITY OF BRITISH COLUMBIA(Vancouver)July 2022\u00a9 Arkadev Ghosh 2022The following individuals certify that they have read, and recommend to the Faculty of Graduate andPostdoctoral Studies for acceptance, the dissertation titled:Essays in Development Economicssubmitted by Arkadev Ghoshin partial fulfillment of the requirements for the degree of Doctor of Philosophy in Economics.Examining Committee:Siwan Anderson, Professor, Economics, UBCCo-supervisorMunir Squires, Assistant Professor, Economics, UBCCo-supervisorClaudio Ferraz, Professor, Economics, UBCUniversity ExaminerArjun Chowdhury, Assistant Professor, Political Science, UBCUniversity ExaminerFarzana Afridi, Professor, Economics, Indian Statistical Institute, Delhi CenterExternal ExaminerAdditional Supervisory Committee MembersPatrick Francois, Professor, Economics, UBCSupervisory Committee MemberJamie McCasland, Assistant Professor, Economics, UBCSupervisory Committee MemberMatt Lowe, Assistant Professor, Economics, UBCSupervisory Committee MemberiiAbstractThe first chapter implements a field experiment in India to understand whether the effects of religious di-versity on team productivity and worker attitudes depend on a firm\u2019s production technology. I randomlyassigned Hindu and Muslim workers at a manufacturing plant in West Bengal to religiously mixed orhomogeneous teams. Production tasks are categorized as high- or low-dependency based on the degreeof continuous coordination required for production. I find that mixed teams are less productive thanhomogeneous teams in high-dependency tasks, but this effect attenuates completely in four months.In low-dependency tasks, diversity does not affect productivity. Despite lowering short-run productivity,mixing improves out-group attitudes for Hindu workers in high-dependency tasks \u2013 but there are little orno effects in low-dependency tasks. Overall, this pattern of results suggests that technology that incen-tivizes individuals to learn to work together is important in overcoming existing intergroup differences \u2013and leads to improved relations and team performance.The second chapter shows that close-kin marriage, by sustaining tightly-knit family structures, im-pedes development. We use US state-level bans on cousin marriage for identification. Our measure ofcousin marriage comes from the excess frequency of same-surname marriages, a method borrowed frompopulation genetics that we apply to millions of marriage records from 1800 to 1940. We show that statebans on first-cousin marriage did reduce rates of in-marriage, and that affected descendants thereforehave higher incomes and more schooling. Our results are consistent with this effect being driven byweakening family ties rather than a genetic channel.The third chapter studies mining activity in Indian states and districts between 1960-2015, and findsthat mining intensity gradually decreases as elections approach. This pattern is manifested in output,mining accidents, and mineral licensing. The magnitude of these cycles are determined primarily bytwo factors: electoral competition and the intensity of Naxalite conflict, an ongoing left-wing insurgencyiiiagainst the Indian government. While mining fatalities are costly during elections, I show that cycles inconflict prone areas are exacerbated in order to minimize the tax base of rebel groups, who thrive onextortion of mining revenues and target elections with violence.ivLay SummaryMy dissertation consists of three distinct chapters in development economics. The first chapter imple-ments a field experiment to understand whether the effects of religious diversity on team productionand worker attitudes depend on a firm\u2019s production technology. I find that in high-coordination tasks,diversity initially leads to lower productivity. But this effect dissipates over time and contact in thesetasks also leads to positive attitude change towards non-coreligionists. These effects are not present inlow-coordination tasks. The second chapter studies the effects of close-kin marriage on economic de-velopment outcomes such as income, schooling and female labor force participation. Using state banson cousin marriage in the U.S., we show that a reduction in first cousin marriages led to an improvementin these outcomes. The third chapter documents political business cycles in mining activity in India andexplores why in contrast to other economic activity, mineral extraction is minimized in election years.vPrefaceChapters 2 and 4 are pieces of original, unpublished and independent work. Chapter 2 involves humanparticipants. The protocol for the study was approved by UBC BREB with approval certificate numberH19-00729. Chapter 3 is joint work with Professor Munir Squires (UBC) and Professor Sam Hwang (UBC).I have been involved throughout each stage of research: collecting data, conceptualizing the researchdesign as well as conducting the empirical analysis.viTable of ContentsAbstract . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . iiiLay Summary . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . vPreface . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . viTable of Contents . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . viiList of Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xiiList of Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xvAcknowledgements . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xvii1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 12 Religious Divisions and Production Technology: Experimental Evidence from India . . . . . 112.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 112.2 Context . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 152.2.1 Hindu-Muslim relations in India . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 152.2.2 The Factory: Production lines and worker characteristics . . . . . . . . . . . . . . . . 162.2.3 Direct Dependency as a measure of production technology . . . . . . . . . . . . . . . 182.3 Research design . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 202.3.1 Treatment and randomization . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 212.3.2 Data collection, experiment timeline and attrition . . . . . . . . . . . . . . . . . . . . 232.3.3 Randomization check . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 24vii2.3.4 Quasi-random allocation of workers to tasks at baseline . . . . . . . . . . . . . . . . . 252.4 Econometric specification . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 252.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 272.5.1 Production data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 272.5.2 Endline phone survey . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 312.5.3 Robustness: Threats to identification . . . . . . . . . . . . . . . . . . . . . . . . . . . . 342.6 Mechanism . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 372.6.1 Assortative (mis)matching in complementary tasks . . . . . . . . . . . . . . . . . . . 382.6.2 Communication . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 382.6.3 Favored mechanism: Minority-stereotyping and discrimination . . . . . . . . . . . . 382.7 Policy discussion: Firm supervisor survey . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 412.8 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 432.9 Tables and figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 452.9.1 Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 452.9.2 Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 542.10 Full Model . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 582.10.1 Setup . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 582.10.2 One shot production . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 602.10.3 Analysis of the model . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 602.10.4 Proof of proposition . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 643 Economic Consequences of Kinship: Evidence from U.S. Bans on Cousin Marriage . . . . . . 673.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 673.2 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 713.2.1 Marriage records . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 713.2.2 Measuring cousin marriage using marriage records . . . . . . . . . . . . . . . . . . . 723.2.3 US cousin marriage rates . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 763.2.4 Census data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 783.3 Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 78viii3.3.1 State bans . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 793.3.2 Empirical specification . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 813.4 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 843.4.1 Effect of bans on cousin marriage rates . . . . . . . . . . . . . . . . . . . . . . . . . . . 843.4.2 Income and schooling . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 863.4.3 Congenital health effects . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 873.4.4 Labor supply . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 883.4.5 Geographic mobility and urbanization . . . . . . . . . . . . . . . . . . . . . . . . . . . 893.4.6 Robustness . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 913.5 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 923.6 Tables and figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 933.6.1 Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 933.6.2 Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1014 Elections, Accidental Deaths and Insurgency: Recipe for India\u2019s Conflict Minerals . . . . . . . 1024.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1024.2 Context . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1054.2.1 Politics in India . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1054.2.2 Mining in India . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1054.2.3 Naxal Violence: Origin, development and characteristics . . . . . . . . . . . . . . . . 1064.3 Conceptual framework . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1094.4 Data and descriptive statistics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1104.5 State-level analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1124.6 District-level analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1154.6.1 Electoral competition and mining cycles . . . . . . . . . . . . . . . . . . . . . . . . . . 1164.6.2 Mining cycles in the Red Corridor . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1204.6.3 Election cycles and Naxalite conflict intensity . . . . . . . . . . . . . . . . . . . . . . . 1224.7 Extensions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1254.7.1 Robustness . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 125ix4.7.2 Discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1274.8 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1294.9 Tables and figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1314.9.1 Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1314.9.2 Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1405 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 144Bibliography . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 147AppendicesA Appendix to Chapter 2 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 161A.1 Randomization steps, implementation timeline and balance (identification) checks . . . . 161A.1.1 Randomization steps and timeline . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 161A.1.2 Quasi-random allocation of workers to tasks at baseline . . . . . . . . . . . . . . . . . 164A.2 Treatment effect on standard output and output gap . . . . . . . . . . . . . . . . . . . . . . . 170A.3 Additional tables referred to in the main text . . . . . . . . . . . . . . . . . . . . . . . . . . . 173A.3.1 Summary statistics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 173A.3.2 Robustness checks and additional results . . . . . . . . . . . . . . . . . . . . . . . . . 175A.3.3 Spillovers . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 185A.4 Additional figures referred to in the main text . . . . . . . . . . . . . . . . . . . . . . . . . . . 188A.4.1 Figures from firm survey . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 194B Appendix to Chapter 3 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 196B.1 Marriage records . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 196B.1.1 Genealogical records . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 197B.1.2 Types of first-cousin marriages, and implications for measures of isonymy . . . . . 198B.1.3 Cousin marriage bans: Evidence from genealogical records . . . . . . . . . . . . . . . 202B.1.4 Census variable definitions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 205B.1.5 Predictors of state bans on cousin marriage . . . . . . . . . . . . . . . . . . . . . . . . 208xB.1.6 Non-random isonymy censoring . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 211B.2 Supplementary tables and figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 214C Appendix to Chapter 4 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 224C.1 Tables and figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 224C.2 Data appendix . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 233xiList of Tables2.1 Proportion Muslim by line-level team and cohort (at baseline) . . . . . . . . . . . . . . . . . 452.2 Characteristics of High- and Low-Dependency tasks . . . . . . . . . . . . . . . . . . . . . . . 462.3 Randomization check . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 472.4 Treatment effect on line-level output . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 482.5 Treatment effect on section ratings . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 492.6 Treatment effect on worker interactions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 502.7 Treatment effect on attitudes at endline: Hindus . . . . . . . . . . . . . . . . . . . . . . . . . 512.8 Heterogeneous attenuation by characteristics of Hindus at baseline (HD section ratings) . 522.9 Treatment effect on worker interactions: Decomposition (Mixed teams) . . . . . . . . . . . 532.10 Bayesian updating (Hindu workers): Prob(Muslim worker exerts eH ) . . . . . . . . . . . . . 613.1 Summary statistics: Marriage records . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 933.2 Calculating cousin marriage rates from isonymy, examples from Tennessee . . . . . . . . . 933.3 Year of enactment of state laws banning first-cousin marriage . . . . . . . . . . . . . . . . . 943.4 Impact of bans on cousin marriage rates . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 953.5 Impact of cousin marriage bans on income and schooling . . . . . . . . . . . . . . . . . . . . 963.6 Income, schooling and urbanization: Placebo regressions from 1850-1940 Censuses . . . . 973.7 Impact cousin marriage bans on genetic outcomes . . . . . . . . . . . . . . . . . . . . . . . . 983.8 Impact of cousin marriage bans on labor supply . . . . . . . . . . . . . . . . . . . . . . . . . . 993.9 Impact of cousin marriage bans on urbanization . . . . . . . . . . . . . . . . . . . . . . . . . 1004.1 Summary statistics of key variables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1314.2 Mining lease distribution and years to scheduled election . . . . . . . . . . . . . . . . . . . . 132xii4.3 Mining output and years to scheduled election . . . . . . . . . . . . . . . . . . . . . . . . . . 1334.4 Fatal mining accidents and years to scheduled election (Poisson) . . . . . . . . . . . . . . . 1344.5 Mining fatalities and years to scheduled election (district-level) . . . . . . . . . . . . . . . . 1354.6 Electoral cycle, political competition and mining fatalities . . . . . . . . . . . . . . . . . . . . 1364.7 Electoral cycle, Red Corridor and mining fatalities . . . . . . . . . . . . . . . . . . . . . . . . . 1374.8 Election cycles and Naxalite conflict (Poisson regressions) . . . . . . . . . . . . . . . . . . . . 1384.9 Elections and coal mine explosives . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 139A.1 Dependency switches . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 164A.2 Dependency sorting . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 165A.3 Dependency sorting: Omitting workers shifted from shut production line . . . . . . . . . . 166A.4 Balance in proportion Muslim . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 167A.5 Randomization check . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 168A.6 Randomization check (Line-level treatment indicator) . . . . . . . . . . . . . . . . . . . . . . 169A.7 Treatment effect on line-level standard output . . . . . . . . . . . . . . . . . . . . . . . . . . . 171A.8 Treatment effect on standard deviation of output gap . . . . . . . . . . . . . . . . . . . . . . . 172A.9 Summary statistics: Hindu and Muslim workers . . . . . . . . . . . . . . . . . . . . . . . . . . 173A.10 Summary statistics: Mean differences (physical environment) . . . . . . . . . . . . . . . . . 174A.11 Treatment effect on output (Line \u00d7 Variety fixed effects) . . . . . . . . . . . . . . . . . . . . . 175A.12 Treatment effect on output (Line \u00d7 Day fixed effects) . . . . . . . . . . . . . . . . . . . . . . . 175A.13 Treatment effect on section ratings . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 176A.14 Treatment effect on section ratings (without controls collinear with religion) . . . . . . . . . 177A.15 Treatment effect on section ratings: Event study . . . . . . . . . . . . . . . . . . . . . . . . . . 178A.16 Treatment effect on worker interactions: Hindus respondents only . . . . . . . . . . . . . . . 179A.17 Treatment effect on section ratings: Adding key controls . . . . . . . . . . . . . . . . . . . . . 180A.18 Proportion of old teammates . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 181A.19 Section change and treatment status . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 181A.20 Heterogeneous attenuation by characteristics of Hindus at baseline (LD section ratings) . . 182A.21 Treatment effect on worker interactions: Decomposition (Mixed teams by dependency) . . 183xiiiA.22 Religious violence and section ratings . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 184A.23 Treatment effect on line-level performance (aggregated section ratings) . . . . . . . . . . . . . . . 184A.24 Inter-religious contact (outside work) and section ratings . . . . . . . . . . . . . . . . . . . . 185A.25 Attrition . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 185A.26 Treatment effect on line-section-level ratings . . . . . . . . . . . . . . . . . . . . . . . . . . . 187A.27 Treatment effect on section ratings (HD after LD) . . . . . . . . . . . . . . . . . . . . . . . . . 188B.1 Genealogical data and Isonymy . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 202B.2 Effect of bans on cousin marriage rates (genealogical records) . . . . . . . . . . . . . . . . . 204B.3 DID Regressions: Impact of bans on ratio of cousin marriage types . . . . . . . . . . . . . . 205B.4 Early versus late bans and state characteristics . . . . . . . . . . . . . . . . . . . . . . . . . . . 209B.5 Pre-trends in isonymy rates . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 210B.6 Impact of bans on cousin marriage rates (Year Bins) . . . . . . . . . . . . . . . . . . . . . . . 214B.7 Cousin marriage rates in levels . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 215B.8 Robustness to threshold choice . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 216B.9 Dropping top and bottom 5% of common surnames . . . . . . . . . . . . . . . . . . . . . . . 217B.10 Including all states (including states that never banned) . . . . . . . . . . . . . . . . . . . . . 218B.11 1930 Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 219B.12 Robustness to years of compulsory schooling . . . . . . . . . . . . . . . . . . . . . . . . . . . 220B.13 Robustness to years of statehood . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 221B.14 Robustness to percent native population . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 222C.1 Election cycle and fatal mining accidents (State-Level) (OLS) . . . . . . . . . . . . . . . . . . 224C.2 Election cycle and mining fatalities (district-level) . . . . . . . . . . . . . . . . . . . . . . . . . 225C.3 Mining cycles, literacy rates and Scheduled Tribe population . . . . . . . . . . . . . . . . . . 228C.4 Correlates of mining fatalities and Naxalite conflict . . . . . . . . . . . . . . . . . . . . . . . . 228C.5 Primary data sources . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 233xivList of Figures2.1 Structure of production lines . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 542.2 Distribution of Direct Dependency . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 552.3 Randomized team structure . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 552.4 Experimental design and timeline . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 562.5 Treatment effect on line-level output (Event study) . . . . . . . . . . . . . . . . . . . . . . . . 572.6 Ethnic diversity and the manufacturing industry . . . . . . . . . . . . . . . . . . . . . . . . . 573.1 Persistence in cousin marriage rates by surname . . . . . . . . . . . . . . . . . . . . . . . . . 1013.2 Consanguinity and income (Cross-country correlation) . . . . . . . . . . . . . . . . . . . . . 1014.1 Sample for district-level study . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1404.2 Distribution of close elections . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1414.3 Accident cycles and electoral competition . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1414.4 Fatality cycles and electoral competition . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1424.6 Total conflict deaths over the electoral cycle . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1424.5 Accident cycles and Red Corridor . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 143A.1 Randomized steps (From baseline structure to randomized teams) . . . . . . . . . . . . . . 163A.2 Percentage deviation from standard output . . . . . . . . . . . . . . . . . . . . . . . . . . . . 171A.3 Deviation from standard output . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 172A.4 Sub-sample analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 186A.5 Structure of production lines . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 188A.6 High- and Low-Dependency sections . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 189A.7 Religious composition of lines and cohorts at baseline . . . . . . . . . . . . . . . . . . . . . . 190xvA.8 High- and Low-Dependency tasks . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 191A.9 Treatment effect on standard output (Event study) . . . . . . . . . . . . . . . . . . . . . . . . 192A.10 Distribution of actual line output and section ratings . . . . . . . . . . . . . . . . . . . . . . . 192A.11 Line output and section ratings . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 193A.12 Correlating IAT scores with survey responses . . . . . . . . . . . . . . . . . . . . . . . . . . . . 193A.13 Characteristics of HD and LD tasks . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 194A.14 Religious mixing and productivity by task type . . . . . . . . . . . . . . . . . . . . . . . . . . . 194A.15 Willingness to segregate workers by religion\/age . . . . . . . . . . . . . . . . . . . . . . . . . 195B.1 Marriage certificate . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 196B.2 Individuals with non-missing ancestral links (genealogical data) . . . . . . . . . . . . . . . . 199B.3 Cousin marriage and isonymy . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 200B.4 Types of first-cousin marriages . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 201B.5 Type 1 first-cousin marriages (Familinx) and isonymy (marriage records) . . . . . . . . . . . 203B.6 Surname Frequency and Zero NR Isonymy Rejection . . . . . . . . . . . . . . . . . . . . . . . 212B.7 Enforcement of cousin marriage bans in the news . . . . . . . . . . . . . . . . . . . . . . . . . 223C.1 Election cycle and mining intensity (state-level coefficient plots) . . . . . . . . . . . . . . . . 226C.2 Scheduled vs unscheduled elections and mining output \u2013 placebo test . . . . . . . . . . . . 227C.3 Red Corridor in Andhra Pradesh and Orissa . . . . . . . . . . . . . . . . . . . . . . . . . . . . 229C.4 Fatality cycles and Red Corridor (state fixed effects) . . . . . . . . . . . . . . . . . . . . . . . . 230C.5 Fatality cycles and Red Corridor (state fixed effects) . . . . . . . . . . . . . . . . . . . . . . . . 230C.6 Naxal rebel deaths over the election cycle . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 231C.7 Security forces deaths over the election cycle . . . . . . . . . . . . . . . . . . . . . . . . . . . . 231C.8 Accident cycles and electoral competition . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 232C.9 Fatality cycles and electoral competition . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 232C.10 Electoral cycle and accident probability (raw data) . . . . . . . . . . . . . . . . . . . . . . . . 233C.11 Electoral cycle, close elections and mining accidents (local polynomial) . . . . . . . . . . . 234xviAcknowledgementsI would like to express my deepest gratitude to Siwan Anderson, Patrick Francois, Matt Lowe, Jamie Mc-Casland and Munir Squires for their incredible support, advice and patience throughout my time at UBC.I am greatly indebted to Patrick Baylis, Victor Couture, Claudio Ferraz, David Green, Sam Hwang, AshokKotwal, Thomas Lemieux, Nathan Nunn, Thorsten Rogall and other participants at the empirical anddevelopment brown-bag seminars at the Vancouver School of Economics for their feedback.I have been extremely fortunate to share my PhD journey with some wonderful colleagues at the VSEwho have helped me more than they can imagine. I would like to especially thank Spreeha Aggarwal,Anand Chopra, Sudipta Ghosh, Nadhanael GV, Leo Ma, Aruni Mitra, Federico Guzman, Anubhav Jha,Dashleen Kaur, Ronit Mukherjee, Clemens Possnig, Catherine van der List and Dongxiao Zhang.I want to thank my friends outside of the PhD especially, Aritra Chowdhury, Abhirup Majumder andDevjyoti Paul for their wholesome support and companionship.I thank my parents, sister and the memories of my grandparents for their unconditional love, supportand sacrifice \u2013 none of this would be possible without them. Finally, I would like to thank my partner Aa-heli for bearing with me and absorbing a lot of the burden that came with this journey. This achievementis as much yours as mine.xviiChapter 1IntroductionThis thesis consists of three distinct chapters in development economics. The first chapter implementsa field experiment in India to understand whether the effects of religious diversity on team productionand worker attitudes depend on a firm\u2019s production technology. The second chapter examines the effectsof close-kin marriage on a range economic development outcomes. In particular, it uses 19th and 20thcentury state bans on cousin marriage in the U.S. to identify the causal effect of weakening family ties onincome, education and female labor force participation. Broadly speaking, the first two chapters explorethe common theme of understanding how social integration (as well as weaker in-group ties) affectseconomic outcomes. By contrast, the third chapter focuses on political business cycles in a developingcountry context. It studies election cycles in several aspects of mining activity (output, licensing andfatalities) in India and aims to understand why in contrast to other economic activity, mineral extractionis minimized in election years.Ethnic diversity in manufacturing firms is often associated with lower output due to poor social tiesand taste based among workers (Becker, 1957; Lazear, 1998; Hjort, 2014). However, there is very littleevidence on how these effects are determined by the nature of production or about the long-run effectsof diversity in firms. The first chapter implements a field experiment in a modern factory in West Bengalto estimate the short- and long-run effects of religious mixing on team productivity and inter-grouprelations under different production technologies.I partnered with a large processed food manufacturing plant in West Bengal India, that employs bothHindus and Muslims. There are multiple production tasks at this factory. With time-use data on thenature of contact amongst workers, I classify these tasks into two broad categories: High-Dependency(HD) and Low-Dependency (LD). This classification is based on the degree of continuous coordinationrequired amongst workers performing a task to ensure uninterrupted production, and the dependence1on teammates for breaks. Worker effort choices have a higher degree of complementarity in HD tasksthan in LD tasks, where workers are required to coordinate intermittently.Two important features of my experimental design are important for identification. The first is that Irandomly assign nearly 600 workers to religiously mixed or homogeneous teams. The second is that thefirm follows a quasi-random method of allocating workers to tasks. Together, they allow me to attributedifferent effects of religious mixing in HD and LD tasks to production technology differences rather thandifferences in characteristics of workers in these tasks. I kept the worker teams intact for a period of fourmonths in order to estimate dynamic effects of mixing.The study uncovers three key findings. The first is that religious diversity negatively affects teamoutput, but only in HD tasks. In LD tasks, religious diversity is costless. The second key finding is thatthe difference in output between HD-Mixed and HD Non-mixed teams attenuate completely by the endof the fourth month. The third key finding is that, at endline, there is a reduction in negative out-groupattitudes for Hindu workers, which is substantially larger from mixing in HD teams compared to LDteams. This is despite the fact that mixed HD teams suffered negative output shocks. In LD teams,mixing has little or no effects on attitudes of Hindus.There could be multiple plausible explanations for these core findings. First, I rule out that theseresults are driven simply by average differences in productivity between Hindus and Muslims \u2013 I showthat Hindus and Muslims are equally productive in this context. Second, the fact that there are no ef-fects from religious mixing in LD tasks further rules out other explanations based on social reputationconcerns around in-group members (Afridi et al., 2020) or distaste for out-group members (Hjort, 2014).Teams in LD tasks are still required to coordinate on many aspects of production even though workerefforts have lower complementarity. Instead, I argue that the effects are driven by the majority group(Hindus) having negative stereotypes about the minority group (Muslims), which leads to the formerexerting low effort in high coordination tasks. While it is statically optimal for Muslim workers to alsoexert low effort in this scenario, given a long enough interaction period, Muslims exert high effort tochange stereotypes against them. Hindu workers gradually update their priors, bringing about positiveproduction and attitudinal changes over time. Muslim workers gain from a high-output equilibrium inthe long-run.2This chapter contributes to work on ethnic diversity and firm production. Several papers documentnegative effects of ethnic diversity on productivity (Hjort, 2014; Afridi et al., 2020; Parrotta et al., 2012;Hamilton et al., 2012; Churchill et al., 2017). Hjort (2014) exploits quasi-random variation in the ethniccomposition of teams in a Kenyan flower plant and finds that ethnically mixed teams have lower pro-ductivity due to taste-based discrimination. Afridi et al. (2020) exploit variation in the caste compositionof teams caused by worker absenteeism in Indian garment factories and show that caste homogeneityboosts productivity. Going beyond these papers, I show how differences in the incentives to interactwith co-workers due to production function differences, affect team productivity. Second, I estimate thedynamic effects of repeated inter-group contact on team production and social preferences in the samesetting. Past studies exploit frequent team switching for identification and thus are not able to identifysuch effects. My results emphasize the need for intergroup contact to occur for a sufficiently long periodof time because the minority group does not have the incentive to invest in shifting priors of the major-ity group otherwise. The disincentive to invest in out-group members in short-term interactions couldexplain why in firms where teams are frequently switched, a history of being in mixed teams does notreduce prejudice and discrimination (Hjort, 2014).I also add to work on social preferences at the workplace (Bandiera et al., 2010, 2013; Mas and Moretti,2009; Carpenter and Seki, 2011; Hjort, 2014; Ashraf and Bandiera, 2018). I show that in the Indian con-text, factory workers discriminate against non-coreligionists leading to output losses. The plant I studyoffers a flat monthly wage to its employees. The wage-level is based on seniority and experience at thefirm. This is different from the setting in the majority of other papers on this topic, which study teamproductivity under group versus individual pay structures. I show that even without explicit daily payincentives, social preferences at the workplace can have large effects on team productivity.This chapter also relates closely to the literature on how social preferences are formed (Fershtmanand Gneezy, 2001; Boisjoly et al., 2006; Jakiela et al., 2011; Mousa, 2018; Rao, 2019) and how the effects ofintergroup contact depend upon the type and nature of contact (Allport et al., 1954; Pettigrew et al., 2011;Bazzi et al., 2017; Paluck et al., 2019). Lowe (2021) shows experimentally that intergroup contact has dif-ferent effects based on the type of contact. While Lowe (2021) creates two types of contact (collaborativeand adversarial) in a sport setting, I use naturally occurring variation in contact driven by production3function differences in a firm setting.Finally, the literature on employer learning in the U.S. (Farber and Gibbons, 1996; Altonji and Pierret,1998; Altonji and Pierret, 2001; Lange, 2007) argues that if firms discriminate amongst workers based oneasily observable characteristics (such as race), then as employers begin to observe (noisy) indicatorsof workers\u2019 performances, the initial information should gradually become redundant. I show that thisholds true for co-workers in a team production setting.The second chapter of the thesis focuses on the role of weakening kinship ties on development. Loosekinship ties have been linked to greater urbanization, economic growth and is thought to have been keyto the historical development of Europe (Enke, 2019; Henrich, 2020). Alesina and Giuliano (2014) havelinked strong family ties to lower contemporary growth rates through their negative effect on generalizedtrust, mobility and female labor force participation. However, direct casual evidence underlying this linkis largely missing.We use an exogenous decline in the rate of marriage between first cousins to estimate the effect ofweakening family ties on range of socio-economic outcomes. We use 19th and 20th century data fromthe US, where state-level bans on first-cousin marriage allow us to causally estimate the effect of cousinmarriage. While now rare, we estimate that 5% of marriages were between first cousins in the US between1800-1850. Thirty-two US states have banned first-cousin marriage, starting with Kansas in 1858. Weuse the timing of the these bans, and the resulting decline in cousin marriage due to their impositionto establish causality. Families with high initial rates of cousin marriage are more likely to have beenexposed to these bans than those with low rates of cousin marriage. Indeed, we show that families withhigh initial rates of cousin marriage see larger drops in these rates in states with early bans. We exploitthis for identification.We measure cousin marriage rates at the surname-level using a method from population geneticswhich we apply to 18 million marriage records between 1800 to 1940. This method relies on the excessfrequency of marriages where spouses share a surname. While it is widely used to estimate cousin mar-riage rates in a population (Crow and Mange, 1965), this is the first paper to use the method in economicsand we apply it to a far larger set of marriages than, to the best of our knowledge, has been done in otherdisciplines. We track cousin marriage rates over time by surname and link these surname-level rates of4cousin marriage to individual economic outcomes in the full count 1850 to 1940 Censuses that includefull names.Our treatment variable is the interaction of surname-level variation in cousin marriage with state-level variation in the duration of bans on such marriages. Specifically we interact (1) the cousin marriagerate for a surname in the pre-period (1800-1858, before the first ban was introduced), and (2) how longa state had banned cousin marriage. This allows us to compare a targeted population of high-cousin-marriage families across states with differential exposure to the timing of bans, rather than simply an-alyzing the effect on state-wide outcomes. We control for state-specific fixed effects to account for anyconfounding variation at the state-level. The key assumption for causal interpretation of our coefficientsis the following: the timing of bans on cousin marriage should not be correlated with factors that affectthe relative outcomes of surnames with initially high versus low rates of cousin marriage. We discuss andaddress possible threats to this identification strategy in the introduction to the chapter.Our first result is to show that the state bans on cousin marriage were indeed effective. We findthat they reduced cousin marriages by about 50% (on average over the entire post-period i.e. between1859-1940), with the effects being larger in states where bans were introduced earlier. We confirm thisresult using a separate dataset drawn from genealogical records which allows us to identify \u2018true\u2019 cousinmarriage rates, rather than infer them from the frequency of same-surname marriages. We find similarestimates using this alternative dataset which suggests that our primary measure, while noisy, is correcton average.We use variation in the extent to which a surname was exposed to a state ban and find that greaterexposure led to higher incomes i.e. surnames with high initial cousin marriage rates experienced dis-proportionately larger increases in income. We also find positive effects on schooling. Importantly, wefind that the gap in income levels in 1940 between individuals with differential exposure to the bans wasabsent in 1850, prior to the first ban. This rules out that our results are driven by pre-existing differences.To complement this, we further show that relative gains in income for high-cousin marriage surnamesappear only a few generations after the bans start being enacted.We explore the relationship between consanguinity and congenital health problems as a potentialexplanation for our findings. However, we do not find that cousin marriage bans affected rates of insti-5tutionalization due to physical or mental health issues. Rather, we find large increases in rural-urbanmigration as well as increases in female labor supply caused by the bans. We thus gravitate to an expla-nation based on the weakening of tight kinship, since past literature has pointed to these outcomes asmarkers of weaker family ties.Our findings add to the literature on the effect of kinship on economic and political outcomes. Ourcausal micro evidence supports the finding of this literature that tight kinship hinders political and eco-nomic modernization. This work typically uses pre-modern measures of kinship tightness from Murdock(1949)\u2019s Ethnographic Atlas and links them to contemporary outcomes (Lowes, 2020; Akbari et al., 2019;Bau, 2021; Schulz et al., 2019; Moscona et al., 2020). Notably, Enke (2019) finds that cultures with higherkinship tightness exhibit more in-group favoritism and hold communal, rather than universal, moralvalues. Further, he shows that with the onset of the industrial revolution societies with loose kinship ex-perienced faster economic development. Complementary work uses survey measures of the strength offamily ties and links these to rich individual-level data on household composition, political participationand economic outcomes (Alesina and Giuliano, 2010, 2014; Ermisch and Gambetta, 2010). Our 19th andearly-20th century US setting offers a window into a society undergoing a substantial shift in marriagepractices while providing individual-level, population-scale data.The practice of cousin marriage in particular has been a focus of this literature. This has partly beendriven by the influential idea that restrictions on unions between cousins loosened kinship bonds inEurope and led to the development of the modern world (Goody, 1983; Schulz et al., 2019; Henrich, 2020).Schulz (2019) and Akbari et al. (2019) find supportive evidence for this, showing that cousin marriageis linked to worse institutional outcomes and higher corruption. Research in contemporary societieshas focused instead on the functional benefits of cousin marriage (Do et al., 2013; Mobarak et al., 2013;Edlund, 2018; Hotte and Marazyan, 2020).1 The reasons they emphasize, dowry payments, inheritance,and the provision of kin-based insurance, may have been relatively unimportant in the 19th centuryUS, leading the practice to eventually die out.2 Another rationale for its disappearance in the US was1These may explain the continued widespread practice of cousin marriage in many contemporary societies: Bittles (2001)estimates that about 10% of marriages worldwide are between first or second cousins. An alternative interpretation is the highdegree of persistence in the custom of cousin marriage, as seen in Giuliano and Nunn (2020).2Similarly, Munshi and Rosenzweig (2016) argue that kinship (caste) insurance networks reduce rates of rural-to-urban mi-gration, which is consistent with our findings.6growing concern over its genetic consequences. However, recent surveys have concluded that the healthconsequences of cousin marriages are modest and do not justify legal restrictions (Bittles, 2012; Bennettet al., 2002). Mobarak et al. (2019) offer the best causal micro evidence available on this, using unmarriedopposite-sex cousins as an instrument for cousin marriage. Their findings suggest that observationalestimates of the negative consequences of cousin marriage on child health are exaggerated and that thetrue effects are small.Our use of surnames to measure kinship and marital ties builds on work such as Cruz et al. (2017);Fafchamps and Labonne (2017) and Angelucci et al. (2010). Buonanno and Vanin (2017), in work con-ceptually related to our own, find that low surname diversity in Italian localities (evidence of in-marriageand limited migration) predicts higher tax evasion but lower crime rates. This is consistent with the ideathat cousin marriage generates cohesion within the group at the expense of those outside of it.The third chapter of this thesis studies mining activity between Indian state elections. A large bodyof literature has focused on understanding political business cycles i.e. how opportunistic politiciansstimulate the economy before elections taking advantage of myopic voters (Cole, 2009; Bhattacharjee,2014; Baskaran et al., 2015). These papers typically find a U-shape pattern in economic activity betweenelections with the level of activity being greater in election years \u2013 since this helps to create a positive per-ception of those running for office. I study several aspects of mining intensity (mining output, minerallicensing, accidents) in India and document exactly the opposite pattern \u2013 mining intensity increasesafter state elections and gradually dampens leading up to the next election.I construct a new state- and district-level dataset from India and first document the existence of po-litical cycles in mineral licensing, mining output as well as accidents at the state-level. I then use district-level data to understand how the magnitude of these cycles are affected by (1) electoral competition and(2) conflict (the Naxalite Insurgency in India). I focus on the Naxalite insurgency because extortion frommining companies is believed to be an important source of funding for the rebel groups. I show thatboth electoral competition and the propensity of conflict intensifies mining cycles. Politically compet-itive districts as well as conflict prone districts exhibit larger reduction in mining accidents in electionyears. While mining fatalities are costly during elections in general, I argue that the disproportionatelylarger reductions in mining activity in conflict prone districts is driven likely by politicians\u2019 objective of7minimizing the rebels\u2019 resource base before elections. This is in the interests of politicians because thesegroups systematically target elections with violence. Finally, I study the intensity of conflict over theelectoral cycle and find that while average levels of violence are not significantly different across miningand non-mining districts, electoral violence is relatively lower in mining districts. This suggests strategicbehavior on the part of politicians. Politicians do not directly influence small businesses owners, con-tractors or even poor villagers who the rebels \u201ctax\" (in non-mining areas) (Kujur, 2009), but with theirlarge scale involvement in the mineral industry in India (Asher and Novosad, 2018), they are able to ma-nipulate activity in a way that suits their electoral agenda.In addition to the main results, I find that mining cycles are larger in districts with greater Sched-uled Tribe (ST) population and more diffused in states with higher literacy rates. A large section of mineworkers belong to the ST community (Srivastava, 2005) in India. As a result, accidents are more likely tobe electorally sensitive in districts having a larger voter base from the same community. Higher literacyrates are generally associated with greater demand for political accountability and lower propensity ofexhibiting voter myopia, which could explain these patterns. Overall, this chapter provides new findingson electorally driven political behavior in an industry marred with severe corruption and conflict in In-dia, analyzes the effect of both fixed and time-varying factors on such behavior, and also sheds light onconsequences of such behavior on resource related conflict.Models of political cycles were first developed by Nordhaus (1975) and Lindbeck (1976). The basisof their argument is that opportunistic politicians stimulate the economy before elections taking advan-tage of myopic voters. Thereafter, Rogoff and Sibert (1988) and Persson and Tabellini (1990) in a separateset of models argued that policy makers signal their ability by creating favourable economic conditionsbefore elections, leading to the emergence of political cycles. The evidence from the empirical literaturein developed countries is mixed. Berger and Woitek (1997) find elections to exert significant influenceon economic output in both Germany and the United States. Veiga and Veiga (2007) document electoralmanipulation in the provision of \u201cvisible\" collective goods in Portuguese municipality elections. On theother hand, McCallum (1978) and Klein (1996) reject the hypothesis that macroeconomic outcomes areinfluenced by elections in the United States. Evidence from the developing world though more recent,is now growing. Gonzalez (2002) shows that the Mexican government systematically uses fiscal policy8before elections to obtain votes. Drazen and Eslava (2010) find that in Colombia infrastructure spendingincreases before elections. In the Indian context, Cole (2009) shows that agricultural credit increases inthe years running up to a state election and more significantly so in districts with a smaller win marginin the previous election. This cycle is generated only by public and not private banks. He however failsto find any impact of such credit expansions on agricultural output. Khemani (2004) also focuses on In-dia and shows that fiscal instruments are targeted in election years to provide favours to pivotal votinggroups. Similarly, Saez and Sinha (2010) find that public expenditure in health and education increasesprior to elections in Indian states.Evidence on political corruption associated with the mineral industry in India is limited, thoughthere is plenty of anecdotal evidence documenting illegal practice. In a recent paper, Asher and Novosad(2018) show that global mining booms in the pre-election period result in criminal politicians runningfor political office and also winning with greater probability. In the post-election period such boomslead to politicians committing more violent crimes and accumulating greater wealth during their time inoffice.There is a strong correlation between the presence of minerals and intensity of India\u2019s Naxalite con-flict. Extortion of mining revenues by rebels is believed to fuel insurgency in India\u2019s \u201cRed Corridor\".Majority of the empirical work on Naxalite violence that study static predictors of conflict intensity, ac-knowledge mineral presence to be a strong determinant (see Ghatak and Eynde, 2017; Hoelscher et al.,2012). Vanden Eynde (2016) finds that negative labour income shocks (measured by deficient rainfall)intensify violence against government forces, but only in districts where the rebels\u2019 tax base is indepen-dent of local labour productivity (mining districts). When hit by a negative income shock, villagers aretempted to join the rebellion but only in mining districts where rebel groups are able to match theirreservation wage, since their resource base is not dependent on local labour productivity. In non-miningdistricts, civilians are tempted to become police informants instead, leading to higher violence againstcivilians.This chapter, though similar in spirit to the literature on political cycles, documents a counter cycli-cal (inverted U-shape) pattern in mining activity between Indian state elections. Minimizing industrialfatalities which are electorally unpopular, is an important factor driving this, though ex-ante deaths and9accidents may seem to be less subject to myopic voting behavior. These results shed light on the dynam-ics of political behavior over the electoral cycle in the mining industry. Furthermore, the mere existenceof political cycles in an industry with both private and public organizations suggests collusive actions be-tween and politicians and private firms. Asher and Novosad (2018) provide evidence of the involvementof criminal politicians in the Indian mining sector. They observe net worth of politicians at the beginningand at the end of their term, and find that mining booms result in larger positive wealth changes. How-ever, they do not analyze behavior over the political term. I address it to some extent in this chapter. Thischapter also provides important new findings on the dynamic nature of the Naxalite conflict, and per-haps most critically evidence of political behavior in dealing simultaneously with electoral competitionand the Naxalite threat.10Chapter 2Religious Divisions and ProductionTechnology: Experimental Evidence fromIndia2.1 IntroductionEvidence suggests that ethnic diversity can lower firm output due to poor social ties and taste-baseddiscrimination among workers (Becker, 1957; Lazear, 1998; Hjort, 2014).3 However, we know very littleabout how these effects depend on the nature of production or about the long-run effects of diversity infirms. It is important to develop knowledge of these issues to understand how firms respond to the costsof diversity. If managing a diverse workforce imposes large costs, firms may limit hiring to minimizeinter-ethnic interactions, or segregate workers perpetuating discrimination. But these market distor-tions could be avoided if the negative effects of diversity are mitigated in the long-run through repeatedintergroup contact and\/or through the adoption of appropriate production technology.This chapter contributes to our understanding of these issues by implementing a field experimentto estimate the short- and long-run effects of religious diversity on team productivity and intergrouprelations under different production technologies. To this end, I partnered with a processed food man-ufacturing plant in West Bengal, India that employs both Hindus and Muslims \u2014 the two main religiousgroups who have a long-standing history of conflict in India (Pillalamarri, 2019). Production tasks at3There is a large literature on the negative effects of ethnic diversity in decision making in the public sphere as well (Easterlyand Levine, 1997; Alesina and Spolaore, 1997; Miguel, 2004). At the same time, diversity has been shown to have positiveeconomic outcomes too \u2013 due to strategic complementarities in interacting with out-group individuals (Artiles, 2020; Montalvoand Reynal-Querol, 2017; Jha, 2013) and\/or under certain specific requirements of ethnic interaction imposed by authority(Bhalotra et al., 2018; Marx et al., 2021).11the firm can be categorized into the following two types depending on the nature of contact betweenworkers: High-Dependency (HD) and Low-Dependency (LD). This classification is based on the degreeof continuous coordination required amongst workers performing a task to ensure uninterrupted pro-duction, and the dependence on teammates for breaks. Worker effort choices have a higher degree ofcomplementarity in HD tasks than in LD tasks, where workers are required to coordinate intermittently.4There are two key features of my research design that are important for identification. The first isthat I randomly assign nearly 600 workers to religiously mixed or Hindu-only production teams. Thesecond is that the firm follows a quasi-random method of assignment of workers to production tasks.5Taken together, they allow me to attribute potentially different effects of religious mixing in HD andLD tasks to production function differences, as opposed to differences in worker types in these tasks.Each production line at the factory comprises a series of (HD and LD) tasks. I designed the experimentto estimate the effects of religious mixing on line-level output, as well as on individual task-level teamperformance. With line-level output, I identify the difference in the effect of mixing in HD versus LDtasks, whereas with task-level performance, I identify the level effect of mixing in HD and LD tasks. I keptthe randomized teams intact for a period of four months in order to estimate dynamic effects of mixing.The experiment uncovers three key findings. The first is that religious diversity negatively affectsteam output, but only in HD tasks. Production lines with mixed teams in HD tasks (HD-Mixed lines)produce 5% lower output than lines with mixed teams in LD tasks (LD-Mixed lines). An analysis of per-formance measures at the task-level reveals that this loss is entirely attributable to mixed teams in HDtasks. In LD tasks, religious diversity is costless. The second key finding is that the difference in out-put between HD-Mixed and LD-Mixed lines attenuates significantly over the treatment period \u2013 fromgreater than 20% at the beginning of the experiment, the effect reduced to less than 1% by the end of thefourth month. This is driven entirely by output gains in mixed HD teams. The third key finding is that,4An example of a HD task is work on a fast moving conveyor belt where each worker is responsible for collecting every secondor third piece of a product on the belt. Even if only one of them cannot keep up, the machine speed needs to be reduced affectingthe productivity of all workers. An example of a LD task is work in a mixing room. Workers typically have well-defined individualduties: for example, one worker is responsible for ensuring that raw materials are weighed properly, another one is entrustedwith arranging flour buckets while a third worker mixes the raw materials. The workers need to coordinate intermittently andthe productivity of one worker does not directly or immediately influence other workers. A detailed description of HD and LDtasks follows in section 2.2.5The HR manager keeps a pool of job applicants who are assigned to tasks on a first-come-first-served basis when vacanciesbecome available \u2014 workers do not get to choose their task when they join or over their tenure. A detailed description of thisprocess and tests to check its validity are presented in section 2.3.4 and Appendix A.1.2.12at endline, there is a reduction in negative out-group attitudes for Hindu workers, which is substantially(23%-56%) larger from mixing in HD teams compared to LD teams. This is despite the fact that mixedHD teams suffered negative output shocks. In LD teams, mixing has little or no effects on attitudes ofHindus.There are several plausible explanations for these core findings. Since there are no Muslim-onlyteams in this study, one might worry that these results are driven by productivity differences betweenHindus and Muslims. In particular, if Muslims have lower productivity, the treatment effects could sim-ply reflect differences in average productivity between mixed and Hindu-only teams. A number of resultsand additional tests suggest that this is unlikely. First, if Muslims were less productive overall, we wouldexpect mixing to reduce productivity in LD tasks too. Second, the fall over time in the treatment effectof mixing in HD tasks is unlikely if Muslims were simply unproductive at these tasks. Third, I test forheterogeneity in this attenuation: I find that teams in which Hindus have had greater past contact withMuslims suffer smaller losses initially relative to teams in which Hindus have had little or no contact.The effects completely dissipate for the former group, but remain negative and statistically significantfor the latter by the end of the intervention. These dynamics are also inconsistent with Muslims beingless productive. Lastly, I show that at baseline Hindus and Muslims were equally likely to be promoted.This suggests that the firm does not perceive them to be differentially productive either. The null effectof religious diversity on productivity in LD sections6 further rules out other explanations based on socialreputation concerns around in-group members (Afridi et al., 2020) or distaste for out-group members(Hjort, 2014). Even though worker efforts have a lower degree of complementarity in LD tasks, teams arestill required to coordinate on many aspects.I develop a conceptual framework and instead argue that the most plausible explanation for the find-ings here is that Hindus have lower priors regarding how hardworking their Muslim co-workers are, rela-tive to in-group Hindu co-workers. But Muslim workers do not make this distinction. This is because ofthe asymmetry between Hindus and Muslims in their exposure to non-coreligionists at baseline. Con-6During a period of religious tensions in West Bengal following the passing of the Citizenship Amendment Act (CAA) andsubsequent riots in New Delhi, I find religious diversity to have negative effects in LD tasks too. This rules out that mixing in LDtasks is simply a placebo treatment where there are no interaction among workers. Instead, the production technology is suchthat output is less sensitive to frictions amongst workers. However, extreme events can lead to workers sabotaging out-groupmembers. These results are presented in Table A.22.13sistent with majority-minority relations, Muslims are always in mixed teams with Hindus, while a largesection of Hindu workers in the firm do not work with Muslims.7 This leads to Muslims having accu-rate priors about Hindus, but Hindus (depending on past exposure) not necessarily having accuratepriors about Muslims. In HD tasks with complementary worker efforts, Hindus optimally choose loweffort based on the low initial prior about their Muslim co-workers, leading to low team output.8 Hinduworkers do update their beliefs about Muslims and forward-looking Muslim workers internalize this be-haviour of Hindu workers. Given a long enough interaction period, Muslims exert high effort despite thefact that Hindus initially exert low effort. This follows because Muslims can persuade Hindus to eventu-ally exert high effort as the latter begin to observe greater realizations of high output days than expectedunder low effort from their Muslim teammates, and as a result gradually update their beliefs. By bearingthis short-run cost, Muslim workers benefit from a high-output equilibrium in the long-run.9 Consistentwith this mechanism, I find that during the intervention period, Hindu workers are more likely to blamelow output on Muslims (than other Hindus), while Muslims show greater willingness to sacrifice theirscheduled break time for Hindus (than other Muslims).The policy implications of my findings hinge crucially on whether firms are aware of the costs of re-ligious diversity, and how they depend on the production technology. To explore this, I surveyed morethan one hundred production supervisors across five different firms that produce similar products. Iasked them to predict the results of my experiment and about ways to mitigate possible negative effectsof religious divisions. They correctly predicted that religious mixing would be more costly in HD tasksthan in LD. But despite the possibility of losses, the majority of supervisors reported to be averse to seg-regation of workers by religion.10 About a quarter of the supervisors correctly cited negative effects of7In factories and other formal workplaces across India, Muslims are generally used to working alongside Hindus, whilea large share of Hindus are not used to working with Muslims. In this firm, roughly 50% of the Hindu workers worked inhomogeneous teams at baseline, while all Muslim workers worked alongside Hindus. Similarly, 43% of Hindus reported tohave no contact with Muslims outside of work, whereas only 9% of Muslims reported the same about Hindus. Based on this,together with evidence on discrimination against Muslims in access to education and labor markets in India (Kalpagam et al.,2010; Basant, 2007), I assume Hindus on average (mistakenly) have lower priors regarding how hardworking their Muslim co-workers are, relative to in-group Hindu co-workers. Of course, I show evidence that Hindus and Muslims are not differentiallyproductive in section 2.6.8In LD tasks, worker efforts are non-complements whereby the effort levels of Hindu workers are not dependent on theirpriors about Muslims. As a result, team output is not affected by diversity.9Note that if the interaction period is not sufficiently long, then the minority group (Muslims) does not invest in the majoritygroup. This is because there will not be enough periods of high-output payoff to recover the loss that the minority group suffersinitially by exerting high effort, even as the majority group exerts low effort.10Note that having religiously mixed and Hindu-only teams at the individual task-level (as in the experiment) is natural in14diversity dissipating with repeated intergroup contact, but the first-order concern was about such seg-regation potentially causing tensions. These findings suggest that effective policy design in this contextmust look beyond just the direct effects of diversity on production and also trade-off potential short-runcosts for long-run benefits of integration.The rest of the chapter is organized in the following manner. Section 2.2 describes the context:Hindu-Muslim relations in India (in brief) and the study firm: its workers, as well as high- and low-dependency tasks. I discuss the research design and data, and present balance checks in Section 2.3.Section 2.4 presents the econometric specifications used. The results and robustness checks are pre-sented in Section 2.5. In Section 2.6, I discuss plausible mechanisms behind the core findings, and de-scribe an outline of a conceptual framework (the model is presented in Appendix 2.10) for the favoredmechanism, and provide some subsequent empirical support. Section 2.7 discusses some policy impli-cations. Finally, section 2.8 concludes.2.2 Context2.2.1 Hindu-Muslim relations in IndiaHindus form the majority of the Indian population (79.8%), while Muslims are the largest minority (14.2%)group (Census, 2011). Hindu-Muslim conflict has plagued India for centuries and has been a recurringphenomenon since partition and independence in 1947 when the country was divided on religious lines\u2013 an episode which itself was marked by large scale religious violence (Talbot and Singh, 2009). Muslimshave since suffered greater discrimination and violence against them, as well as borne larger economiclosses due to such tensions (Mitra and Ray, 2014). Across the country, Muslims continue to lag behindHindus on various economic indicators including income and education (Asher et al., 2018), face so-cial exclusion (Alam, 2010) as well as discrimination in the labor market (Kalpagam et al., 2010; Khan,2019) due to their minority status. Hindu-Muslim relations have especially deteriorated in West Bengalrecently as local state politics has seen significant polarization on religious lines (Nath and Chowdhury,2019).this context \u2013 because Hindus comprise 80% of the population and each task requires five to six workers on average (see Figure2.1). Supervisors showed concerns about complete segregation of workers by religion on the production floor i.e., having onlyall-Hindu and all-Muslim teams.15The share of Muslim population varies greatly across states and districts in India. Muslims constituteroughly 25% of the population in the district where my partner factory is located: this is close to the shareof Muslims in the factory itself, as well as in other manufacturing plants in the area. Therefore, in termsof representation of Muslims, the factory resembles the average manufacturing plant in the area.2.2.2 The Factory: Production lines and worker characteristicsIn this section, I describe the factory: the structure of production lines and sections, HD and LD tasks,as well as the operation of shifts. I also discuss the pay structure of workers and report characteristics ofthe workers by religion.Production lines, sections and shiftsThe factory produces packaged bakery products. There are six production lines in total, each ofwhich produces a different product. Figure 2.1 illustrates the structure of the production lines.Each line is sub-divided into sections (small blocks in the figure) based on the production task that isundertaken in that section. The numbers in parenthesis denote the count of workers in each of thesesections.11 Production occurs in three different shifts: morning, afternoon and night. There are threecohorts per production line, who as a team rotate shifts on a weekly basis.12 As a result, workers havefixed teams at both the line-level and line-section-level i.e., their co-workers do not typically change,only their shift of work as a team changes weekly.13Religious composition of production linesTable 2.1 reports the proportion of Muslim workers in each line-level team across the three cohortsat baseline. Line 4 only has two cohorts while all the other lines have three cohorts each. While there isvariation in the proportion of Muslims across teams, it is clear from this table that Hindus and Muslimsare not segregated in particular lines or cohorts in the factory. On average, each line and cohort roughlyhave between 15%-25% Muslim workers, which is very close to the overall share of Muslims in the factory.This is formally shown in Figure A.7. I regress a dummy variable denoting a worker\u2019s religion on line and11Some of the production lines can produce multiple products and these numbers can vary (though only very little) depend-ing on the exact product being manufactured. Figure 2.1 is based on the number of people in each section during the baselinesurvey. The numbers during the intervention were slightly different for some sections.12Teams move from morning to night to afternoon shifts.13Occasionally workers are moved across shifts and lines. This is determined by worker absenteeism and turnover.16cohort fixed effects and show that balance in religious composition of production lines and\/or cohortscannot be rejected.The fact that Muslims are in a minority, together with the structure of production lines that requiresmall section-level worker teams within lines, means that a large section of Hindu workers have littleor no contact with their Muslim counterparts. This can be observed in Figure 2.1, where the religiouscomposition of production sections of all six lines is shown for one particular cohort. A large numberof sections (close to 50%) have no Muslim workers at all. The share of Muslim workers in most of theother sections is between 0.1 and 0.3. The composition is similar across the other two cohorts as well.This is important for two reasons. First, the degree of inter-religious contact induced by the treatment(60% Hindus and 40% Muslims in mixed teams) represents a significant change from the baseline levelof contact for Hindus. Second, the majority-minority asymmetry in exposure to non-coreligionists atbaseline might mean that Hindus and Muslims behave differently when randomized into mixed teams.Pay structure of workersWorkers at the factory are paid a flat monthly wage based on their experience and level of expertise(skill) on the job. Wages are not dependent on daily team productivity but performance is evaluatedfrequently; poor performance over a period of time can lead to workers being moved to a lower skillgroup. Alternatively, performing well can lead to promotion. Workers are categorized into unskilled,semi-skilled and operator groups. Approximately 80% of the workers are unskilled and the rest are semi-skilled or operators. Semi-skilled workers undertake the same tasks as unskilled workers, while operatorsare in charge of handling machines.Characteristics of Hindu and Muslim workersSummary statistics of worker characteristics are reported in Table A.9. It is apparent that workers arenot sorted into HD and LD jobs based on their religious identity. There are however important differ-ences between Hindus and Muslims. Muslim workers have lower schooling, as well as lower tenure atthe factory. It has been documented in other studies as well that Muslims on average tend to have lowereducation relative to Hindus in India (Bhaumik and Chakrabarty, 2009). The difference in average tenurehowever might be surprising. This can be explained by the fact that in the district where the factory islocated, Muslims have traditionally been tailors, which many families still continue to pursue as their17business. Since families in this region are typically well-connected, this network allows Muslims to workin the informal tailoring sector, providing them with an outside option of employment. The managementoften cited this as a factor behind the larger turnover of Muslim workers.Muslim workers report having much greater contact with Hindus outside of work (as well as at work),which is expected given that Hindus form the majority group in the study area and across India in gen-eral. Consistent with this, Muslims report to be more comfortable than Hindus when it comes to com-municating with non-coreligionists. Surprisingly, both groups report to be equally uncomfortable takingorders at work from non-coreligionists. Finally, as shown in Table A.9, Hindus are much more likely tosupport the controversial National Registrar of Citizens (NRC), a bill which is often criticized for discrim-inating against Muslims.142.2.3 Direct Dependency as a measure of production technologyDirect Dependency is defined as the degree of continuous coordination required amongst workers per-forming a task to ensure uninterrupted production. I study it as the key aspect of production technol-ogy for two main reasons. First, a key distinction between high- and low-dependency tasks relates toa core idea in economics: the degree of complementary of labor inputs. Worker efforts have a highdegree of complementary in HD tasks, while they have a lower degree of complementarity or are non-complements in LD tasks. Second, the degree of complementarity in labor inputs affect incentives tointeract, suggesting that this might matter for the effects of religious divisions. Some key characteris-tics of high- and low-dependency sections (or tasks) are listed in Table 2.2. Figure A.8 provides a visualillustration of HD and LD tasks.Task coordinationThe first key distinction between high- and low-dependency tasks is in the amount of continuouscoordination required amongst co-workers. A high degree of continuous coordination is required in HDsections, whereas it is only intermittent in LD ones. I quantify this with time-use data. Research assis-tants recorded minutes (out of 10) of continuous coordination required amongst workers for productionto continue without interruption in each section. HD sections typically require workers to coordinate14The NRC is a list of people who can prove that they came to India before 24th March, 1971. It is a widely held view thattogether with the Citizenship Amendment Act (CAA), the NRC could be discriminating against Muslims (Chapparban, 2020).18continuously for 9-10 minutes (out of 10), whereas the average in LD sections is only 2 minutes. Sectionsabove the median value (\u2265 9) on this scale are classified as HD sections and the rest as LD sections.The distribution of Direct Dependency is shown in Figure 2.2. Most tasks require either high contin-uous coordination (9 or 10 minutes out of 10) or less than 2 minutes of continuous coordination \u2013 thisleads to the bi-modal distribution in the figure. This allows easy classification of tasks into HD and LDtypes, an important (third) reason to pick this measure over others.Control over breaks\/relief timeThe second key distinction between HD and LD tasks is about control over breaks during the pro-duction process. Due to dependence on co-workers every minute of the production process in HD tasks,each worker individually has little control over when they can take a break. Sub-groups of workers needto provide \u201crelief\" to other workers in the same HD section, a concept known as \u201crelief time\". There areoften disagreements amongst workers regarding how to schedule these as well as arguments when someworkers take more time than allocated. Supervisors reported such disruptions to be a common causefor lower productivity. By contrast, in LD sections each worker has much greater control over schedulingbreaks.Physical mobilityPhysical mobility is restricted in HD sections. For example, workers are typically required to standclose to each other on conveyor belts and pick products up as they move on the belt. Coordination withothers doing the same is therefore key. In LD sections, greater individual control over the productionprocess allows workers greater physical mobility.Repetitive monotonyRepetitive monotony is higher in HD sections compared to LD sections since work cycles are shorter.The machine speed set by the supervisor often determines the speed of work, allowing workers littlecontrol over the process. If workers do not perform up to the mark, supervisors may need to reducemachine speed causing loss in output. Informal interviews with the supervisors made it clear that itis not uncommon for them to vary machine speed in these areas. This could happen due to workerabsenteeism leading to changes in teams, as well as due to workers simply not coordinating as expectedon certain days of production. In LD sections, workers typically have more control over process speed,19and can re-allocate their time across different sub-tasks to a greater extent.15Direct Dependency and other task-level characteristicsIn Figure A.6, I show all six production lines at the factory broken down into HD and LD sections. InTable A.10, summary statistics of various aspects of the physical environment of HD and LD sections arepresented. I focus on factors which could act as potential confounders to the main mechanism in thispaper. I measured the degree of non-work interaction (time workers spend chatting) and noise levels ineach section of each production line and rule out that HD and LD sections are systematically differenton these aspects of the physical work environment. The only statistically significant difference betweenHD and LD sections is in the average temperature; HD sections tend to be warmer by two degree Celsius.This difference is primarily due to a few colder LD sections in one particular production line. One couldworry that hotter temperatures might intensify the negative effects of religious divisions, driving partof the effects that I find. This is not the case \u2013 all my results are robust to dropping this productionline\/sections from the analysis.162.3 Research designThis section discusses the research design. I first go through the randomization process and then presentbalance checks over a range of worker characteristics across the different treatment arms. Before theintervention, workers were informed that their teams would be changed in order to assess the effect ofteam-switching on productivity. The new team lists (post randomization) were printed and posted onthe production floor. No additional information was provided. Religion of teammates can be directlyinferred from their names in this context.1715From the description of HD and LD tasks it might seem LD tasks are unequivocally better, but that is not the case. Thereare various aspects of LD tasks, such as heavy lifting in certain sections or working in mixing rooms that have unpleasant smellwhich workers reported to dislike.16These results are available upon request.17Whether a person is a Hindu or a Muslim can be determined from their first name itself in the Indian context. In very fewcases where the first name maybe ambiguous, the last name would certainly reveal one\u2019s religion. My sample consists of onlyHindus and Muslims.202.3.1 Treatment and randomizationAs mentioned earlier, the factory operates in three shifts (morning, afternoon, night) and an entire cohortof workers move from one shift to the next on a weekly basis. A new set of workers come to work in eachshift on a particular day. Therefore, each line has three different cohorts working on it each day of theweek. For the purpose of randomization, I moved workers across cohorts, holding their production lineand section of work fixed.18Individual workers were randomized into line-section-level teams in order to achieve two distincttypes of teams (treatments) at the line-level. The first type comprised of line-level teams with religiouslymixed groups only in HD sections (HD-Mixed lines), while the second type had religiously mixed groupsonly in LD sections (LD-Mixed lines). Two of the randomized cohorts within each line were of one teamtype while the third cohort was of the other type. Figure 2.3 below provides a visual illustration of the twotypes. I use Line 2 from Figure 2.1 for this illustration.Individual section names are replaced by HD and LD labels to denote section (task) type. The first type ofline-level team has all its HD sections mixed (partly shaded in grey) while its LD sections are comprisedof only Hindu workers (HD-Mixed line). The structure in the second type is exactly the opposite \u2013 LDsections have religiously mixed teams while HD sections have only Hindu workers (non-shaded) (LD-Mixed line).19 This leads to four different types of line-section-level teams: 1. HD Mixed 2. HD Non-Mixed 3. LD Mixed and 4. LD Non-Mixed. Whether a production line would have two cohorts of HD-Mixed lines (and one LD-Mixed) or the other way round was determined by the overall number of Hindusand Muslims in the line at baseline. Production data are available for both line-level as well as line-section-level teams. Therefore, any differences in overall line-level performance between teams can bedisaggregated to line-section-level performance.Randomization was constrained by one key limitation \u2013 the number of workers switching their sec-tion of work (their task) had to be minimized. Even though the induction of workers to specific tasks(unless as an operator) takes only between one to two days, it is impossible to train all workers in new18For a small share (7.9%) of workers this was not the case. Some workers had to be (randomly) moved from their tasksat baseline to achieve the desired line-level team types. However, such task-shifting is not correlated with treatment status.Section 2.5.3 includes a discussion on this.19At the line-section-level, religiously mixed and Hindu-only teams are the ones that are naturally formed at baseline (recallFigure 2.1).21tasks simultaneously \u2013 this would lead to substantial interruptions and breakdown in production. Themanagement was not willing to do this. As a result, the randomization process was designed such thatdid it not require the majority of workers to change their section of work and hence the dependency oftheir task at baseline. I address concerns with respect to selection of workers into HD and LD jobs sub-sequently.The first step in the randomization process involved determining the final (target) number of Hindusand Muslims in each section of each production line (across all cohorts). Since workers were not movedacross production lines, this was typically constrained by the overall number of Hindus and Muslims ina line across the three cohorts at baseline. The share of Muslims in each production line at baseline wasclose to the overall share of Muslims in the plant (approximately 18%). After randomization, the share ofMuslim workers in mixed sections (both HD and LD) of all six lines was typically between 35%-40% (thiswas of course balanced between HD and LD sections).20The second step in the process involved sorting workers by section \u00d7 religion \u00d7 skill21 (across all3 cohorts in a line) and shifting workers across sections (tasks) in order to ensure that each section ofeach line had enough Muslim workers (summing across cohorts) required for randomization (as deter-mined in the first step). This had to be done at baseline because not all sections of all lines had enoughMuslim workers (sometimes none) such that the desired line-level team structures in Figure 2.3 couldbe achieved. For example, the Injector section in Line 3 had no Muslim workers at all across the threecohorts. In such cases some randomly chosen Hindu workers in that section were shifted out and re-placed with randomly chosen Muslim workers from another similar section with enough Muslims. Thisprocess meant that at the end of step 2, all sections of all lines had both Hindu and Muslim workers22who would then be randomly allocated to line-section-level teams. This also satisfied the management\u2019srequirement of minimum section (task)-shifting.20Note that the religious composition of a particular section in a line would be exactly the same across all cohorts if theybelonged to the same line-level team type. In other words, if cohorts A and B in Line 1 were such that all their HD sectionswere mixed and LD sections were non-mixed, then each of their HD sections would have exactly the same ratio of Hindu toMuslim workers i.e. Packing in cohort A would have exactly the same number of Hindus and Muslims as Packing in cohort B.Non-mixed teams of course only have Hindu workers.21Workers are classified into three skill levels: unskilled, semi-skilled and operator. Each section typically has an operator ora semi-skilled worker (depending on the type of work), and the rest are all unskilled workers. The randomization process didnot alter this structure.22This is required because for each section of each line there would at least be one line-level team where that section wouldhave to have a mixed group.22Lastly in the third and final step, workers were sorted by their new section (post step 2) \u00d7 religion \u00d7skill and randomly allocated into line-section-level teams in order to achieve the line-level team struc-tures shown in Figure 2.3. Line-level teams were then randomly allocated to one of the three shifts. Adetailed description of each step involved in the randomization process is presented in Appendix A.1.Figure A.1 provides a visual illustration of the same, especially focusing on how section-shifting allowsformation of the desired line-level team structures.2.3.2 Data collection, experiment timeline and attritionData used for the analysis in this paper come from two main sources. I use administrative records ofproduction obtained directly from the firm\u2019s management to estimate treatment effects of diversity online-level output. The firm records total output at the line-level line in each shift; this measure is tieddirectly to the revenues of the firm. Before the intervention, supervisors were also trained by the produc-tion manager to rate the performance of each line-section-level team independent of the performanceof the entire line or other sections in the line. These ratings are used to directly estimate the effect ofdiversity on output in HD tasks separately from LD tasks.23Workers participated in an in-person survey at baseline but only a phone survey could be conductedat endline due to COVID-19 related restrictions in India. The baseline survey included a wide set ofquestions ranging from employment related ones such as tenure, history of past teams, attitudes towardstaking orders from and interacting with non-coreligionists, to objective worker characteristics such asage and schooling. I also asked workers about their political preferences, focusing on factors that couldcapture taste discrimination towards religious groups. These include preference for political parties thatare associated with favoring a particular religious group and support for bills that are widely criticizedfor discriminating against Muslims.The focus of the endline survey was primarily on interactions (accusations, blame, providing relieftime etc.) that happened during the intervention and on worker attitudes that could capture the effectsof inter-religious contact in HD and LD environments on inter-group relations. Summary statistics of key23It is nevertheless possible that these ratings do not appropriately take into account spillover effects from upstream to down-stream sections. In section A.3.3 (Appendix), I restrict attention to sub-samples for which spillovers are likely to be less of aconcern and show that my main results are replicated.23variables are presented in Table A.9; differences in characteristics of Hindus and Muslims have alreadybeen discussed in section 2.2.2. Figure 2.4 presents the timeline of the intervention and sample size bytreatment arm. There are 15 line-level teams24 (7 HD-Mixed Lines and 8 LD-Mixed Lines) and 113 line-section-level teams (23 HD-Mixed, 33 LD-Mixed, 29 HD Non-Mixed and 28 LD-Mixed). A total of 586workers were part of the intervention distributed in the following way in line-section-level teams: 175in HD-Mixed, 117 in LD-Mixed, 196 in HD Non-Mixed and 98 in LD Non-Mixed. A total of 546 workerscould be reached at endline for the phone survey (attrition rate 6.8%).252.3.3 Randomization checkBalance checks in Table 2.3 show that randomization was successful. Outcomes are divided into twobroad categories - (1) those that are relevant at work (Panel A) and (2) general characteristics and at-tributes (Panel B). The unit of analysis here is an individual. The main regressors are the interactionterms Mixed\u00d7 LD and Mixed\u00d7HD which denote the type of line-section-level team and hence the treat-ment status of an individual. Line \u00d7 Section fixed effects are included in these specifications, wherebythe main effect of HD versus LD is not separately identified. The omitted group is therefore all workersassigned to non-mixed teams.26 Across a range of characteristics that include factors that are relevantat the workplace (such as tenure and past contact with non-coreligionists), as well as general attributes(such generalized trust, altruism and contact outside work), workers are similar across the treatmentarms.Finally, it is also important to show that the proportion of Muslim workers is balanced across mixedHD and LD teams, to rule out that the treatment effects are driven by different \u201cdegrees\" of religiousmixing across the two types of tasks. This is shown in Table A.4.24Note that at full capacity the firm would have 17 line-level teams as shown in Table 2.1. However, in the experiment thereare 15 line-level teams only. This is because during the period of the intervention, the firm decided to operate at lower capacitydue to low product demand compared to previous years (even though the experiment was timed to coincide with the periodwhen, in terms of seasonality, the firm usually experiences the highest demand). As a result, production lines 1-3 had threecohorts each whereas lines 4-6 only had two cohorts each (Figure 2.1). This change occurred before the randomization began,so the experiment was not affected by it.25In Table A.25, I show that attrition is balanced across treatment arms.26I use this particular specification for balance checks because the same specification is used to estimate treatment effectsat the line-section-level on team production, as well as on individual-level survey outcomes. As a robustness check, I use Linefixed effects instead of Line\u00d7 Section fixed effects in Table A.5 (whereby the main effect of HD versus LD is identified) and showthat worker characteristics are balanced across HD and LD sections. I also show balance in individual characteristics acrossline-level teams (i.e. HD-Mixed lines versus LD-Mixed lines overall) in Table A.6.242.3.4 Quasi-random allocation of workers to tasks at baselineSince the majority of workers continued to work in their original tasks (i.e. the area of work was not ran-domized), one might worry about distinguishing between the effects of task types versus worker types(on team productivity) in religiously mixed teams. This is particularly important if workers are able toself-select into high- or low-dependency sections. The randomization check already rules out such sys-tematic sorting. Nevertheless, I address this concern in more detail in Appendix A.1.2. I argue that workercharacteristics are balanced across HD and LD tasks due to the firm\u2019s hiring and worker allocation policyand not simply by chance. The HR manager always has a pool of job applicants who are called upon ona first-come-first-served basis, when vacancies become available. As a result, workers do not have theoption to choose their area of work when they join. However, workers may quit at different rates acrossthe two types of tasks, leading to possible selection bias. If that were the case, this would be reflectedin the average tenure of workers in HD and LD sections. As shown in Table A.5, this is not the case \u2013tenure is balanced between workers in HD and LD sections. I then show that only a handful of workers(15.9%) have switched their area of work from when they first joined the firm. Finally, I show that theseswitches are not correlated with observable characteristics of the workers and have happened purely dueto organizational requirements at the firm.2.4 Econometric specificationOutcomes in this paper are measured at three levels: 1. Production line-level, 2. Production line-section-level, and 3. Individual-level. Line-level real output data are linked to the firm\u2019s revenues. Line-section-level ratings were recorded by production supervisors daily during the period of the experiment only.These data help investigate the source of line-level differences in real output. Survey measures at base-line and endline are at the individual worker level. I use these to study worker interactions during pro-duction as well as treatment effects on attitudes.Line-Level specificationI compare line-level output between HD-Mixed and LD-Mixed lines as shown in Figure 2.3. The25specification used is:Ykl st =\u03b21Tk +\u03b1l +\u03b1s +\u03b1t +\u03f5kl st , (2.1)where Ykl st is output from line-level team k, in line l , in shift s on day t . Tk denotes the treatment status(1 if HD-Mixed line and 0 if LD-Mixed line). The coefficient \u03b21 denotes the line-level treatment effect.\u03b1l , \u03b1s and \u03b1t are line, shift and day fixed effects respectively. I include production line fixed effects tocontrol for product type, shift fixed effects to account for differences in worker productivity at differenttimes of the day (morning, afternoon, night) and day fixed effects to control for factory-wide shocks todemand. Standard errors are clustered at the line-cohort-level (or in other words at the line-level team).Since there are only 15 clusters at the line-level, I also present wild cluster bootstrap standard errors(Cameron et al., 2008) for these regressions.Line-Section-Level specificationSupervisors assigned a daily rating (out of 5) to each line-section-level team, independent of theperformance of other sections in the line. I use this data to evaluate the source of line-level differencesin output. The following baseline specification is used:Ymkl st =\u03b21Mi xedmkl \u00d7LDml +\u03b22Mi xedmkl \u00d7HDml +Xmkl +\u03b1ml +\u03b1s +\u03b1t +\u03f5mkl st , (2.2)where Ymkl st is the performance rating of section m of team k in line l in shift s on day t . Mi xedmkldenotes whether the section has a religiously mixed or homogeneous team (which is determined byline-level team type k). LDml and HDml are dummies coded 1 if the section is classified as HD and LDrespectively (this is defined by line l and section m only). I use the interaction terms Mi xedmkl \u00d7HDmland Mi xedmkl \u00d7 LDml to identify effects of having mixed teams in HD and LD sections respectively(given by the coefficients\u03b21 and\u03b22). Since line\u00d7 section effects\u03b1ml are included in these regressions, thedummies HDml and LDml are not separately introduced. Xmkl is a vector of line-section-level controls.\u03b1s and \u03b1t are shift and day fixed effects respectively.Individual-level specificationI surveyed workers both at baseline and endline. I use the baseline data for randomization checks asshown in section 2.3 and also for heterogeneous treatment effects which follow in section 2.5. As men-26tioned earlier, the endline data is used to evaluate treatment effects on worker attitudes and interactionsbetween teammates during production. The main specification is:Yi mkl =\u03b21Mi xedmkl \u00d7LDml +\u03b22Mi xedmkl \u00d7HDml +Xi mkl +\u03b1ml +\u03f5i mkl , (2.3)where Yi mkl is the outcome of interest for individual worker i of section m of team k in line l . Xi mkl isa vector of individual-level controls. All other variables are described exactly as before. The treatmenteffects are estimated by coefficients just as in the line-section level specification described above.2.5 Results2.5.1 Production dataThis section begins by showing that HD-Mixed lines produce lower output than LD-Mixed lines, but thiseffect attenuates over time. I then proceed to the line-section-level analysis and show that line-leveldifferences in output are driven entirely by losses from religious mixing in HD sections, while mixing hasno effect in LD sections.Line-LevelProduction supervisors record total output from each production line at the end of each shift. Table2.4 shows that HD-Mixed lines produced lower output compared to LD-Mixed lines. Observations inthis regression are at the line-cohort-day-level. The outcome variable in Column (1) is the log of totaloutput (in pieces) produced by a line-level team in a particular shift of a day. Column (1) shows that HD-Mixed lines on average produced 5% lower output compared to LD-Mixed lines over the period of theintervention. This effect is economically large. Given average output per shift of 450,000 pieces (acrossall lines) and the average product priced at Rs 10 ($ 0.13), the results suggest that the firm\u2019s revenue wouldincrease by up to Rs.225,000 ($3100) per shift, from having only LD-Mixed lines relative to having onlyHD-Mixed lines.The firm also records total output using the number of boxes with final products that are packed atthe end of a shift. These boxes are used to ship products to the market and each box typically includes27multiple pieces of a product. The effects are robust to using this variable as the outcome instead (Column2). Since each production line can manufacture more than one variant of the same product, I showrobustness to the inclusion of line\u00d7 variety fixed effects in Table A.11. Finally in Table A.12, I include line\u00d7 day fixed effects \u2013 the results remain robust.27Over the entire period of the intervention HD-Mixed lines produced 5% lower output than LD-Mixedlines, but how did the treatment effect evolve over time? This would inform us whether repeated interac-tion with the same set of non-coreligionist co-workers can help ameliorate some of the negative effects ofmixing on output. In Figure 2.5, I present a event study plot of output (logged) produced over the periodof the intervention, by team type. These are from binned regressions using the same specification as insection 2.4, with the treatment period split into five equal sized bins. The difference in output producedby HD-Mixed and LD-Mixed lines was the largest at the beginning of the intervention and it graduallyattenuated over time.28 Interestingly, output from both HD-Mixed as well as LD-Mixed lines followed anupward trajectory throughout the four months of the intervention. This might be because of two rea-sons: 1. The firm was itself adjusting to new teams and therefore only gradually increased productiontargets as workers became more comfortable with each other and 2. The experiment was timed to co-incide with the period during which the factory faces high demand for its products; so that productionremains uninterrupted, absenteeism is low and teams don\u2019t disintegrate. This could have also led to thefirm setting higher output targets in each subsequent month of the intervention.Overall, these results imply that religious diversity is relatively more costly in HD tasks than in LDtasks. But the overall line-level differences (between HD-Mixed and LD-Mixed lines) could be drivenby religious mixing lowering output in both types of tasks but more in HD, or mixing increasing outputin both types of tasks but more in LD. Another possibility is that it affects output negatively (or has noeffect) in HD tasks, but positively in LD tasks. Finally, it is also possible that mixing only (negatively)27Based on raw material usage, supervisors at the firm record standard output against actual output produced. Negativedeviations from standard output imply greater raw material wastage. In Appendix A.2, I show that wastage or \u201cOutput Gap\" islarger in HD-Mixed lines despite raw materials being allocated equally among HD-Mixed- and LD-Mixed lines. Furthermore,the variance of Output Gap is also greater in HD-Mixed lines, suggesting that diversity in HD tasks lead to relatively greateruncertainty in terms of achieving daily output targets. Speculatively, this might mean that team output is more susceptible toidiosyncratic shocks such as religious events or conflict from religious mixing in HD work environments.28The difference in standard output between the teams is much smaller (and statistically indistinguishable from 0) as ob-served in Figure A.9. This would be expected if the firm did not react to these differences across teams by redistributing plannedproduction away from low productive lines to high productive ones.28affects output in HD tasks but not in LD tasks. I cannot distinguish between these possibilities usingline-level data as there are no homogeneous line-level teams by design. I take this up next in the line-section-level analysis, where such comparisons are possible due to the presence of teams composed ofonly Hindu workers. In other words, the level effect of diversity in HD and LD tasks can individually beidentified at the line-section-level, whereas at the line-level only the difference from religious mixing inHD versus LD tasks could be identified.Line-Section-LevelI now present treatment effects on line-section-level performance ratings. Recall that there are four dif-ferent types of teams at this level: HD Mixed, HD Non-Mixed, LD Mixed and LD Non-Mixed. The per-formance of each section was rated (between 0 to 5) daily by production supervisors. These ratings werebased on a benchmark measure of time-use efficiency. The benchmarks were different across tasks. Forexample, Mixing sections were rated on the number of batches mixed per hour, while most other sec-tions downstream until Packing were rated on the number of trays with unfinished products that weresent onto the following section every hour, accounting for the number of trays received from the previ-ous section. This ensured that no section was penalized for the actions of sections upstream. Packingsections were rated on the number of boxes packed with final goods as well as on packaging materialwastage.Table 2.5 presents the core results from the line-section-level analysis. In column (1), I regress rawratings on a dummy variable that denotes whether a line-section-level team is religiously mixed or not(Mixed). The coefficient on Mixed is negative and marginally significant suggesting that mixed teamsperform worse overall. Note that line \u00d7 section effects are included in all specifications in the line-section-level analysis, whereby the identifying variation comes from within the same line-section acrossdifferent treatment cohorts (teams). These are important to include because of the different benchmarksused to rate each section.All regressions also include average tenure and schooling of workers in the section as controls, toaccount for differences between Hindus and Muslims on these dimensions.29 In column (2), I introduce29The results are robust to the exclusion of these controls as reported in Table A.14 in the Appendix.29the interaction terms (Mixed \u00d7 HD) and (Mixed \u00d7 LD) to estimate the effect of having a mixed team ina HD section separately from a LD section. The coefficient on Mixed \u00d7 LD in column (2) is small andnot statistically significant while that on Mixed \u00d7 HD is negative and statistically significant at the 5%level. This suggests that having mixed teams lead to lower ratings in HD sections but not in LD ones.In columns (3) and (4), the outcome variable is coded 1 if the the rating received is above median and 0if lower.30 The effects with a binary dependent variable are similar to those with raw ratings and moreprecisely estimated. In summary, this is direct evidence that lower output in HD-Mixed lines (relativeto LD-Mixed) is caused entirely by lower output in religiously mixed HD sections, while in LD sections,mixing is costless. In Table A.13, I run separate regressions for HD and LD sections and find similareffects.I next examine whether there is convergence in line-section-level performance over time betweenmixed and non-mixed HD teams. This is likely given that line-level output differences between HD-Mixed and LD-Mixed lines attenuated over time (recall Figure 2.5). I split the intervention period intofive equal sized bins (exactly as in the line-level analysis), and show that this is indeed the case. Theresults are presented in Table A.15.The baseline effect is reported in column (1), which shows a large, negative and statistically signif-icant effect of having a mixed HD team. In column (2), I introduce interaction effects with the eventbins. Coefficients on earlier bins are larger (negative) and they gradually reduce in magnitude. This sug-gests that the largest negative effects of religious mixing on HD section output occurred at the beginningof the experiment when the new teams were first formed; and performance ratings of mixed and non-mixed teams gradually converged over time. The baseline effect and interactions with the event bins arepresented for LD sections in columns (3) and (4) respectively. The baseline effect is small and not statis-tically significant, while the interactions are noisy with no clear dynamic pattern. Overall, these resultsare re-assuring in that they line up closely with the line-level event-study analysis, but using granularproduction data at the line-section-level.30A large fraction of ratings is concentrated between 4 and 5 (see Figure A.10), making a binary dependent variable alsoappropriate for this specification. I aggregate up line-section-level ratings to the line-level (averaging across all sections) andrun specification 2.1. The results are presented in Table A.23, which show, similar to Table 2.4, that HD-Mixed lines performworse than LD-Mixed lines, although the effects are less precisely estimated due to the smaller variation in section ratingscompared to actual line-level output.302.5.2 Endline phone surveyThe endline survey focused on two main sets of outcomes: 1. Those that capture actual interactionsbetween workers during production and 2. Attitudes towards non-coreligionists co-workers. Only aphone survey could be conducted at endline because of restrictions related to COVID-19. As a result,a large set of outcomes that I was interested in, including political preferences that respondents maybeuncomfortable discussing over the phone, could not be recorded.31 I take up each of the two sets ofsurvey outcomes in turn.Worker interactionsIn Table 2.6, I focus on the first set of factors. These collectively proxy for the degree of cohesion andcoordination in a line-section-level team. There are three main outcomes variables. The first questionasked respondents to identify co-workers who they thought did not contribute sufficient effort at anypoint during the intervention (\u201cIdentified teammate as contributing low effort\"). If a worker identifies histeammate to have not contributed as much effort as other workers did, or to the extent that is expected,then this outcome is coded 1 for a worker-teammate pair. I then asked workers to identify teammateswho have blamed them in the past for not performing up to the mark (\u201cBlamed by teammate\"). Theoutcome variable is coded 1 for teammates who have blamed the respondent at least once during theintervention period. The final question asked workers to pick teammates who they would give up theirrelief time for, if asked or already have in the past. Relief time refers to breaks that each worker is entitledto at regular intervals during their shift. In HD sections, workers typically need to coordinate on breaksto a greater degree than in LD sections. The outcome variable is coded 1 for teammates that workers arenot willing to give up their relief time for (\u201cUnwilling to give up relief time\"). Note that these questionswere asked retrospectively in lieu of more high frequency data, since many workers reported to have had31In addition, one might be worried about social desirability bias in the responses, since the outcomes I study are self-reported (even though both the baseline and endline surveys were conducted one-to-one with the respondents and anonymityand confidentiality were emphasized). To deal with this, I correlate baseline responses to survey questions (that were askedagain at endline and used as outcomes in Table 2.7) with scores from an Implicit Association Test (IAT) that the workers took.The test involved associating Hindu and Muslim names with positions in the firm hierarchy (worker, operator, supervisor, pro-duction manager etc). A positive score on this test denotes a bias towards having Hindus in higher positions, while a negativescore shows preference towards Muslims. I correlate these scores with workers\u2019 reported attitudes towards taking orders fromnon-coreligionsts as well communicating with non-coreligionists (Figure A.12). Hindu workers with a larger positive score areless likely to say they are comfortable taking orders from and communicating with Muslims. Similarly, Muslim workers witha larger negative score are less likely to say they are comfortable taking orders from and communicating with Hindus. Thissuggests that workers\u2019 responses are correlated strongly with their actual preferences and helps provide confidence in the self-reported survey outcomes.31problems with their teammates in the past but also mentioned that they subsided over time.32Observations in Table 2.6 are at the worker-teammate level for line-section-level teams. In otherwords, there are (N \u2212 1) observations for each worker, where N denotes the total number of workersin the line-section-level team. I include line \u00d7 section fixed effects and therefore compare similar sizeteams doing the same task. Columns (1), (3) and (5) show that mixed teams perform worse on all of thesemeasures. Workers in mixed teams are 4.2 percentage points (30%) more likely to identify a teammate ascontributing low effort, 4 percentage points (50%) more likely to have been blamed by a teammate and6.4 percentage points (25.6%) less likely to give up their relief time for a teammate. In columns (2), (4)and (6), I introduce the interaction terms Mixed \u00d7 HD and Mixed \u00d7 LD to test for differential effects bytask type. Clearly, having mixed teams in HD sections lead to greater frictions.However, I find that workers in mixed LD sections report to have been blamed more by co-workersthan those in mixed HD sections. Individual mistakes are more easily identifiable in LD tasks comparedto HD tasks, which is perhaps why this pattern is observed.33 Note that both of these effects are statisti-cally significant on their own.More generally, it can be observed that mixed teams in LD sections also suffer from these frictions to agreater extent than homogeneous teams \u2013 the effects on the interactions Mixed \u00d7 LD are positive andmeaningful in magnitude though not precisely estimated. In fact, one cannot statistically reject that theeffects in LD sections are different from those in HD, though the effects in HD sections are much larger.Importantly however, these do not translate into mixed teams performing any worse than non-mixedteams in LD sections, which is the case in HD sections, as shown in Table 2.5. The sample is restricted toonly Hindu respondents in Table A.16 and similar patterns are observed.These results are consistent with the treatment effects on output and inform us of actual interactionsbetween workers that led to those effects. Coordinating closely as a team on a wide set of issues is im-portant in HD tasks and lower team cohesion caused by these frictions can reduce team output. Whilemixing in LD tasks also leads to some frictions, the production technology is such that team output is lesslikely to be sensitive to these problems, which explains the null effects in LD tasks.34 But despite these32For example, workers were asked if they have been blamed by a teammate at least once in the past, or asked to identifyworkers who they thought were not contributing effort at any point during the intervention.33It is also plausible that by endline these frictions had subsided more in HD sections than in LD ones.34Of course, extreme events such as religious violence after the passing of the Citizenship Amendment Act (CAA) did affect32frictions, output differences between HD-Mixed and HD Non-Mixed sections attenuated over time. Thenext set of results study treatment effects on attitudes of workers towards non-coreligionists at endline,and formally tests whether the attenuating output effects are accompanied by improved inter-group re-lations.Attitudes at endlineFor attitudes, treatment effects are restricted to Hindu workers only, as Muslim workers are alwaysin mixed teams. I use three main outcome variables, two of which are questions also asked at base-line. Workers were asked if they are equally comfortable taking orders from non-coreligionists (\u201cTakingOrders\"), whether they find communicating with non-coreligionists (in general) as comfortable as co-religionists (\u201cCommunicating\") and finally if they prefer to be in mixed or all-Hindu groups if teamswere to change again in the future (\u201cCo-working\"). While the first two questions were unincentivized,for the third question, surveyors mentioned to the workers that their responses would be recorded andkept in mind for future team changes.I first report the main effect of being randomized into a mixed team. Outcomes in Table 2.7 are atthe individual worker level. All outcomes show positive effects from mixing. Relative to those in homo-geneous teams, Hindu workers in mixed teams are 16.8% more likely to report that they are comfortabletaking orders from Muslims (Column 1) and 20% more likely to be comfortable communicating withMuslims (Column 2). Finally, Column 3 shows that they are 18.7% more likely to not express preferencefor being in a Hindu-only team. These effects are economically significant in magnitude and suggestlarge gains for Hindu workers from repeated contact with Muslim colleagues. In Columns (2), (4) and(6), I introduce the interaction terms Mixed \u00d7 HD and Mixed \u00d7 LD. The effects are entirely driven bycontact in HD sections.The coefficients on Mixed \u00d7 HD are economically large in magnitude and statistically significant atthe 1% level. The coefficients on Mixed \u00d7 LD are small and not statistically significant, suggesting a nulleffect in LD sections. The differences between the effects in HD and LD sections are large and statisticallysignificant. These findings on positive attitude changes of Hindu workers towards Muslims (from mixingoutput in mixed LD sections (see Table A.22). But overall, the lower sensitivity of team output to these frictions is perhaps alsowhy there is little incentive for workers to try to overcome their differences. This is reflected in the next set of results where Ishow reductions in negative out-group attitudes from mixing for Hindu workers, but only in HD tasks.33in HD tasks) are consistent with attenuating output differences between mixed HD and non-mixed HDteams (Table A.15), as well as with the overall convergence in line-level output between HD-Mixed andLD-Mixed lines (Figure 2.5).Summarizing the main resultsOverall, it is insightful and non-obvious that the largest positive effects of treatment on attitudes oc-curred in teams that also suffered the largest negative output shocks. This suggests that working in closequarters even with some frictions (in HD teams) leads to more positive effects on intergroup relationsthan working in LD teams. These results emphasize the importance of contact that forces people tolearn to work together in overcoming existing differences leading to reduced prejudice. Purely from aprofit maximizing point of view however, firms may have little incentive to mix workers in HD tasks ifit leads to output loss. This unfortunately suggests that discrimination may persist in equilibrium andemphasizes the need for targeted management practices to mitigate them.2.5.3 Robustness: Threats to identificationIn this section, I discuss potential threats to the identification strategy and describe how they are dealtwith. I discuss factors linked to the research design (such as the absence of Muslim-only teams) as wellas those that randomization cannot directly account for (such as differences between mixed and homo-geneous teams on demographic dimensions other than religion).Religion and productivityFirst, I address concerns regarding potential bias that could stem from religion simply proxying for dif-ferences in other dimensions (education, tenure, etc.) between mixed and non-mixed teams inducedby randomization. One might be worried that it is not the interaction between religious mixing and theproduction technology itself that leads to productivity loss, but that this interaction simply proxies forthese other differences between Hindus and Muslims (or HD and LD tasks).35 For example, it might bethe case that differences in schooling between Hindus and Muslims are not important in LD sections,35A more fundamental worry may be that due to lower schooling and tenure, Muslims uniformly have lower productivity.If that were the case however, we should find religious mixing in LD tasks to lower output as well \u2013 but we do not find that.I nevertheless control for these factors in the line-section-level analysis, though the results remain robust to excluding theminstead.34but might be a problem in HD sections, given the nature of contact. In other words, it is differences ineducation between Hindus and Muslims that matter in some tasks and not others, as opposed to theproduction technology being the important factor.To deal with this, I introduce interactions between the dummy variable Mixed and these variablesas controls, in addition to the interaction terms Mixed \u00d7 HD and Mixed \u00d7 LD in the line-section-levelspecification. I specifically use three variables: group size, tenure of workers and schooling of workers.HD sections tend to have more workers, and one might be concerned about differences in responses ofworkers from being mixed in larger groups as opposed to smaller groups. For example, diversity mightbe costly when groups are larger because there is likely to be a wider set of issues that require coordi-nation on. The other two are more obvious choices given the differences amongst Hindu and Muslimworkers on these dimensions. The results are reported in Table A.17 \u2013 I introduce the interacted controlssequentially. Column 4 reports results from the specification with all the controls. Reassuringly, the in-teraction term Mixed \u00d7 HD remains negative and significant after the inclusion of these controls. Notethat the interactions Mixed \u00d7 Schooling and Mixed \u00d7 Tenure are both positive and meaningful in mag-nitude (though not statistically significant). This suggests that higher tenure and schooling can dampensome of the negative effects of diversity in HD sections. Note also in columns (3) and (4), the coefficientson the interaction term Mixed \u00d7 LD are statistically significant suggesting that diversity might be costlyin LD tasks as well, if workers have very low tenure or schooling.By design, Muslims workers are only in mixed teams in this experiment. In other words, the treat-ment of being in a mixed team is perfectly collinear with the presence of Muslims. This was done for twomain reasons. First, Muslims comprise of only 18% of all workers in the factory, whereby forming ho-mogeneous Muslim teams would lead to significant loss of statistical power in estimating the effects ofreligious mixing. Second, at baseline, there were no homogeneous Muslim teams to begin with; thereforeexperimentally generating such teams could raise ethical concerns. The issue this raises is that Muslimworkers may have lower productivity, and this could be driving my findings. However, the null effectof mixing in LD tasks suggests that this is extremely unlikely. Second, there is significant heterogene-ity in how mixed teams perform at HD tasks. When Hindus have been in mixed teams with Muslimsin the past, I find the negative effects of diversity to be muted significantly (see Table 2.8). If Muslims35generally had lower productivity, and especially so at HD tasks, it is unlikely that the negative effects ofmixing in these tasks would attenuate so significantly when analyzing heterogeneity by characteristics ofHindu workers in mixed teams. These results are discussed in more detail in the following section. Third,the large attenuation of the negative effects over time is also not consistent with Muslims having lowerproductivity at HD tasks. Finally, I find that Hindus and Muslims were equally like to be promoted asoperators or semi-skilled workers at the factory at baseline (see Table A.9). Since the skill-designation ofworkers affect salary, this suggests that the firm does not perceive Hindus and Muslims to be differen-tially productive either.36New versus old teammatesOne might be concerned that the finding that religious diversity negatively affects productivity is drivenin part by the difficulty of working alongside new co-workers, as opposed to the frictions that arise whenworking alongside non-coreligionists. This would be problematic if the share of new co-workers was notbalanced between HD- and LD-Mixed teams, as well as between mixed teams (HD or LD) and Hindu-only teams.I formally reject this possibility in the results reported in Table A.18. These are individual worker-levelregressions where the outcome variable is the proportion of workers in one\u2019s current team (randomizedteam) that were also in their line-section-level team pre-randomization. The mean of the outcome vari-able is 0.34, which is expected since workers in each production line-section were randomized betweenthree different cohorts \u2013 whereby roughly a third of the workers would be known to each other after newteams were formed. Importantly, as shown in Columns (1) and (2), the proportion of new workers isbalanced across mixed and non-mixed line-section-level teams. Further, the interactions Mixed \u00d7 HDand Mixed \u00d7 LD are small in magnitude and not statistically significant. This suggests that the findingsin this paper do not simply result from the inability of workers to coordinate with new colleagues, sinceworkers on average had the same proportion of new teammates irrespective of treatment status.36Further, the results in Table 2.7 (with only Hindus), do not suffer from this collinearity problem. They suggest that anenvironment that forces people to learn to work together is important to alleviate group-level differences. The positive effectson attitudes of Hindu workers would be unlikely if Muslims did not perform well at HD tasks.36Treatment status and section changes due to randomizationThe randomization process involved moving 7.9% of the workers from their original sections (tasks) atbaseline so that the line-level team structures in Figure 2.3 could be achieved. While this is a small shareof workers, it is nevertheless important to show that treatment status is not correlated with the probabil-ity of section-switching. If that were the case one could argue that the treatment effects are potentiallycontaminated. For example, if mixed HD teams have a greater share of workers who changed their sec-tions, it is possible that it is in fact the time required to adjust to new tasks that explains the results. To rulethis out, in Table A.19, I regress a dummy denoting whether the section (task) of a worker was changeddue to randomization, on the treatment dummies. In columns (1) and (2), I include only a dummy forwhether the team is religiously mixed or not (Mixed) and then in columns (3) and (4) I include its in-teractions with section type (HD or LD). I include line \u00d7 baseline section effects in columns (1) and (3)and line \u00d7 section effects in columns (2) and (4). The coefficients across the different specifications aresmall and not statistically significant. Only in column (4), the coefficient on Mixed \u00d7 HD is negative andmarginally significant, suggesting that the probability a worker switched their baseline section is actuallymarginally lower for those in mixed HD sections. This exercise therefore rules out the possibility that thetreatment effects are driven by differential rates of section-switching across treatment arms during therandomization process.2.6 MechanismThe three main findings of this experiment are: 1. Religious mixing leads to lower team output but onlyin HD tasks, 2. Output differences between mixed and non-mixed HD teams attenuate over time and 3.Attitudes of Hindus towards Muslims improve from mixing in HD tasks but not in LD. In this section, Ifirst discuss plausible mechanisms behind these core findings and then my favored explanation throughthe brief outline of a model. The predictions of the model are borne out by the data and these empiricaltests also help refute the other explanations.372.6.1 Assortative (mis)matching in complementary tasksIf Muslims have lower productivity, positive assortative matching (only all-Hindu and all-Muslim teams)would be the output maximizing allocation of workers in HD tasks. While this can explain the staticresults of mixing, there must additionally be on the job learning or skill transfer from Hindus to Muslimsin this framework to explain the dynamic results. However, evidence presented in section 2.5.3 alreadyrules out that Hindus and Muslims are differentially productive.2.6.2 CommunicationReligious mixing could also lead to lower output in HD tasks due to pure communication problemsamongst Hindus and Muslims. And over time, improving communication can cause production gains.An important strength of my setting is that there are no linguistic differences amongst religious groups\u2014 majority of the workers in my sample are born in the same district and speak the same language. It istherefore unlikely that the inability to communicate effectively with non-coreligionists is the key channeleither.372.6.3 Favored mechanism: Minority-stereotyping and discriminationHaving ruled out Hindu-Muslim differences in productivity and\/or communication breakdown as pri-mary channels, I focus on stereotyping and discrimination as the potential main mechanism. I present aconceptual framework (the full model is presented in section 2.10 at the end of the chapter) of minority-stereotyping to rationalize the core results (by the majority) and present its empirical tests.Outline of the conceptual frameworkA key distinction is made between Hindu and Muslim workers in this framework based on the asymmetryin their exposure to non-coreligionists at baseline. A large section of Hindu workers at the factory havenever worked with Muslims, while 100% of the Muslim workers have worked with Hindus (recall Figure2.1). Based on this, together with evidence on discrimination against Muslims in access to education andlabor markets in India (Kalpagam et al., 2010; Basant, 2007),38 I assume that Hindus (mistakenly) believe37Consistent with this, I find that baseline contact (self-reported) with Muslims outside of work (for Hindus) does not mitigatethe negative effects of mixing in HD tasks (see Table A.24). The hypothesis here is that greater contact with non-coreligionistsoutside of work might make individuals more effective communicators with them.38In fact, Muslims in my sample have significantly lower schooling than Hindus (Table A.9).38Muslims have lower productivity. Muslim workers do not make this distinction between in-group andout-group workers. This asymmetry in baseline priors leads to multiple equilibria in HD interactionsdue to complementarities in the production function.39Workers interact in teams for a given length of time and can exert high or low effort, with high effortbeing more costly. Hindus (depending on past exposure) start off with the belief that Muslims may not becapable of high effort: in other words with some probability Hindus believe Muslims are a behaviouraltype who always exert low effort (stereotyping).40 Hindus and Muslims are identical in all other aspects:both are capable of high effort and both face the same cost of effort. If Hindus assign a small probabilityto Muslims being capable, they optimally exert low effort in HD tasks, since the cost of high effort is toolarge given their belief. Hindu workers use Bayes rule to update their prior based on their own effortand realized output (teammate effort is not directly observed). Muslim workers understand that they arebeing underestimated and can \u201cinvest\u201d in shifting their Hindu teammate\u2019s prior.If Hindus exert low effort, it is a static best response for their Muslim teammates to also exert loweffort in HD tasks. However, I show that there is an equilibrium where given a fixed remaining inter-action length, Muslims invest in shifting beliefs of their Hindu teammates by exerting high effort (evenas Hindus exert low effort) if and only if Hindu workers\u2019 priors are not below a certain threshold value.The intuition behind this is that if Muslims exert high effort, Hindus observe greater realizations of highoutput events than expected given their belief; and therefore they gradually update. Once beliefs of Hin-dus are high enough such that they find exerting high effort optimal, a high-output static equilibrium iscoordinated on. Muslims only find their investment in the majority group worthwhile if initial Hindu be-liefs are not too low; since transition to the high-output equilibrium must occur early enough such thatMuslim workers\u2019 initial investment cost is compensated for by sufficient periods of high-output payoff.Empirical testsAn important implication of the model is that Hindu workers with a high initial belief that Muslims alsoexert high effort are less likely to discriminate against them. Therefore, Hindu workers who in the past39In HD tasks, the joint effort of all workers determines the likelihood of high (and low) output. In LD, total output is modelledas the sum of individual expected output (output is still a stochastic function of individual effort) and therefore the priors ofHindu workers are inconsequential in determining effort.40Hindus think Muslims may be behaviourally disposed to exerting low effort or face infinite cost of high effort \u2014 in terms ofthe model these two are equivalent.39have had Muslim co-workers (for a sufficiently long period of time), should continue to optimally exerthigh effort based on their higher priors, when randomized into a mixed HD team. At baseline, I collecteddata on a range of different factors that can help directly test this hypothesis. I have details of the teameach worker was in before the intervention which allows me to determine the degree of past contactthat they have had. In addition, I collected data on political preferences of workers at baseline. Thesespecifically relate to factors that could capture anti-Muslim sentiments.I test how these factors affect the performance of mixed teams in HD tasks41 in Table 2.8. In col-umn (1), I first show that there is an overall attenuation of the (negative) effects in HD tasks over time. Incolumns (2) and (3), I split the sample into the following parts: those teams in which Hindus (on average)have had above median contact with Muslims at baseline and those where they have had below mediancontact. Consistent with the model, the negative effect of diversity on team output is concentrated inthe second group, while the effect on the former is small and not statistically significant. In columns (6)and (7),42 I split the sample based on measures of political preference of Hindus to capture a differentset of stereotypes against Muslims. I use support for the (Hindu) majoritarian BJP party and the NRC(which together with the CAA has been widely regarded as discriminating against Muslims), proponentsof which might hold the stereotype that Muslims are inherently less patriotic and committed to the causeof the nation and its growth (Banerjee, 1991).43 The results follow the same pattern as for baseline ex-posure. The heterogeneity in the attenuation of the effects by characteristics of Hindus is also apparentin Columns (2)-(7). Mixed teams in which Hindus have either not worked with Muslims in the past, orhave low tenure, or strongly support the BJP\/NRC suffer larger losses initially from mixing and the effectsdo not completely dissipate, while the effects are smaller initially and dissipate entirely if Hindus do nothave these characteristics\/preferences. This is also consistent with the theory.A key feature of the model is that the minority group \u201cinvests\u201d in the majority group to amelioratenegative stereotypes about them. In Table 2.9, I restrict attention to only mixed teams (across HD and LD41I also study how these factors affect performance of mixed teams in LD sections. The effects are small in magnitude andnot statistically significant. These results are presented in Table A.20.42In columns (4) and (5), I split the sample based on tenure at the firm and find the effects to be driven by workers with lowtenure.43In terms of beliefs about effort, Hindus with these preferences might hold the prior that Muslims do not care enough abouteffort at work. In general, in the baseline data I find that Hindus who have had greater contact with Muslims are less likely tosupport the NRC or report to favour the BJP. These correlations are consistent with the results in Table 2.8.40sections) and use dummies for the religion of the respondent, that of the person being referred to in thesurvey question, and their interaction as the main regressors. Columns (1), (3) and (5) show that whileMuslim workers are more likely to be identified as not contributing effort, be blamed and have fewerco-workers willing to give up relief time for them (over the entire intervention), they themselves are lesslikely to criticize their co-workers.The coefficients on the interaction terms introduced in Columns (2), (4) and (6) show that the criticismof Muslim workers come largely from their Hindu counterparts, while Muslim workers are actually will-ing to give up relief time for Hindu co-workers with a higher probability (than for Muslim co-workers).This decomposition lends support to the idea that it is indeed stereotyping of minorities by the majoritygroup which results in lower team cohesion and output initially; while the minority group initiates theintegration process.44Taken together, these results support minority-stereotyping and discrimination as the primary mech-anism behind the core results. They also provide evidence against the hypothesis that Muslims may havelower productivity, or that the negative effects of mixing in HD tasks result from communication issues.These latter explanations are inconsistent with the null effects in mixed teams in which Hindus have lessstereotypical attitudes towards Muslims.2.7 Policy discussion: Firm supervisor surveyDo firm supervisors understand the costs of diversity and how they depend on the production function?Can they predict the findings from this experiment, and if so, do they suggest integration of workers onlyin LD tasks or do they recommend other management practices to ameliorate possible negative effectsof religious mixing in HD tasks? To analyze these policy relevant questions, I surveyed supervisors andoperators (personnel with some leadership role) of five different processed food manufacturing plantsin April, 2021.Participants were first asked to denote which of the two tasks (HD or LD in Figure A.8): (1) requiresgreater continuous coordination and communication amongst co-workers and (2) is likely to cause more44In Table A.21, I further decompose the findings of Table 2.9 into HD and LD sections and show that the effects discussedabove are driven by HD sections and less so by LD sections.41frictions and arguments amongst workers. They picked the HD task more frequently for both of thesequestions (Figure A.13). Interestingly, while close to 80% of the supervisors chose the HD task for (2),a fair share of them also picked either the LD task (17%) or mentioned both HD and LD (35%) for (1).This reiterates an important point about the mechanism behind the core results in this paper: workersdo not simply sabotage or undermine the efforts of their out-group members, which is possible to do inLD tasks as well. Rather, a negative perception of out-group members causes frictions which are costlywhen working in production environments that require workers to be significantly dependent on eachother.Participants were then asked to predict whether a religiously homogeneous or mixed team wouldbe more productive in each task. They were informed that I have conducted an experiment to test thisand that they would be rewarded with Rs 25 (about 30% of their hourly wage) if their answer matcheswith my findings\u2014 this was meant to reduce social desirability bias in the answers. Between 40%-45% ofthe supervisors mentioned that religiously mixed teams would be more productive in both tasks (FigureA.14). This could be because of social desirability bias or as I show next, supervisors actually think ofissues beyond direct productivity arising from segregation of workers (by religion), which prompts themto answer in this manner. Nevertheless, a significantly higher share of respondents mentioned that ahomogeneous team would be more productive at the HD task (30%) than the LD task (8%). Overall,about a third of the supervisors predicted correctly that homogeneous teams would be more productivein HD tasks and about half of them correctly mentioned that mixing would be inconsequential in LDtasks.While it is possible that a large share of supervisors do not understand the costs of diversity and con-sequently do not segregate workers, it is also possible that there are additional costs that do not justifysegregation. To understand this systematically, respondents were finally asked if they are willing to segre-gate workers by religion and\/or age if workers do not perform well as a team because of these differences.I use age as a natural benchmark because in the Indian context age differences could be an importantsource of conflict amongst teammates. The supervisors generally seem to be averse to segregation oneither dimension, but they are especially opposed to segregation by religion (Figure A.15), despite thepotential for losses. About a quarter of the supervisors correctly (as I find) cite negative effects of diver-42sity dissipating over time as their reason. However, the first order concern is about segregation actuallyraising tensions further. Informal conversations with supervisors suggest that some of the concerns theyhave in mind are with respect to such segregation creating a hostile environment in common areas ofinteraction (canteen, tea room), in addition to tensions on the production floor.In sum, this survey shows that roughly between a third to a half of the supervisors correctly predictedthe results of the intervention. However, it is clear that despite the possibility of losses, the majority ofsupervisors are averse to segregation of workers by religion. Many of them, being aware of the long-term gains from repeated contact are willing to trade off potential short-run costs of non-segregation toproductivity. But they are also concerned about costs to segregation that are typically hard to identify asa researcher by simply analyzing production data. This is perhaps why previous studies find it difficultto reconcile productivity losses arising from diversity with non-segregation of workers in the firms theystudy (Hjort, 2014).Speculatively, the short-run but significant cost associated with organizing HD production with anethnically diverse workforce may impede firms (especially those with low working capital) from grow-ing and adopting complex assembly-lines processes in developing countries (Kremer, 1993; Hsieh andOlken, 2014). Since the manufacturing sector is likely to have a larger concentration of HD tasks (relativeto agriculture or services), this could be one potential explanation for why ethnically fractionalized coun-tries have lower share of employment in manufacturing as well as firms with lower foreign technologytake up \u2013 even after controlling for income (Figure 2.6).The implications of the interaction between ethnic diversity and production technology for broader eco-nomic change can be an important avenue for future research.2.8 ConclusionMy findings suggest that both the nature and duration of contact are important in understanding how re-ligious diversity in firms may impact productivity. An environment that makes workers highly dependenton each other creates incentives for them to invest in building social capital with out-group members.This brings about positive changes in attitudes as well as productivity gains over time, but it might be un-profitable in the short-run through lost output. Overall, my results suggest a potential tension between43the goal of maximizing short-run productivity and that of improving intergroup relations. More spec-ulatively, they might help explain why in equilibrium there can be a lot of integration at work withoutintergroup relations improving \u2013 the integration might only occur in contexts where intergroup contactis socially ineffective.Beyond conceptual contributions, this chapter has a few important implications for policy. First,firms with high-dependency production should minimize team switching in order to mediate possi-ble negative effects of diversity. Second, in firms with low-dependency production, exposure to non-coreligionists might not necessarily reduce negative outgroup attitudes. While this might cost the firmlittle in terms of lost output, a less cohesive work culture can lead to problems outside of daily pro-duction. Such firms might benefit from additional measures to ensure a collaborative environment forworkers to interact in. This can even be achieved outside the workplace, for example though sportsteams (Lowe, 2021; Mousa, 2018). In general, an open question remains whether that can also lead toproductivity gains at the workplace. If that is indeed the case, the cost to output from mixing workersin HD tasks to integrate them could be avoided.45 However, if belief updating with respect to specificsabout co-workers\u2019 effort levels at work is the driving factor (as suggested in the theoretical framework),contact outside the firm might not be able to entirely mitigate the negative effects of diversity.As economies undergo structural transformation, the nature of economic production changes, whichpotentially influences the type of inter-ethnic interactions. My results suggest that the costs of diversitymay increase as economies move away from traditional agriculture to manufacturing activity and thendecrease with the transition to services. In traditional agricultural societies, land cultivators largely workin LD environments with limited contact with new people, but manufacturing activity involves a highershare of HD work (construction work, small firms etc.), as well as contact with new people on a regularbasis, making diversity costly. In services, with a comparatively higher share of LD work and a regularset of colleagues, these costs might be low again. One important aspect of this is that identity diversitymight act as a hindrance in transitioning to formal manufacturing work by perpetuating discriminationamongst groups (A.Churchill and Danquah, 2020).Finally, the finding that minorities (Muslims) bear the cost of integration in this context is general-45Of course arranging such organized collaborative contact might itself be costly for a firm in terms of time and resources.44izable to many other settings, especially the U.S. For example, the argument that African-Americans arerewarded less for their effort (relative to the average American), requiring them to work harder to achievesimilar career goals (DeSante, 2013) or the finding that Asian immigrants in the U.S., being aware of theirunequal racial status, work twice as hard as a normative path to success and assimilation by achievingmodel-minority status (Zhou, 2004 and Zhou and Xiong, 2005), relate closely to my results in the In-dian context. Overall, this implies that minority (the oppressed) groups, despite being discriminatedagainst, may play a crucial role in the process of nation-building through initiating economic and socialintegration in diverse societies. But the above statement must be caveated \u2013 we still have much left tounderstand with respect to if\/how this would also translate into assimilation in the sense that they donot feel a divide between participation in mainstream institutions and cultural practices.2.9 Tables and figures2.9.1 TablesTable 2.1: Proportion Muslim by line-level team and cohort (at baseline)Line Cohort 1 Cohort 2 Cohort 3 AverageLine 1 0.30 0.23 0.19 0.24Line 2 0.11 0.07 0.27 0.15Line 3 0.24 0.24 0.13 0.20Line 4 0.22 0.26 - 0.23Line 5 0.15 0.19 0.07 0.14Line 6 0.14 0.07 0.23 0.15Average 0.19 0.18 0.18 0.18Note: Each production line (apart from Line 4) has a total of three cohorts working on it in each of thethree shifts in a day. This table reports the share of Muslim workers in each line (across all sections) atbaseline \u2013 for all three cohorts. Please note the total number of workers in each line-cohort is the same.45Table 2.2: Characteristics of High- and Low-Dependency tasksWork condition High-Dependency (HD) Low-Dependency (LD)Task coordination High and Continuous Low and IntermittentControl over breaks Low HighPhysical mobility Restricted GoodRepetitive monotony High (Machine Speed) Low (Occasionally paced by machine)Note: This table lists some key differences between work characteristics of High- and Low-Dependency tasks.46Table 2.3: Randomization checkPanel A: Outcomes relevant at work Panel B: General characteristics and attributesTenure Muslim co-workers Taking Communicating Age Schooling Trust Altruism Inter-religious con-Hindus Orders tact outside work(1) (2) (3) (4) (5) (6) (7) (8) (9)Mixed \u00d7 LD 0.0623 0.0277 0.0496 0.0857 1.5012 -0.2158 0.5354 0.0280 0.0371(0.3378) (0.0219) (0.0556) (0.0525) (1.4079) (0.5013) (0.3505) (0.2203) (0.0475)Mixed \u00d7 HD -0.0042 0.0169 -0.0027 -0.0347 0.7232 0.3499 -0.0883 -0.0495 0.0088(0.3259) (0.0172) (0.0471) (0.0481) (0.8184) (0.3619) (0.3015) (0.1649) (0.0475)p(Mixed \u00d7 LD = Mixed \u00d7 HD) 0.87 0.70 0.44 0.07 0.60 0.33 0.14 0.75 0.65Mean Dep Var. 4.45 0.12 0.73 0.53 34.47 7.84 3.79 6.65 0.45Line \u00d7 Section F.E. Yes Yes Yes Yes Yes Yes Yes Yes YesReligion F.E. Yes No Yes Yes Yes Yes Yes Yes YesN 586 478 586 586 586 586 586 586 586Adj. R2 0.122 0.029 0.012 0.045 0.076 0.070 -0.005 -0.013 0.099* p<0.10, ** p<0.05, *** p<0.010. The unit of observation is an individual worker. Standard errors clustered at the line-section-level team. \"Tenure\" and\"Schooling\" are measured in years and as highest grade completed respectively. \"Taking Orders\" is a dummy variable coded 1 if the respondent reported to bealways comfortable taking orders from non-coreligionists and 0 if they reported to be sometimes or always uncomfortable. \"Communicating\" is coded 1, 0.5and 0 for the responses \u201cAlways comfortable\u201d, \u201cSometimes uncomfortable\u201d and \u201cAlways uncomfortable\u201d when asked about being comfortable communicatingwith non-coreligionists. Survey questions on \u201cTrust\" and \u201cAltruism\" are used from the World Value Survey (WVS). The dependent variable \"Inter-religiouscontact\" refers to the degree of cross-religion interaction that workers had at baseline, outside of work. The variable is coded 1, 0.5 and 0 if a worker mentionedthat during the daily course of their life they: 1) interact with more than 5 non-coreligionists 2) interact with 1 to 5 non-coreligionists, or 3) do not interact withanyone outside their religion, respectively.47Table 2.4: Treatment effect on line-level output(1) (2)Log Output (Pieces) Log Output (Boxes)HD-Mixed vs LD-Mixed Line -0.0487*** -0.0519**(0.0163) (0.0220)Bootstrap (Wild Cluster) C.I. [-0.093, -0.013] [-0.107, 0.007]Day F.E. Yes YesShift F.E. Yes YesProduction Line F.E. Yes YesMean Dep Var. 10.80 6.97(1.24) (0.943)N 1045 1045Adj. R2 0.722 0.644* p<0.10, ** p<0.05, *** p<0.010. Observations are daily output produced byline-level teams. Standard errors clustered at the line-level team in paren-thesis. Wild cluster bootstrap (Cameron et al., 2008) confidence intervals insquare brackets. HD-Mixed Line is a dummy coded 1 for a line-level teamwith all HD sections religiously mixed and LD sections non-mixed, and 0 forexactly the opposite line-level structure (LD-Mixed Line).48Table 2.5: Treatment effect on section ratingsRating (Raw) Rating>Median(1) (2) (3) (4)Mixed -0.0204* -0.0254***(0.0119) (0.00899)Mixed \u00d7 LD -0.0067 -0.0047(0.0144) (0.0121)Mixed \u00d7 HD -0.0349** -0.0474***(0.0185) (0.0121)p(Mixed \u00d7 HD = Mixed \u00d7 LD) 0.229 0.011Mean Dep. Var. 3.82 3.82 0.44 0.44(0.83) (0.83) (0.50) (0.50)Education and Tenure Controls Yes Yes Yes YesDay F.E. Yes Yes Yes YesShift F.E. Yes Yes Yes YesLine \u00d7 Section F.E. Yes Yes Yes YesN 6909 6909 6909 6909Adj. R2 0.600 0.600 0.358 0.358* p<0.10, ** p<0.05, *** p<0.010. Observations are daily ratings received by line-section-levelteams. Standard errors clustered at the line-section-level team. \u201cMixed\" is a dummy variablecoded 1 if the line-section-level team is religiously mixed. Line \u00d7 Section fixed effects are in-cluded in the all specifications; as a result the main effect of HD versus LD is not separatelyidentified in columns (2) and (4). Education and tenure control for the mean of schooling andtenure of workers in the line-section-level team.49Table 2.6: Treatment effect on worker interactionsIdentified teammate as Blamed Unwilling to give upcontributing low effort by teammate relief time(1) (2) (3) (4) (5) (6)Mixed 0.0420*** 0.0400** 0.0640*(0.0137) (0.0158) (0.0365)Mixed \u00d7 LD 0.0317 0.0817*** 0.0339(0.0226) (0.0228) (0.0563)Mixed \u00d7 HD 0.0445*** 0.0301* 0.0719*(0.0154) (0.0175) (0.0423)p(Mixed X HD = Mixed X LD) 0.62 0.05 0.57Mean Dep. Var 0.14 0.14 0.08 0.08 0.25 0.25Worker Skill F.E. Yes Yes Yes Yes Yes YesReligion F.E. Yes Yes Yes Yes Yes YesLine \u00d7 Section F.E. Yes Yes Yes Yes Yes YesObservations 3696 3696 3684 3684 3727 3727Adj. R2 0.016 0.016 0.013 0.014 0.072 0.072* p<0.10, ** p<0.05, *** p<0.010. Observations are at the worker-teammate level for line-section-level teams i.e. there are (N-1) observations per worker, where N denotes the number of workers inthe section. Standard errors clustered at the line-section-level team. \u201cMixed\" is a dummy variablecoded 1 if the line-section-level team is religiously mixed. Line\u00d7 Sections fixed effects are includedin the all specifications; as a result the main effect of HD versus LD is not separately identified incolumns (2), (4) and (6). Workers were asked to choose teammates who they: (1) think have notcontributed sufficient effort at any point during the intervention (2) have been blamed by duringthe intervention and (3) would give (or already have) up their relief time for.50Table 2.7: Treatment effect on attitudes at endline: HindusAttitudes towards MuslimsComfortable: Taking Orders Communicating Co-working(1) (2) (3) (4) (5) (6)Mixed 0.1249*** 0.0985** 0.1145***(0.0448) (0.0403) (0.0348)Mixed \u00d7 LD 0.0180 -0.0781 0.0198(0.0778) (0.0618) (0.0626)Mixed \u00d7 HD 0.1866*** 0.2004*** 0.1691***(0.0555) (0.0406) (0.0439)p(Mixed \u00d7 HD = Mixed \u00d7 LD) 0.086 0.000 0.076Mean Dep. Var. 0.74 0.74 0.49 0.49 0.61 0.61Sample Baseline Mean Baseline Mean Endline Non-mixed MeanBaseline controls Yes Yes Yes Yes Yes YesWorker skill F.E. Yes Yes Yes Yes Yes YesLine \u00d7 Section F.E. Yes Yes Yes Yes Yes YesN 448 448 448 448 448 448Adj. R2 0.066 0.072 0.066 0.088 0.063 0.068* p<0.10, ** p<0.05, *** p<0.010. The unit of observation is an individual worker. Standard errorsclustered at the line-section-level team. \u201cMixed\" is a dummy variable coded 1 if the line-section-levelteam is religiously mixed. The main effect of HD versus LD is not separately identified in columns(2), (4) and (6) because Line \u00d7 Section fixed effects are included. \u201cTaking Orders\u201d is a dummy variablecoded 1 if the respondent reported to be comfortable taking orders from Muslims, and 0 otherwise.\u201cCommunicating\u201d is coded 1, 0.5 and 0 for the responses \u201cAlways comfortable\u201d, \u201cSometimes uncom-fortable\u201d and \u201cAlways uncomfortable\u201d respectively, when asked about being comfortable communi-cating with Muslims. For \u201cCo-working\" the outcome is coded 1,0.5 and 0 for the responses \"Mixedteam\", \"Indifferent\" and \"Hindu-only team\" when asked about respondents\u2019 preferred team type forfuture changes.51Table 2.8: Heterogeneous attenuation by characteristics of Hindus at baseline (HD section ratings)Sample: Full Contact at Baseline Tenure at Baseline Support for BJP and NRC(1) (2) (3) (4) (5) (6) (7)Above Median Below Median Above Median Below Median Above Median Below MedianMixed \u00d7 0-60 days -0.0661* -0.0458 -0.1816*** 0.0202 -0.0953** -0.1248*** -0.0496(0.0391) (0.0498) (0.0595) (0.0800) (0.0431) (0.0438) (0.0619)Mixed \u00d7 61-120 days -0.0355 -0.0195 -0.0802** 0.0497 -0.0319 -0.0792*** 0.0177(0.0234) (0.0429) (0.0337) (0.0500) (0.0325) (0.0242) (0.0712)Mean Dep. Var. 3.86 3.83 3.89 3.84 3.88 3.87 3.83Education and Tenure Controls Yes Yes Yes Yes Yes Yes YesDay F.E. Yes Yes Yes Yes Yes Yes YesShift F.E. Yes Yes Yes Yes Yes Yes YesLine \u00d7 Section F.E. Yes Yes Yes Yes Yes Yes YesObservations 3466 1884 1582 1462 2004 2384 1082Adj. R2 0.609 0.633 0.596 0.605 0.620 0.602 0.631* p<0.10, ** p<0.05, *** p<0.010. Observations are daily ratings received by line-section-level teams. Standard errors clustered at the line-section-level team. \u201cMixed\" is a dummy variable coded 1 if the line-section-level team is religiously mixed. In column (2), the sample consistsof all line-section-level teams in which the share of Muslim teammates, that Hindus in that team had at baseline, is above median. In column(3), the sample consists of all line-section-level teams in which the share of Muslim teammates, that Hindus in that team had at baseline,is below median. In columns (4) and (5) teams are split by median tenure of Hindus at baseline. In column (6), the sample consists of allline-section-level teams with above median support for the BJP or the NRC (averaged across all Hindu workers in the team). In Column (6),the sample consists of all line-section-level teams with below median support for the BJP or the NRC (averaged across all Hindu workers inthe team).52Table 2.9: Treatment effect on worker interactions: Decomposition (Mixed teams)Identified teammate as Blamed Unwilling to give upcontributing low effort by teammate relief time(1) (2) (3) (4) (5) (6)Target Muslim 0.0528*** 0.0861*** -0.0159 0.0048 0.0474*** 0.0090(0.0175) (0.0225) (0.0126) (0.0213) (0.0176) (0.0332)Respondent Muslim -0.0172 0.0152 -0.0009 0.0192 -0.0450 -0.0830**(0.0221) (0.0266) (0.0199) (0.0291) (0.0316) (0.0356)Target Muslim \u00d7 -0.0995** -0.0612 0.1139*Respondent Muslim (0.0485) (0.0406) (0.0657)Mean Dep. Var 0.15 0.15 0.10 0.10 0.28 0.28Worker Skill F.E. Yes Yes Yes Yes Yes YesLine \u00d7 Section F.E. Yes Yes Yes Yes Yes YesObservations 2033 2033 2029 2029 2035 2035Adj. R2 0.018 0.025 0.013 0.016 0.064 0.084* p<0.10, ** p<0.05, *** p<0.010. Observations are at the worker-teammate level for line-section-level teams i.e. there are (N-1) observations per worker, where N denotes the number of workers inthe section. Standard errors clustered at the line-section-level team. Workers were asked to chooseteammates who they: (1) think have not contributed sufficient effort at any point during the inter-vention (2) have been blamed by during the intervention and (3) would give (or already have) uptheir relief time for.532.9.2 FiguresFigure 2.1: Structure of production linesStages of ProductionProportion MuslimLine 3Line 5Mixing (4) Deposit (11) Oven (2) Tray\/Cooling(4) Depanning (4) Packing (8) Cfc (5)Mixing (3) Deposit (10) Oven (2) Injector (3) Depanning (11) Packing (4) Cfc (5)Mixing (2) Oven (2) Cooling (5) Packing (6) Cfc (3)Mixing (3) Oven (3) Cream (6) Packing (5) Box Machine (2)Box FIlling (14) Cfc (5)Mixing (3) Oven (3) Cream (6) Packing (5) Box Machine (2)Box FIlling (14) Cfc (5)Line 1Line 2Line 6Line 4Mixing (3) 1st Line (3) 2nd Line (12) Oven (2) Tray Wash (4) Injector (3) Depanning (4) Packing (4) Cfc (11)f ( )Note: This figure shows the structure of all six production lines in the factory. The numbers in parentheses denote the countof workers in each section per cohort. Each production line has three cohorts working on it in each of the three shifts in a day.The color shades denote the proportion of Muslim workers in each section in one particular cohort at baseline. Please refer tofigure A.5 in the Appendix for this figure without the color shades.54Figure 2.2: Distribution of Direct DependencyNote: This figure shows the distribution of Direct Dependency. Enumerators visited every section of each production line andtook stopwatch measures of the number of minutes (out of 10) for which workers were continuously dependent on each otherfor production to occur. The figure is generated from these stopwatch records at the line-section-level.Figure 2.3: Randomized team structureHD-Mixed LineMixing high-dependency sectionsMixedLD-Mixed LineMixing low-dependency sectionsLD HD LD HD LD HD HDLD HD LD HD LD HD HD Non-Mixed (Hindus)Note: This figure shows the two different types of line-level teams after randomization. Sections are partially shaded to denotemixed teams. HD-Mixed lines had all their HD sections mixed and LD sections non-mixed. The opposite is true for LD-Mixedlines.55Figure 2.4: Experimental design and timeline Line Level Teams: 15 HD-Mixed Lines: 7LD-Mixed Lines: 8Survey Data In-person Survey N= 586Hindus: 480 (81.9%)Muslims: 106 (18.1%)HD-Mixed: 23LD-Mixed:33 LD Non-Mixed: 29Attrition Rate: 6.8%Endline Phone SurveyN= 546Hindus: 448 (82%) Muslims: 98 (18%)Time-use data collection for classification of tasks into HD and LD typesBaseline Survey HD and LD ClassificationRandomization and ImplementationLine-LevelLine-Section-LevelEndline SurveyJuly (2019)-August (2019)October (2019) November (2019) - March (2020) April (2020)- May (2020) ... ... ......HD  Administrative Production Data...Survey DataLDHDHDLD LDHD HDHDLD LD LD LD HD HD HDLD LD LD LD HD HDH...HDLD HDLD LD LD HD HD LD HD LD LD HD HDLDHDLDLDHD Non-Mixed:28Line-Section-Level Teams: 113HD Non-Mixed: 196LD Non-Mixed: 98     Total Workers: 586(Hindus: 480, Muslims:106)      Individual-Level LD-Mixed: 117HD-Mixed: 175Note: Shaded boxes denote mixed teams. The share of Muslim workers in mixed teams is between 35%-40% (balanced across HD and LD sections). This diagram showsthe timeline of the intervention. The baseline survey was completed between July and August in 2019. Time-use data in order to classify tasks into HD and LD typeswere collected in October 2019. The experiment was conducted between November 2019 and March 2020. Details of sample size by treatment arms are presented in thefigure. A phone survey was conducted at endline in April and May of 2020 due to COVID-19 related restrictions.56Figure 2.5: Treatment effect on line-level output (Event study)Note: This figure is generated from binned regressions (this plot is created using the STATA command binsreg, which imple-ments binscatter estimation with robust inference proposed in Cattaneo et al. (2019)). using exactly the same controls variablesas in Table 2.4. The treatment period is divided into 5 equal sized bins. The outcome variable is output produced in pieces(logged). Bars denote 95% confidence intervals.Figure 2.6: Ethnic diversity and the manufacturing industryNote: Data on ethnic fractionalization come from the Historical Index of Ethnic Fractionalization (HIEF) dataset. Data on shareof workers in manufacturing and percentage of firms using foreign technology are obtained from the World Bank EnterpriseSurvey.572.10 Full ModelThis section presents the theoretical framework. The primary objective of the model is to rationalize thecore empirical results, especially the mechanism behind the attenuation in output losses in HD-mixedsections over time. The model makes predictions specially with respect to heterogeneous treatmentseffects based on worker characteristics, which I subsequently test for in the data.A key distinction is made between Hindu and Muslim workers in this framework. Consistent withmajority-minority relations, a large section of Hindu workers at the factory have never worked with Mus-lims in the past, while 100% of the Muslim workers have worked with Hindus. Based on this asymmetryin exposure at baseline, together with the evidence on discrimination against Muslims in access to edu-cation and labor markets in India (Kalpagam et al., 2010; Basant, 2007),46 I assume Hindus (mistakenly)on average believe that Muslims are not as hardworking as them.47 Muslim workers do not make thisdistinction between in-group and out-group workers given that they have had much greater contactwith Hindus. This asymmetry in baseline priors leads to multiple equilibria in HD interactions due tocomplementarities in the production function, while in LD this does not matter.As mentioned, Muslims have accurate priors about Hindus, while Hindus might not necessarily havethem, it will depend on past exposure. Muslims are aware that they are being stereotyped by Hindus butcan \u201cinvest\" in shifting the priors of Hindus.2.10.1 SetupProduction is composed of two types of tasks, HD (high-dependency) and LD (low-dependency). I makethe following assumptions about the production process:1. There are two workers in each type of task (generalizes to multi-worker easily)2. There are two types of output: High (OH ) and Low (OL)3. Worker effort is the only input in production and it is not observed directly by teammates46In fact, Muslims in my sample have significantly lower schooling than Hindus (Table A.9).47An implicit assumption here of course is that in reality Hindus and Muslims are equally productive. I present direct evidencefor this in section 2.5.3.584. There are two types of effort: High (eH ) or Low (eL)5. Output in each task is a noisy function of worker effort6. Effort is costly: c(eH ) > c(eL) = 0Assumptions 1,2,4 and 6 are made for simplicity and easily generalizes to settings where output,effort and effort cost are continuous variables and there are multiple workers in each task. There areseveral factors that workers do not have direct control over which influence productivity and also makeperfectly observing teammate\u2019s effort difficult. These include machine breakdowns, inadequate raw ma-terial planning and unanticipated production stoppages due to supply chain issues. Assumptions 3 and5 are made based on these factors.The production function for HD tasks can be written as:yHD (ek1,ek2) = p(ek1,ek2)OH + {1\u2212p(ek1,ek2)}OL (2.4)where eki denotes effort level k = (H , L) for worker i = (1, 2). p(ek1,ek2) denotes the probability of highoutput (OH ) conditional on effort. Clearly, the joint effort of both workers determines the probability ofhigh output and the marginal value of effort is thus higher in teammate\u2019s effort level.The probability of high output conditional on effort levels of both the workers are:(eH ,eH ) = pH (2.5)(eH ,eL) = (eL ,eH ) = pHL (2.6)(eL ,eL) = pL (2.7)where pH > pHL > pL . The production function in LD tasks is linear in worker efforts and is written as:yLD (ek1,ek2) =2\u2211i =1{p(eki )oh + (1\u2212p(eki ))ol } (2.8)where oh and ol denote high and low individual output levels respectively. In LD sections total outputis therefore the sum of individual expected output. The probability of high and low output (conditional59on eH and eL) are pH and pL respectively with pH > pL .2.10.2 One shot productionIn HD sections, high effort (eH ) is statically preferred by a worker if and only if their teammate also exertshigh effort (eH ). In other words, there is no incentive to free-ride when teammate exerts eH . Mathemat-ically, this condition implies:(pH \u2212pHL)(OH \u2212OL)> c(eH )> (pHL \u2212pL)(OH \u2212OL)48 (2.9)In LD sections, value of a worker\u2019s effort is not dependent on teammate\u2019s effort level. As a result weassume eH is the dominant action, implied by:(pH \u2212pHL)(OH \u2212OL)> c(eH )49 (2.10)2.10.3 Analysis of the modelWorkers interact repeatedly for T periods in a task. HD sections are the interesting case here due tocomplementarity in worker efforts in the production function. I first solve the model for HD sectionsand subsequently discuss LD sections.Hindu workers (majority group)Hindu workers who are in mixed teams could have been in non-mixed ones, which they believe wouldbe more productive. In other words, they assign probability \u03c0t (in period t , initial belief is \u03c00) on theirMuslim teammate exerting high effort, which in the case of coreligionists (other Hindus) is 1. Therefore,with probability (1-\u03c0t ) Hindus believe Muslims maybe be \u201clazy\" \u2013 a behavioural type that always exertslow effort. This can be thought of as Hindus thinking Muslims have infinite cost of high effort or thatthey are simply behaviourally disposed to exerting low effort.48This expression is obtained by re-writing: pH OH + (1\u2212 pH )OL - c(eH ) > pLOH + (1\u2212 pL)OL > pHLOH + (1\u2212 pHL)OL -c(eH ).49The expression is ph oh + (1\u2212ph )ol - c(eH ) > pl oh + (1\u2212pl )ol .60A Hindu worker\u2019s problem is then given by:V = max(et )Tt=0T\u2211t=0Pt (et ,\u03c0t ) (2.11)where et denotes the action in period t (choice variable), \u03c0t is the prior at t (state variable) and Pt (et ,\u03c0t )is the expected (perceived) payoff at time t . Each period, given their current prior, their own action andrealized output, the Hindu worker\u2019s belief about the effort level of their Muslim teammate is updated.The transition matrix at any period t , with current prior \u03c0t , is:Table 2.10: Bayesian updating (Hindu workers): Prob(Muslim worker exerts eH )Own Effort\/Realized Output OH OLeH\u03c0t pH\u03c0t pH+(1\u2212\u03c0t )pHL\u03c0t (1\u2212pH )\u03c0t (1\u2212pH )+(1\u2212\u03c0t )(1\u2212pHL )eL\u03c0t pHL\u03c0t pHL+(1\u2212\u03c0t )pL\u03c0t (1\u2212pHL )\u03c0t (1\u2212pHL )+(1\u2212\u03c0t )(1\u2212pL )Note: The prior of a Hindu worker in period t is denoted by \u03c0t .Muslim workers (minority group)Unlike Hindu workers, Muslim workers have always been in mixed teams. They are used to being stereo-typed in this manner. In other words they are aware that Hindus are operating on incorrect priors.Muslim workers choose an optimal effort investment path based on the time horizon. At any giventime t and set of history s (which determines prior \u03c0t of Hindu teammates), Muslim workers choose aneffort level. Their problem can be written as:V = E\u03c8(T\u2211t=0Pt (at , st )|\u03c0o) (2.12)where \u03c8 denotes the mapping from a set of histories (from 0 to t \u2212 1) to actions at = (eH , eL) and Ptdenotes expected payoff in each period conditional on the set of history and preferred action choice inthat period. State st (history of high vs low output events) defines the current belief (\u03c0t ) of the Hinduworker regarding their Muslim co-worker.Note that for any t=k, the problem above can be re-written asV \u03c8k (s) = {\u2211s\u2032\u2208Sk+1Pk (s, a)+\u00b5k (s\u2032|s, a)V \u03c8k+1(s\u2032)},k = N \u22121, ....,0 (2.13)61where \u03c0 denotes mapping from each possible history ht = (so , ao ,.....,st\u22121, at\u22121) to actions at = \u03c8t (ht ).\u00b5(.) denotes the probability of a future state (belief of the Hindu worker) conditional on actions andcurrent state. The optimal effort path for a Muslim worker is then a mapping from state histories toactions \u03c8\u2217 such that,\u03c8\u2217k (s) \u2208 ar g maxa\u2208eH ,eL {\u2211s\u2032\u2208Sk+1Pk (s, a)+\u00b5k (s\u2032|s, a)V \u03c8\u2217k+1(s\u2032)} (2.14)Markov EquilibriumIt is clear from equation (2.9) that statically there are two equilibria of this game, one where both workersexert eH and the other where both exert eL . Since this game is repeated, it is possible to have strategiesthat are a function of the history of the game, as well as beliefs of Hindu workers. I am not going to ruleout the possibility of some complicated equilibria based on such strategies. Instead, I will be looking atan equilibrium where individuals condition behaviour on commonly known beliefs of Hindus.Definition: P\u00af is the probability that a Hindu believes a Muslim is exerting eH beyond which it is staticallypayoff maximizing for a Hindu to also contribute eH .P\u00af is the threshold value such that if \u03c0t is greater than this value, or in other words if Muslims are believedlikely enough to be contributing high effort, Hindus will exert high effort in response. Note that P\u00af isexogenous and is obtained by comparing net expected payoff to a Hindu worker from exerting high effortversus exerting low effort, given \u03c0t .For a given value of \u03c0t , the payoff from exerting eH and eL are as follows:P (eH ,\u03c0t ) =\u03c0t {pH OH + (1\u2212pH )OL}+ (1\u2212\u03c0t ){pHLOH + (1\u2212pHL)OL}\u2212 c(eH ) (2.15)P (eL ,\u03c0t ) = pt {pHLOH + (1\u2212pHL)OL}+ (1\u2212\u03c0t ){pLOH + (1\u2212pL)OL} (2.16)Comparing (2.15) and (2.16) high effort yields high greater payoff iff (2.15) > (2.16), which is the casewhen\u03c0t > c(eH )\u2212 (pHL \u2212pL)(OH \u2212OL)(pH +pL)(OH \u2212OL)= P\u00af (2.17)This gives us P\u00af . From equation (2.9) it can be seen that the numerator in the RHS is positive. Given this,62I now proceed to characterizing the equilibrium.Proposition: There exists an equilibrium in which, for a given remaining interaction length T , there is a\u03c0T \u2264 P\u00af , such that for \u03c0 \u2265 \u03c0T , Muslims will exert eH . If \u03c0 < \u03c0T Muslims exert eL . Along the equilibriumpath, Hindus exert eL when \u03c0< P\u00af and eH otherwise.Proof: A formal is provided at the end of the section, I provide the intuition for the proof here. If\u03c0 is lowerthan P\u00af (at a certain period t ), or in other words if the belief of the Hindu worker is not high enough to ex-ert eH , it is a static best response for the Muslim worker to also exert eL . However, the Muslim worker can\"invest\" in shifting priors of the Hindu worker, if it leads to higher payoff in expectation by transitioningto a high output static equilibrium. In order for that to be worthwhile, there must be enough periods inexpectation with \u03c0 > P\u00af , such that the cost of exerting eH (while the Hindu worker exerts eL) is compen-sated for and net payoff to the Muslim worker is greater than exerting eL (in expectation). At time t , givena remaining interaction length T , \u03c0T is the minimum (threshold) value (of \u03c0) for eH to be worth for theMuslim worker.50 If the belief of the Hindu worker at t (\u03c0t ) is below \u03c0T , then not enough interactionsare left (in expectation) for the Muslim worker\u2019s investment in shifting the beliefs of the Hindu worker tobe worth it.51 eL is then the best response in that period.The Hindu worker\u2019s belief at time t (\u03c0t ) is essentially the state-variable in this Markov equilibrium.The Hindu worker\u2019s action along the equilibrium path is thus eL if in that period\u03c0t < P\u00af and eH otherwise.Additional ImplicationsI now note a few additional implications of this model which are empirically testable.1. On average (during the intervention), Hindus would blame low output on Muslims, Muslims wouldnot blame Hindus. Muslims would invest in shifting Hindu beliefs.I collected data on actual interactions between workers (accusations for contributing low effort,blame etc.) which I use to test this prediction.50\u03c0T is determined by the remaining length of interaction in the game and does not depend on the number of periods thathave already elapsed.51A couple of things are worth mentioning here. First, even though exerting eH might not be worth it at time t , a luckysequence of high output events can change that, such that in some future period it might be worth it. Alternatively, even thougheH might be worth it in some period, a series of bad outcomes can lead to beliefs of the Hindu worker drifting downwardswhereby the Muslim worker may not find it worthwhile to exert high effort anymore in the future.632. If Hindus have had past contact with Muslims, we are more likely to see high output in those mixedteams initially.The idea here is that if Hindus have had enough experience of working with Muslims in the past,such that their initial belief \u03c0 is greater than P\u00af , Hindus and Muslims will coordinate immediatelyon a high output static equilibrium. I use information on pre-randomization teams of individualsas a proxy for past contact with Muslims in order to test this in the data.3. Closer the beliefs of Hindus to P\u00af , the faster (in expectation) is convergence to high output.This is related to the point above. The closer initial beliefs of Hindu workers are to P\u00af , fewer arethe number of periods with eH required from Muslim workers, before the transition to high outputstatic equilibrium is made. This means mixed teams in which Hindu workers have lower priorsat baseline, might not see output differences between mixed and non-mixed HD teams completedissipate during the intervention period.2.10.4 Proof of propositionProposition: There exists an equilibrium in which, for a given remaining interaction length T , there is a\u03c0T \u2264 P\u00af , such that for \u03c0 \u2265 \u03c0T , Muslims will exert eH . If \u03c0 < \u03c0T Muslims exert eL . Along the equilibriumpath, Hindus exert eL when \u03c0< P\u00af and eH otherwise.Proof: Suppose a Hindu and a Muslim worker are working together in a team for periods t = 1, .....,T ,where T is finite but can be arbitrarily large. We assume \u03c0 < P\u00af , whereby the Hindu worker exerts loweffort eL initially. At time period 0, the Muslim worker maximizes expected future payoff. High effort isoptimal in the beginning for the Muslim worker iffV eHk = {\u2211s\u2032\u2208Sk+1Pk (s,eH )+\u00b5k (s\u2032|s, a)V eHk+1(s\u2032)}\u2265 T P eL (2.18)for k = T \u22121, ....,0. Suppose at time 0, (2.18) is true. Then, any other investment path rather than eH atthe beginning (specifically one where the Muslim worker initially exerts eL and then eH ) is sub-optimal.To see this, suppose that this were not the case by contradiction. Then there exists some t1 and t2 suchthat,64(2.19)t1PeLa(H) =eL+ t2P eHa(H) =eL + (T \u2212 t1 \u2212 t2)PeHa(H) =eH\u2265 { \u2211s\u2032\u2208Sk+1Pk (s,eH )+ \u00b5k (s\u2032|s, a)V eHk+1(s\u2032)}k=T\u22121,...,0\u2265 T P eLwhere t1 and t2 respectively denote time periods during which the Muslim worker expects to put loweffort and high effort respectively (while the Hindu worker still has not updated their prior above P\u00af ). Thenotation P ja(H)=k denotes that expected payoff to the Muslim worker in a period he exerts effort j andthe Hindu worker\u2019s action is k. We can similarly split the payoff from exerting high effort and write theinequality as(2.20)t1PeLa(H) =eL+ t2P eHa(H) =eL + (T \u2212 t1 \u2212 t2)PeHa(H) =eH\u2265 t\u02dc1P eHa(H)=eL + (T \u2212 t\u02dc1)PeHa(H)=eH\u2265 T P eLwhere t\u02dc1 denotes the number of periods until which the the Muslim worker expects to exert eH while theHindu worker\u2019s \u03c0 < P\u00af . Re-writing the above we have (and ignoring the last inequality),t1(PeLa(H) =eL\u2212 P eHa(H) =eH )+ t2(PeHa(H) =eL\u2212 P eHa(H) =eH )+ T PeHa(H) =eH\u2265 t\u02dc1(P eHa(H)=eL \u2212 PeHa(H)=eH)+ T P eHa(H)=eH(2.21)Notice that t2 in expectation (at t= 0) must be larger than t\u02dc1. This is because if the Muslim worker startsoff with eL , in expectation it will take longer to shift the prior of the Hindu worker above P\u00af .Now I show that if the belief of the Hindu worker is not too low, then the Muslim worker will exert eH .I split the payoff of the Muslim worker into two parts: before and after (expected) period j , such that forall t \u2264 j , \u03c0t \u2264 P\u00af and \u03c0t > P\u00af for t > j . The Muslim worker will exert eH iff(2.22)t j PeHa(H) =eL+ (T \u2212 t j )P eHa(H) =eH \u2265 T PeLSuppose this is true. Consider the following extreme scenarios and the consequent prior of Hindu work-ers: (1) in each period before j , high output is produced and (2) in each period before j , low output isproduced. The priors in cases (1) and (2) respectively are:(2.23)(1) :\u03c00pj\u22121HL\u03c00pj\u22121HL + (1\u2212 \u03c00)pj\u22121L(2.24)(2) :\u03c00(1\u2212 pHL) j\u22121\u03c00(1\u2212 pHL) j\u22121 + (1\u2212 \u03c00)(1\u2212 pL) j\u2212165(1) and (2) give the lower and upper bound on the beliefs of the Hindu worker about the type of the Mus-lim worker at time j . The expected prior at time period j can therefore be written as a linear combinationof the expressions above. Re-writing, we therefore have,(2.25)\u03c00pj\u22121HL\u03c00pj\u22121HL + (1\u2212 \u03c00)pj\u22121L+ A. \u03c00(1\u2212 pHL)j\u22121\u03c00(1\u2212 pHL) j\u22121 + (1\u2212 \u03c00)(1\u2212 pL) j\u22121(2.26)=\u03c00\u03c00 + (1\u2212 \u03c00)( pLpHL ) j\u22121+ A \u03c00\u03c0+ (1\u2212 \u03c00)( 1\u2212pL1\u2212pHL ) j\u22121where A is a negative constant. In period j we therefore must have(2.27)\u03c00\u03c00 + (1\u2212 \u03c00)( pLpHL ) j\u22121+ A \u03c00\u03c0+ (1\u2212 \u03c00)( 1\u2212pL1\u2212pHL ) j\u22121> P\u00afSince the L.H.S. is increasing in j , while the R.H.S. is fixed, we clearly have a value of j such that inequalityis satisfied. However, it cannot be so large that equation (2.22) is not satisfied.In this case \u03c00 is the starting belief of the Hindu worker. Note that the L.H.S of equation (2.27) isdecreasing in \u03c00, which suggests if \u03c00 is too small a larger j is required. Given T fixed, the smallestvalue of \u03c0 that allows equation (2.22) to be satisfied (i.e. when the equation holds with exact equality)is essentially the threshold value \u03c0T such that if \u03c00 \u2265 \u03c0T , then the Muslim worker exerts eH in period 0.Note that this threshold is updated every period based on the number of interactions that remain.A Hindu worker simply operates on their prior \u03c0t (state variable) in each period in this Markov equi-librium. If \u03c0t > P\u00af , then Hindus exert eH and eL otherwise. Both actions are best responses given priors.66Chapter 3Economic Consequences of Kinship:Evidence from U.S. Bans on CousinMarriage3.1 Introduction\u201cDespite their capacity to form capital, kinship societies remain poor. To explore the economics of kinshipsocieties is thus to explore the economics of underdevelopment.\u201d (Bates, Greif, and Singh, 2004)The weakening of ties among extended family has, since Weber (1951), been associated with de-velopment. Recent work by Enke (2019) suggests that loose kinship ties became advantageous in theindustrial era, and are linked to urbanization and economic growth. Indeed, Henrich (2020) argues thatloosened kinship ties were key to the historical development of Europe.52 Consistent with this, strongfamily ties have been linked to lower contemporary growth rates through their effect on generalizedtrust, geographic mobility, and female labor force participation (Alesina and Giuliano, 2014). The causalrelationship underlying this link, however, is still unclear. Family ties may react flexibly to changes inincentives rather than being fundamental causes of economic outcomes (Bau, 2021). A prominent the-ory in anthropology holds that the increasing economic role of women is what drives the loosening ofkinship bonds, while sociologists have argued that urbanization dissolves kinship ties.5352See also Schulz, Bahrami-Rad, Beauchamp, and Henrich (2019); Greif and Tabellini (2017); Fukuyama (2011); Korotayev(2000). Notably, the decline of tribes in Europe and the rise of the nuclear family in the late medieval period long preceded theindustrial revolution (Greif, 2006).53See Murdock (1949); Naroll (1970) on \u2018main sequence theory\u2019 in anthropology, and Wirth (1938); T\u00f6nnies (1957); Fischer(1975) on the role of urbanization on kinship ties. Farber (2000) summarizes the latter view using the German proverb \u201ccity airmakes one free\u201d and briefly reviews both literatures. Empirical analysis of this link is complicated by the correlation of strongkinship ties with other historical characteristics, such as disease burdens and type of agriculture, which may directly affect67This chapter uses an exogenous decline in marriage between first cousins to estimate the effect ofweakening kinship ties on income. We do this using US data from the 19th and 20th centuries, wherestate-level bans on first-cousin marriage allow us to identify the causal effect of cousin marriage.54 Whilenow rare in the US, we estimate that 5% of marriages were between first cousins in the first half of the19th century.55 We show that the decline of cousin marriage had direct and meaningful economic conse-quences, including higher income and more schooling. Our results suggest this effect is not driven by thegenetic consequences of cousin marriage. Instead, consistent with the weakening of kinship ties, we finda large increase in rural-to-urban migration.56 Our findings rely on two key contributions: a method forcalculating cousin marriage borrowed from human biology, and an identification strategy that exploitsthe timing of state bans on cousin marriage.Our measure of cousin marriage comes from the excess frequency of marriages where spouses sharea surname. The rate of isonymous (\u201csame-surname\u201d) marriages has been widely used to estimate rates ofcousin marriage in a population (Crow and Mange, 1965).57 This paper is the first use of marital isonymyin economics, and we apply it to a far larger set of marriages than, to our knowledge, has been donein other fields. While this method comes at the cost of substantial measurement error, our procedureadjusts for both false positives (unrelated spouses who share a surname) and false negatives (cousinswho do not share a surname). We apply this method to a dataset of 18 million US marriage records from1800 to 1940. These publicly available records, digitized and transcribed at scale for use by amateurgenealogists, contain the date and place of marriage and the (pre-marital) names of the spouses. Thisallows us to track cousin marriage rates over time by surname. We then link these surname-level ratesof cousin marriage to individual economic outcomes using 1850 to 1940 US Census returns that includefull names.Our causal analysis exploits the timing of state-level bans on cousin marriage. Thirty-two US statesdevelopment. See for example Walker and Bailey (2014); Denic and Nicholls (2007).54Fittingly, the prohibition of marriage between cousins is thought to have been central to the dissolution of clans in Europeand the loosening of kin bonds (Goody, 1983; Schulz et al., 2019).55Among some subsets of the US population, high rates of cousin marriage have persisted until quite recently (Brown, 1951;Reid, 1988; Thomas et al., 1987).56The link between family ties and geographic mobility is highlighted in Alesina et al. (2015); Munshi and Rosenzweig (2016);Greif and Tabellini (2017); Schulz (2019).57We use the terms \u2018cousin marriage,\u2019 \u2018consanguinity\u2019 and \u2018inbreeding\u2019 interchangeably. See Colantonio et al. (2003) for areview of this literature. More recently, DNA analysis has been used to validate results from isonymy, as reviewed in Calafell andLarmuseau (2017).68have banned first-cousin marriage, starting with Kansas in 1858. We restrict our analysis to this set ofstates, and use differences in the timing of bans to identify treatment effects. These bans are unlikely tohave affected all residents equally, and we exploit this to identify the effects of cousin marriage. Specif-ically, surnames with high rates of cousin marriage are assumed to be more exposed to potential statebans. This is reasonable given surnames exhibit strong persistence in cousin marriage rates over time,and hence surnames with initially low rates of cousin marriage are unlikely to have been directly affectedby these bans. Indeed, we find that surnames with high initial rates of cousin marriage see dispropor-tionately large drops in these rates in states with early bans.Our surname-state-level treatment interacts surname-level variation in cousin marriage rates withstate-level variation in the duration of bans on such marriages. That is, we use the interaction of (1) therate of cousin marriage for a surname in the pre-period (1800-1858), and (2) how long a state has had aban on cousin marriage. Rather than compare state-wide outcomes, this allows us to compare a targetedpopulation of high-cousin-marriage families across states with early versus late bans. It also allows forstate-specific fixed effects to control for any confounding state-wide variation. Causal interpretation ofour coefficients rests on a key identifying assumption: the timing of state bans on cousin marriage shouldnot be correlated with factors that affect the relative outcomes of surnames with initially high versus lowrates of cousin marriage. We address the two main threats to identification in the following ways.The first concern is that families with high initial rates of cousin marriage in states with early bansmay be different than those in states with late bans. For example, these families may have been eithermore or less rural, and these differences could have persisted until 1940. We address this concern usingthe 1850 census to estimate baseline outcomes for surname-state cells to control for pre-existing dif-ferences. We also report results from placebo regressions that use 1850 measures as outcomes. Theseregressions directly test for pre-existing differences between high and low cousin marriage surnames instates with early bans on cousin marriage relative to states with late bans.The second threat to identification is that states with earlier bans may have enacted other policiesthat differentially affected families with initially high rates of cousin marriage. For example, the timing ofcompulsory schooling laws is correlated with that of bans on cousin marriage. We address this by includ-ing relevant contemporaneous state-level policies interacted with a surname\u2019s rate of cousin marriage in69the pre-period. If bans on cousin marriage were proxying for these other policies, these additional inter-actions should attenuate their effect.Our first result is that state bans on cousin marriage led to large reductions in measured rates ofcousin marriage. Specifically, the duration of state bans on cousin marriage interacted with a surname\u2019srate of cousin marriage in the pre-period, which serves as our treatment variable, strongly predicts ratesof cousin marriage in the post-period. We find that state bans reduce cousin marriage rates by abouthalf. We confirm this result in an appendix using an entirely different method and a dataset drawn fromgenealogical records. This alternative dataset allows us to identify \u2018true\u2019 cousin marriages, rather than in-fer them from frequencies of same-surname marriages. Both methods find similar magnitudes of cousinmarriage reductions following a ban, which suggests that our isonymy measures, while noisy, are correcton average.Using variation in the extent of a surname\u2019s exposure to a state ban, we find that reductions in cousinmarriage led to higher incomes. That is, we find that state bans on cousin marriage caused dispropor-tionate increases in incomes for men whose surnames had high initial rates of cousin marriage. By 1940,exposure to a ban on cousin marriage led to 4-6% higher income for surnames with high initial ratesof cousin marriage. We also find an increase of 0.2 years of schooling. These magnitudes comparesurnames with initial rates of cousin marriage that are one log point apart. This would represent, forexample, the comparison of surnames with 16% (\u2018high\u2019) cousin marriages to those with 6% (\u2018low\u2019).Crucially, we show that this gap between the 1940 incomes of individuals with differential exposure tocousin marriage bans was absent in 1850, prior to the first ban. This suggests our results are not driven bypre-existing differences. We complement this placebo by showing outcomes for census rounds between1850 and 1940, and show that the income gap between individuals with different levels of exposure tostate bans increases over time in a pattern consistent with our mechanism. That is, relative gains inincome for high-cousin-marriage surnames only appear a few generations after bans start being enacted.A potential explanation for these results comes from the relationship between inbreeding and con-genital health problems. Our findings suggest this channel does not drive the increase in income andschooling. We do not find any evidence that bans on cousin marriage affected rates of institutionaliza-tion due to physical or mental illness.70We then test whether these results are instead caused by weakened kinship ties. The literature onkinship and strong family ties points to two key outcomes we can measure: geographic mobility andfemale labor supply. We find a large increase in rural-to-urban migration. Exposure to cousin marriagebans leads to a 5% increase in the likelihood of living in an urban area for surnames with high initialrates of cousin marriage. However, we do not find any effect on inter-state migration. Bans also leadsto increased labor supply for women, but no change in labor force participation. Unlike in Alesina andGiuliano (2014), however, we do not find effects on the labor supply of young or of elderly men.The rest of the chapter proceeds as follows: Section 2 presents our data and the method we use toestimate rates of cousin marriage. Section 3 describes our empirical strategy, including a discussion ofthe state bans on cousin marriage. Results are in Section 4, and Section 5 concludes.3.2 DataThis section begins with a description of our dataset of marriage records. We then discuss how we use therate of same-surname marriages to calculate rates of cousin marriage across surnames and over time.Finally we briefly discuss the Census data we use for measuring outcomes. Appendix B.1.1 describesgenealogical data which, while not used in our main analysis, validates our use of isonymy (i.e. same-surname unions) to infer cousin marriage rates, as discussed below.3.2.1 Marriage recordsThe marriage records in our dataset come from handwritten documents which have been scanned, tran-scribed and made publicly available online by Family Search (familysearch.org). We retrieved thisdata for all US states between 1800 and 1940. The transcribed marriage records typically include namesof both spouses, and the date and location of marriage. Appendix B.1 includes a scanned image of a sam-ple marriage record, details about what other information these records contain, and our data cleaningprocedure.How good is the coverage of our marriage records? A surprisingly stable benchmark for the US isan annual rate of approximately 10 new marriages per 1000 people (Stevenson and Wolfers, 2007). Ourrecords, averaged annually over the period 1800 to 1940, include about 4 marriages per 1000 people. This71suggests that while our dataset is not comprehensive, it accounts a substantial share of marriages in agiven year.Table 3.1 provides summary statistics of our marriage records. The first column includes all marriagerecords, while the second and third columns include only records either before or after the first US stateban on cousin marriage. While the rate of marriages where the spouses share a surname is low, it is no-ticeably lower in the latter period of our sample. Further, while we provide more nuance below, a roughbenchmark is that the rate of cousin marriage in a population is about four times the rate of isonymy,suggesting cousin marriage rates declined from approximately five percent in the pre-period to aboutthree percent in the post period.3.2.2 Measuring cousin marriage using marriage recordsIn the absence of direct measures of cousin marriage during our period of interest, we use a methodtaken from population genetics to estimate these rates from our dataset of marriages.58 The basic in-sight behind the method is straightforward: First cousins, who share two grandparents, will sometimesalso share a surname. A family where cousins frequently marry will therefore tend to have a higher shareof same-surname (isonymous) marriages than one where they do not. This section describes the formalapplication of isonymy to our dataset of marriages, including corrections to account for isonymous mar-riages between unrelated individuals, and marriages between cousins that are not isonymous \u2013 that is,both false positives and false negatives.The use of surnames at marriage to estimate rates of cousin marriage was first proposed by Darwin(1875). Crow and Mange (1965) formalized this approach and showed that the rate of inbreeding in ahuman population can in some cases be derived from marriage records. That seminal paper spurred alarge literature applying their technique to various populations. (Lasker 1985 and Colantonio et al. 2003review this literature. For examples of marital isonymy applied to US populations see Swedlund andBoyce 1983; Jorde 1989; Relethford 2017.) The link between isonymy and inbreeding has more recentlybeen bolstered by studies which combine surnames with DNA results (Sykes and Irven, 2000; Gymrek58The only dataset we know of with direct measures of consanguinity is Familinx (Kaplanis et al., 2018), which is derived fromonline genealogies. However, as we describe in Appendix B.1.1, it is anonymized and hence cannot be used for our main anal-ysis, which requires surname-level variation. It is useful, however, in allowing us to perform a number of validation exercises.72et al., 2013; Calafell and Larmuseau, 2017).Some isonymous marriages are between unrelated people who happen to share a surname. That is,not all Smiths are cousins. To deal with this, we make use of Crow and Mange (1965)\u2019s decompositionof total isonymy into its random and nonrandom components. Total or observed isonymy P is simplythe fraction of marriages where spouses share a surname. (Throughout this paper, we refer to the pre-marital, or \u2018maiden\u2019, surnames of marriage partners. Once married, almost all couples in our settingshare a surname, which is uninformative.) Random isonymy P r is defined as the share of marriages wewould expect to be isonymous in a population if individuals chose their partners at random. This rate isderived solely from the distribution of surnames in a pool of marriage partners. As per Crow and Mange(1965), random isonymy in a set of marriages is defined asP r =\u2211snms \u00d7n fs ,where nms and nfs are the shares of males and females, respectively, with surname s. In our case, weuse the surname-level rate of random isonymy, which is essentially a measure of how common thatsurname is in the population. Total, or observed, isonymy can then be decomposed into its random andnonrandom components as follows:P = P r +P n \u2212P r P n .Nonrandom isonymy P n is thus the excess share of isonymous marriages \u2013 deviation from the rate wewould expect if individuals were marrying at random. We use nonrandom isonymy to calculate cousinmarriage rates since, in expectation, it nets out marriages between unrelated partners who happen toshare a surname. Nonrandom isonymy, then, adjusts for false positives in calculating cousin marriagerates from isonymy.Likewise, not all cousin marriages are isonymous. An individual\u2019s first cousins can be divided intofour types, which are labeled as the offspring of either their (1) father\u2019s brother, (2) father\u2019s sister, (3)mother\u2019s brother, or (4) mother\u2019s sister. In a patrilineal society, where children take the surname of theirfather, only marriages between the first type leads to isonymy.59 This is illustrated in Appendix figure59Second cousins and more distant relations may also, of course, share a surname. One of the contributions of Crow andMange (1965) is to show that the degree of inbreeding between two marriage partners is proportional to their probability of73B.3. In the second type, for example, the father passes down his surname but his sister\u2019s children taketheir father\u2019s name. If all four types are equally likely, one quarter of cousin marriages will be isony-mous. Hence, a first approximation of the rate of cousin marriage in a population is four times the rateof isonymy. Multiplying the isonymy rate by the correct factor, then, adjusts for false negatives in calcu-lating cousin marriage rates from isonymy.The relationship between isonymy and cousin marriage relies on the assumption, alluded to above,that consanguineous relations occur through male and female ancestors in equal proportion. That is,all four types of cousin marriage are equally likely. Globally, this assumption does not always hold, no-tably in societies that distinguish linguistically between types of first cousins. Many Arab societies, forexample, have a preference for marriage between cousins whose fathers are brothers (Korotayev, 2000).However, no such preference seems to have existed in the US at the time, which is consistent with the lackof linguistic distinction in European languages between types of first cousins (Schneider and Homans,1955; Swedlund and Boyce, 1983). We test this in Appendix B.1.1 using genealogical data and find thatthe proportion of each type of cousin marriage is roughly one quarter and shows no secular trend.60 Fur-ther, we use a log transformation of cousin marriage rates in our analysis, which means our results arenot sensitive to linear transformations.These are the steps we take to construct our measures of cousin marriage for a surname s. We beginby selecting a location and time period under consideration, for example Tennessee from 1859 to 1940.Within this setting, let N be the total number of individuals (such that the number of marriages is N \/2)and Ns be the number of individuals with surname s. N ms and Nfs denote the number of males andfemales with surname s. We drop a surname from our analysis if N ms or Nfs is less than 50, as we deemthese samples too small to provide usable estimates of isonymy. Otherwise, perform the following steps:Step 1: Observed isonymy Ps1. Define Nss as the number of individuals with surname s whose marriage partner also has surnameisonymy.60Two other relevant assumptions are that naming practices are consistent (a child always receives their father\u2019s surname) andthat illegitimacy, adoption and surname changes are negligible (Crow and Mange, 1965). Following the literature on isonymyin the US, we take the first for granted (see for example Swedlund and Boyce 1983). Illegitimacy and adoption are importantto geneticists, as it creates a mismatch between inherited genes and inherited surnames. In our case, this distinction is unim-portant if children bear the surname of the family that raised them, and hence we do not attempt to correct for them. Surnamechanges were common for Blacks during our period of interest (most did not have inheritable surnames prior to emancipation)and so, partly for this reason, we exclude Blacks from our analysis.74s.2. Calculate the observed isonymy rate for this surname: Ps \u2261Nss\/Ns .Step 2: Random isonymy P rs[resume]Subdivide observations into state-decade marriage pools, where decades are denotedwith subscript d . To simplify notation we use lowercase notation for surname ratios, e.g., nsd \u2261Nsd \/Nd and nksd \u2261 N ksd \/N kd for k = m, f . Calculate random isonymy for each decade pool as fol-lows:P rsd \u2261nmsd nfsd(nmsd +nfsd )\/2\u2261nmsd nfsdnsdThe denominator can be simplified to nsd because by construction there are equal numbers ofmales and females (since the unit of observation is a marriage record). The numerator above is theproduct of the share of males and females with surname s. Notice that if either is zero, randomisonymy is zero. The denominator simply normalizes this product by the share of individuals withsurname s. If a surname is held by an equal numbers of males and females, the formula abovesimplifies to P rsd = nmsd = nfsd . Aggregate these decade marriage pools for each surname, weightingby the number of individuals in each pool:P rs =\u2211dP rsd \u00d7NsdNs.Step 3: Nonrandom isonymy P ns[resume]Calculate nonrandom isonymy using the values of Ps and P rs defined in the precedingsteps:P ns \u2261Ps \u2212P rs1\u2212P rs,which is taken from the following decomposition of observed isonymy, Ps = P rs +P ns \u2212P rs P ns .Step 4: Cousin marriage rate[resume]Finally, we calculate the cousin marriage rate by assuming (as described above) that onequarter of cousin marriages are isonymous. The cousin marriage rate is then four times the non-75random isonymy rate, bounded below by zero:Cousi nM ar rs \u2261max{0,P ns }\u22174.This procedure is slightly different for pre-period isonymy. Since the number of marriage recordsin 1800-1858 is substantially smaller, we calculate country-wide surname measures of cousin marriage.That is, the \u2018setting\u2019 is now all of the US, from 1800 to 1858, rather than doing the above steps state bystate as we do in the post period. The only modification to the steps listed above is in our calculation ofrandom isonymy (Step 2), where we still use a state o and decade d to define a marriage pool. However,we aggregate across state-decade pools in the following way:P rs =\u2211odP rsodNsodNs.We now turn to the application of this method to our specific context, the US between 1800 to 1940.3.2.3 US cousin marriage ratesWe use our dataset of marriage records to measure cousin marriage at the level of a surname or surname-state. For concreteness, Table 3.2 presents marriage data on Wallaces, Wheelers and Greens from Ten-nessee, and the calculation of their isonymy and cousin marriage rates in the post period. Of 648 indi-viduals who appear in the marriage records with the surname Wallace in the post-period, 24 married an-other Wallace. This 3.7% rate of isonymy is much larger than the expected rate of marriages between Wal-laces under random mating, 0.04%. Net of this random component, nonrandom isonymy for Wallacesis 3.67%. Since only one of the four (roughly equiprobable) types of cousin marriage lead to isonymy, wemultiply this by four to reach a cousin marriage rate of 15%. Table 3.2 provides the same statistics forWheelers and Greens of Tennessee, for comparison. Note that in some cases the number of isonymousmarriages observed may be less than predicted by random mating, in which case nonrandom isonymywill be negative. In such cases, we treat the cousin marriage rate as being equal to zero.Random isonymy is the rate of isonymy we would expect if a given group were to marry at random.This requires a decision as to what constitutes a marriage pool or marriage market. That is, if individ-76uals were marrying at random, what is the pool of other individuals they could choose to marry. Thisshould obviously be limited by both time and geography. We subdivide the pre- and the post-periodsinto decade-long segments, and use the decade-state as a marriage pool for the calculation of randomisonymy. Within each of these decade-state marriage pools, we calculate the random isonymy rate foreach surname, as described above. We then take the average random isonymy rate for each surnameacross a period, weighted by the number of observations in each of its two subperiods. This rate of ran-dom isonymy is always positive, and is larger for more common surnames.The use of surnames as a core unit of analysis merits some justification. While it would be ideal tolink individuals through generations using direct family links, we believe that surnames provide a usefulproxy. First, there are many of them. Our marriages dataset contains 30,000 surnames that appear inmore than 200 marriages. Further, while some surnames are common (Smiths account for about 1% ofthe population), most people hold relatively uncommon names. The top 100 surnames account for only18% of our marriage records.Second, cousin marriage rates for given surnames are highly persistent over time. We show this inFigure 3.1, where we calculate cousin marriage rates for each surname (aggregating across states) in thepre and the post periods, and plot them against each other. That is, surnames with high cousin marriagerates in 1800-1858 also have high rates in 1859-1940. This is reassuring as it suggests that surname-levelrates of isonymy, which we use to estimate cousin marriage, are measuring stable traits. In turn, thestability of cousin marriage rates is consistent with Giuliano and Nunn (2020), who show persistence ofsuch practices over very long periods of time.Finally, recent work using DNA sequencing finds that surnames are highly predictive of shared ances-try. Starting with Sykes and Irven (2000), a number of studies have found that Y-chromosome sequencesare strongly correlated amongst males who share a surname. Indeed, Gymrek et al. (2013) show that thelinking of Y-chromosome sequences to surnames is so reliable that anonymous publicly available DNAsequences can often be linked to specific individuals. Calafell and Larmuseau (2017) provide a review ofthis literature. One consistent finding is that this genetic link is weaker for the most common names (e.g.Smith), which is taken as evidence of these names having multiple independent origins. This would bethe case if unrelated males independently took the name Smith, in this case as a marker of their profes-77sion. This is in part why we use non-random isonymy, rather than observed isonymy, as our principalmeasure of cousin marriage prevalence.613.2.4 Census dataData on individual outcomes come from the 1850 to 1940 restricted complete count US Census fromIPUMS (Ruggles et al., 2015). We use data on income, education, location of residence, migration andlabor supply. Appendix B.1.4 provides a complete list of the outcome variables used in our analysis andtheir definitions.We link an individual\u2019s census outcomes to a surname-state rate of cousin marriage. For most of ouranalysis, we use their father\u2019s state of birth, rather than their current (e.g. 1940) state of residence, toaccount for potential inter-state migration.62 Doing so excludes anyone from our sample whose fatherwas born outside the US. This is useful since the link between immigrants and pre-period rates of cousin-marriage is tenuous. We also restrict our sample to Whites, since many Blacks took on formal surnamesonly after the Civil War (Byers, 1995; Litwack, 1979) and hence we cannot use surnames to link 1940Blacks to their historical marriage patterns. We now turn to a description of our empirical analysis, whichlinks our measures of cousin marriage from marital records to these census outcomes.3.3 AnalysisWe combine our measure of cousin marriage with exogenous variation in the propensity to marry firstcousins to estimate a causal effect on economic outcomes. This exogenous variation comes from a seriesof state bans on first-cousin marriage, enacted from 1858 onward. We start this section by introducingthese state bans, after which we describe our empirical strategy that exploits this policy variation.61Our results are robust to the exclusion of common surnames, as mentioned in section 3.4.62The 1940 census only asked for father\u2019s state of birth for a random 5% of the population, which reduces our usable sampleconsiderably. Prior census rounds ask for father\u2019s state of birth for the entire population, though these contain fewer usefuloutcomes (no wage data, and no grades of schooling).783.3.1 State bansThirty two US states have enacted legislation banning first-cousin marriage, starting with Kansas in 1858.Table 3.3 lists each US state and the year in which it enacted a ban on first-cousin marriage, if ever.63There is wide variation in the timing of bans. Kansas was joined by eight states in the 1860s, two in the1870s, 1880s and 1890s, six in the 1900s, five in the 1910s, and six thereafter. Table 3.3 also reports thenumber of years cousin marriage had been banned as of 1940, the last year of our analysis.The US is unique with respect to this type of legislation: It is the only member of the OECD to restrictfirst-cousin marriage, and the only country globally with sub-national bans (Bittles, 2012). Why did theUS ban cousin marriage while Europe and its other offshoots did not? And what explains the state-levelvariation that we use for causal identification? Paul and Spencer (2016) summarize their conclusionon these questions: \u201cIn short, it would seem that laws against cousin marriage are explained by thesame factors as legislation permitting compulsory sterilization: relatively poor and powerless targets, anincreasingly pessimistic view of heredity, a new willingness to regulate on behalf of the public\u2019s health,and a decentralized political system easily swayed by highly motivated activists.\u201dIndeed, in the most sustained treatment of the topic, Ottenheimer (1996) argues that US attitudesturned so decisively against cousin marriage in the 19th century due largely to a growing belief in itsnegative health consequences. Much of this, he argues, was due to sensationalist news articles or studiessuch as the Bemiss Report (Bemiss, 1858) which exaggerated the health risks of cousin marriage. The UKand much of Europe, however, saw attitudes towards cousin marriage change around the same period.The more pronounced shift in the US, according to Ottenheimer (1996), was due in part to the influenceof theories of civilizational progress which saw family structures of Native American tribes as evidencethat cousin marriage was a form of backwardness (Morgan, 1877; Ottenheimer, 1990). Further, the asso-ciation of cousin marriage with royalty in Europe may have dampened legislative zeal in prohibiting itthere (Paul and Spencer, 2016).While these accounts may explain the general change of attitudes, they do little to explain legislative63While our analysis does not differentiate between types of bans, there are some differences in their details across states. Forexample, Indiana allows first cousins to marry if they are both above 65. Illinois allows them to marry if they are both above 50or either is sterile. See Paul and Spencer (2016) for more details on these bans, and for references to the specific legal statutesby which they were enacted. See also Bratt (1984) for a discussion of these bans from a legal perspective. We do not know ofsystematic data on enforcement of these bans. However, Figure B.7 presents historical news articles that illustrate at least someenforcement.79variation within the US. Some complementary accounts, in contrast, do address state-level variation.The first, by Farber (1968), suggests that the greater individualism and heterogeneous ethnic origins ofsettlers in the Midwest and West led them to more forcefully oppose first-cousin marriages as a meansof assimilation. Ottenheimer (1996), in return, argues that a parsimonious theory fits the data better:Widespread national change in attitudes towards first-cousin marriage only took legal shape when newmarriage laws were drafted as states joined the Union. Older states, therefore, were less likely to amendtheir long standing marriage statutes. Finally, Yamin (2009) argues that activists and lawmakers pushedin some places to extend the reach of the state with an aim to reshape families. This movement, whichreached its peak in the Progressive Era, likewise led states to introduce compulsory schooling, child laborlaws and compulsory sterilization.We find some support for these theories in predicting which states ban cousin marriage. For example,states that entered the union later are more likely to have enacted a ban: of states that achieved statehoodprior to 1850, 53% eventually enacted a ban, compared to 80% of those who entered afterwards. In con-trast, conditional on having ever banned cousin marriage, the state characteristics discussed above donot significantly predict the timing of these bans. We conduct simple empirical tests of these proposedexplanations in Appendix B.1.5, by testing whether the following characteristics predict the timing ofcousin marriage bans: year of statehood, year of compulsory school, and share foreign born in 1850. Wealso test for the proportion of population which was urban in 1850, the literacy rate, and measures ofreligious composition. We also test whether the timing of bans is correlated with state-level prevalenceof cousin marriage. We find that it does not. We further show that the timing of bans is uncorrelated withstate-level trends in cousin marriage rates.Consistent with the relatively weak predictive power of these theories, some historians have em-phasized the haphazard nature of the legislation against cousin marriage. Discussing these bans, Pauland Spencer (2008) highlight \u201cthe ease with which a handful of highly motivated activists\u2013or even oneindividual\u2013can be effective in the decentralized American system, especially when feelings do not runhigh on the other side of an issue. The recent Texas experience, where a state representative quietlytacked an amendment barring first-cousin marriage onto a child protection bill, is a case in point.\u201d (Pauland Spencer, 2008, p. 2628)80However we cannot rule out that systematic differences exist between states that predict their deci-sion of whether and when to ban first-cousin marriage. To deal with some of this potential confoundingvariation, our identification strategy focuses exclusively on differences in the timing of these bans Thatis, we exclude states that never banned cousin marriage from our analysis.64What if bans were enacted earlier or later in states that were more individualistic and ethnically di-verse, more recently settled, or more concerned with legislating the health of families? Firstly, all of ourregressions include state fixed effects. This deals with the most obvious concerns related to the selec-tion of states into enacting a cousin marriage ban. However, bias may arise if the state characteristicscorrelated with such bans also have a differential effect on surnames with high rates of cousin marriage.This could be the case, for example, if people with these surnames lived in more remote areas, and statesthat passed cousin marriage bans were more likely to impose compulsory schooling laws which mayhave had a disproportionate effect on this population. After presenting our main results, we show thatthese state characteristics do not drive our results. We now turn to our empirical strategy, which exploitsvariation in the timing of state bans.3.3.2 Empirical specificationThe goal of this analysis is to study the causal effect of group-level cousin marriage rates on individual-level economic outcomes. To do so, we estimate the effects of cousin marriage bans on rates of cousinmarriage and on economic outcomes. Crucially, we identify surnames with high rates of cousin mar-riage, and treat these as being more exposed to a potential ban. This is justified in part by the high levelof persistence of surname-level cousin marriage rates, as shown in Figure 3.1. Our treatment, then, is atthe surname-state level, and consists of the interaction of two continuous variables. The first measureshow long a ban has been in place in a given state by 1940, and the second is a surname\u2019s rate of cousinmarriage prior to the first ban. Our baseline specification is the following:Yi sor =\u03c0[Y r sB ano \u00d7 ln(Cousi nM ar r pr es )]+\u03b4Xi +\u03c1s +\u03c1o +\u03c1r +\u03c8i sor , (3.1)64As we discuss in section 3.4, our main results hold when we also include states that never instituted a ban.81where i denotes an individual, s denotes surname, o denotes father\u2019s birth (\u2018origin\u2019) state, and r denotescurrent state of residence. Yi sor denotes an outcome of interest. Xi are controls for a quadratic functionof age, while \u03b1s ,\u03b1o and \u03b1r are surname, state of origin, and state of residence fixed effects, respectively.We cluster standard errors at the surname-state (origin) level. Our results are robust to clustering stan-dard errors at the state level instead.For each individual, Y r sB ano \u00d7 ln(Cousi nM ar r pr es ) is the interaction between (a) the fraction ofyears between 1858 and 1940 that cousin marriage was banned in their father\u2019s birth state o as per table3.3, and (b) pre-period cousin marriage rates for their surname s. For example, consider a \u201cJohn Bailey\u201din 1940 whose father was born in Pennsylvania. Pennsylvania banned cousin marriage in 1902, and theBailey rate of cousin marriage from 1800-1858 is 8.7%. The treatment value for this person then would be0.46\u00d7 ln(0.087), where 0.46 is the fraction of years between 1858 and 1940 where Pennsylvania bannedcousin marriage.The uninteracted main effects Y r sB ano and ln(Cousi nM ar rpr es ) do not appear in (3.1) becauseof the inclusion of state of origin and surname fixed effects, \u03c1o and \u03c1s . That is, we control flexibly forany state-level differences, including any that may be correlated with the timing of bans. Similarly, thiscontrols for any differences across surnames that are correlated with their rates of cousin marriage. Ouridentifying assumption is that the timing of state bans on cousin marriage is not correlated with factorsthat affect the relative outcomes of surnames with high versus low rates of 1800-1858 cousin marriage.This would be violated if, for example, states which banned cousin marriage early also enacted otherpolicies which differentially benefited families that had high rates of cousin marriage in the pre-period.We directly test for this by including interactions of state characteristics with pre-period cousin marriagerates.A number of choices in the specification above merit further discussion. We start with our choice ofpre and post periods. The pre period starts in 1800, the first year for which we have marriage records,and ends in 1858, the year Kansas enacted the first state ban on first-cousin marriage. The post periodends in 1940, the last year for which we have census outcomes. We aggregate marriage records over suchlong periods in part because most surname-state cells have few marriage observations per year. Gettingreasonably precise estimates of cousin marriage using marital isonymy requires a sample with many82marriages. These long time-scales are further justified because of the potentially long-lasting effects ofcousin marriage. A child of parents who are cousins may pass on a strong family-orientation to their ownchildren. Attachment to kin is highly persistent within societies and changes slowly, over generations(Giuliano and Nunn, 2020). It is also likely that the bans will not immediately affect economic outcomes.It will initially affect the choice of marriage partners, which will eventually influence decisions of whereto live, how much schooling to acquire, and what occupation to pursue.Another key specification choice is how we measure cousin marriage rates. Following the cross-country (or cross-region) literature on the effects of cousin marriage (Schulz et al., 2019; Schulz, 2019;Henrich, 2020), we use the logarithm of the rate of cousin marriage to account for the presumed non-linearity in its effects.65 However, the log transformation emphasizes small differences across surnameswith rates of cousin marriage near zero. This is problematic because the number of marriages we useto calculate isonymy rates for most surnames does not allow us to statistically distinguish low rates ofcousin marriage from zero.66 Further, surnames with fewer same-surname marriages than expectedgiven random mating have a measured rate of cousin marriage of exactly zero. To avoid dropping thesesurnames and to attenuate some of the noise, we censor our cousin marriage rates from below. Specifi-cally we use rates of cousin marriage where we take the log of max{\u03b5,P ns }, rather than max{0,Pns }, whereP ns is the rate of non-random isonymy (excess rate of same-surname marriages) for surname s. In ourbaseline specification, we set \u03b5 = 0.015 and consider alternative values in our robustness checks. Thistransformation allows us to focus on variation along the range of values for which we can distinguishcousin marriage from noise. We also show our results are robust to simply using the level of cousin mar-riage rather than the log, and therefore avoid this censoring procedure altogether. We now turn to theapplication of the empirical strategy described in this section to our data.65Henrich (2020), for example, writes that \u201cthe impact, on both the social world and people\u2019s psychology, of increasing theprevalence of cousin marriage from zero to 10% is much bigger than the effect created by increasing it by the exact sameamount, from 40% to 50%.\u201d66We show in appendix B.1.6 that non-random isonymy values below 0.015 are typically statistically indistinguishable from 0.833.4 ResultsThis section begins by showing that our treatment variable, which exploits state-level variation in thetiming of cousin marriage bans, is a strong predictor of cousin marriage rates from 1859-1940. That is,the bans did reduce rates of cousin marriage, in proportion to how long they were in place during thisperiod. This is followed by our main result: bans on cousin marriage led to higher incomes and schoolingin 1940 for individuals whose surnames were exposed to these bans.We then explore mechanisms behind this finding, starting with the health effects of cousin marriage.While we have limited ability to measure health outcomes, our results suggest these do not drive ourmain results. We then study whether this increase in income is caused by a loosening of kinship bonds.While we cannot test for this directly, we test for prominent outcomes from the literature on kinshipand strong family ties. In a review, Alesina and Giuliano (2014) highlight the following effects of strongfamily ties: lower labor force participation of women, youth and the elderly; lower rates of geographicmobility and urbanization; less trust; lower political participation; and higher self-reported happinessand health. Farber (2000), reviewing the sociology and anthropology literature on kinship systems, simi-larly emphasizes the link between kinship ties and urbanization, geographic mobility and the economicrole of women in society. Of these, our data allow us to test the effects of declining cousin marriage onlabor supply, as well as geographic mobility (including the decision to move to an urban centre). Wefind strong evidence in support of the hypothesis that reductions in cousin marriage encourage urban-ization, no evidence for a change in inter-state migration, and some evidence of a modest increase infemale economic activity.3.4.1 Effect of bans on cousin marriage ratesOur first result is to show that bans on first-cousin marriage did decrease rates of cousin marriage asmeasured using our marriages dataset. Specifically, we find that surnames with higher rates of isonymyin the pre-period (1800-1858) see a disproportionate fall in isonymy in the post-period (1859-1940) instates with early bans.Table 3.4 presents these results. Our treatment variable, the state-level years of cousin marriage baninteracted with surname-level pre-period cousin marriage, has a strong negative impact on cousin mar-84riage in the post-period. Column 1 presents results using the censored log transformation of cousinmarriage, while column 2 presents the raw rate of cousin marriage. To interpret magnitudes, comparecousin marriage rates across early and late ban states for a relatively \u2018exposed\u2019 surname\u2013that is, one witha high initial rate of cousin marriage. For a surname with a 10% rate of cousin marriage from 1800-1858,banning in 1858 versus 1940 leads to a reduction of cousin marriage of 2.3 percentage points from 1859-1940. For a surname with the mean rate of cousin marriage in the pre-period (approximately 5%), thedecline would be just over one percentage point, or half the mean rate of cousin marriage in the post-period.Our specification models the effect of a cousin marriage ban as being linear in years. This is reason-able if, each year, marriages are simply affected by whether a ban is in place that year or not. However,if for example enforcement increases gradually, the relationship may not be linear. We present nonpara-metric results in Appendix Table B.6, where we divide the post-period into five sixteen-year bins. Weshow that the effect of bans in reducing cousin marriage increases monotonically in their duration.Further, we show that the finding that cousin marriage bans were effective in reducing rates of cousinmarriage does not depend on our method for calculating cousin marriage rates or on our empirical strat-egy. Appendix B.1.1 replicates this result using an entirely distinct dataset derived from genealogicalrecords to directly identify cousin marriages, rather than inferring them from same-surname marriagerecords.67 Any potential problems with this alternative dataset should be orthogonal to the potential is-sues of measuring cousin marriage using isonymy in marriage records.68 That dataset, since it does notinclude surnames, does not lend itself to our surname-specific analysis. Instead, we create a state-yearpanel of cousin marriage rates, and identify the effect of a state ban on cousin marriage after controllingfor state and year effects. This analysis suggests that cousin marriage rates fall by about half in state-yearswith a ban on cousin marriage, which closely matches the magnitude of results from our main empiricalstrategy.67Data is from Kaplanis et al. (2018), downloadable at familinx.org68Specifically, one potential issue is that bans disproportionately affected marriages between cousins that share a surname,which would lead us to overstate the reduction in cousin marriage. We show in Appendix B.1.3 that this was not the case.853.4.2 Income and schoolingWe use surname-state variation in exposure to cousin marriage bans to study their impact on incomeand schooling. Our most striking result is that exposure to bans on cousin marriage leads to higherincomes. Table 3.5 presents results for two measures of 1940 income: individual wage earnings, andimputed income based on occupation.69Cousin marriage bans lead to substantial increases in both measures, as shown in columns 1-4 ofTable 3.5. Here, we regress income on our treatment variable, as well as surname, state of origin and stateof residence fixed effects, and a quadratic control for age. We restrict our analysis to Whites whose fatherswere born in the US, since it is only for these individuals that surnames can reasonably be linked to pre-period marriage records. We restrict to males in most specifications because their surname lineage isidentifiable both pre and post-marriage. We also restrict our sample to the prime working ages of 18-50.Columns 1 and 3 present results from our basic specification. We find that state bans on cousinmarriage caused disproportionate increases in incomes for men whose surnames had high initial rates ofcousin marriage. By 1940, exposure to a ban on cousin marriage led to 4-6% higher income for surnameswith high initial rates of cousin marriage. This magnitude, as with the ones below, compares surnameswith initial rates of cousin marriage that are one log point apart. This would represent, for example, thecomparison of surnames with 16% (\u2018high\u2019) cousin marriages to those with 6% (\u2018low\u2019).In Columns 2 and 4 we also include surname-state level pre-treatment controls to account for poten-tial pre-existing differences in outcomes. Specifically, we use two variables that are available in the 1850census: (1) imputed income (log occupational income) and (2) a measure of urbanization (the log of thepopulation size of an individual\u2019s place of residence). While both predict 1940 income, coefficients onthe treatment variable are almost unchanged.Similarly, schooling is measured using two 1940 outcomes: an individual\u2019s highest grade completed,and a binary variable for whether an individual is currently attending school. Since the latter is primarilyinformative for individuals who are of secondary school age, we restrict that sample to 12-18 year-olds.69The 1940 census offers a better measure of income than preceding censuses, since for the first time individuals were askednot only for their occupation but also for their wage income. Non-wage income (for example from a family business or farmoutput), however, was captured only by asking whether the respondent received more than $50 of non-wage income in the pastyear. Occupational income is a measure generated by the Census Bureau to allow for measures of income where these are notavailable. These variables are described in more detail in Appendix B.1.4.86Results from columns 5-8 show that bans on cousin marriage increased schooling. As above, magnitudescan be interpreted as follows: banning cousin marriage led to 0.25 additional years of schooling for sur-names with high initial rates of cousin marriage. The probability of being in school (for 12-18 year-olds)in 1940 increases by 1.7 percentage points (column 7), though this effect is only marginally significant.An important concern with the results above is that the relative outcomes of males with high-cousin-marriage surnames may have been different in states with early bans even in the absence of these bans.For example, cousin marriage may have been a less rural phenomenon in states with early bans, whichcould bias our findings. To address this concern, we test for pre-existing differences between high andlow cousin marriage surnames that are correlated with the timing of state bans.We do this in Table 3.6 using measures of income, schooling and urbanization that are available inthe US census from 1850 to 1940.70 Since the first ban was passed in 1858, we should expect the effectof the bans to only show up gradually over the census years. Reassuringly, we find the effects to be small(and statistically insignificant) in the 1850 census when no bans had yet been enacted. They gradually getlarger in magnitude over the next census rounds, with the effects being statistically significant startingin 1920, at which time three quarters of the potential treatment period (1859-1940) had gone by. Theseresults suggest that our results using 1940 census outcomes are driven by the causal impact of cousinmarriage bans, which gradually change individual-level outcomes as the treatment period elapses.3.4.3 Congenital health effectsOne possible explanation for the positive effects of a reduction in cousin marriage on income and school-ing is that they are due not to the cultural shift engendered by a change in family structure, but ratherdue to the direct genetic effects of a reduction in consanguinity.A substantial literature has studied the effects of inbreeding on child development due to the ex-pression of recessive genes. However, evidence on the magnitude of these effects is mixed. Saggar andBittles (2008) review this literature and conclude that inbreeding is associated with modestly higher riskof neonatal and post-neonatal mortality. A recent paper by Mete et al. (2020) finds that in Pakistan, chil-dren born into consanguineous unions tend to be stunted and have lower cognitive scores. This litera-70We show results for every other decennial census round. The 1890 census records were destroyed in a fire, hence the some-what irregular pattern of census rounds.87ture, however, almost universally relies on correlations of inbreeding with health outcomes, with limitedability to control for factors which might be correlated with consanguinity. Mobarak et al. (2019) providea more causal analysis using an instrument derived from the number of opposite-sex cousins availableat age of marriage. They find far more modest results and argue that previous observational estimatesare upwardly biased.To the extent that inbreeding does lead to worse health outcomes and cognitive deficits, some of theeffects of cousin marriage on economic outcomes could come through this channel. We test this usingcensus data on whether an individual lives in a long-term care facility such as a hospital, mental institu-tion or home for the physically handicapped. The results are presented in table 3.7. For consistency, weprovide results for 18 to 50-year-old males in columns 1-2, though we also report results for all Whites incolumn 3. In columns 4-6 we present similar results using the 1930 census instead of the 1940 census.The rate of institutionalization in the 1930 census is over three times larger, which may provide morepower in detecting an effect.71We do not find any evidence that cousin marriage bans reduced the probability of either being hospi-talized or of being admitted to a mental institution. While these outcomes are coarse measures of healthor cognitive ability, they provide some evidence that our results on the effects of cousin marriage on eco-nomic outcomes are not driven by biological channels. Moreover, our results here are consistent withmore recent studies that have tried to establish a causal relationship between consanguinity and healthand find small or no effects.We now turn to outcomes which are linked to another channel by which reductions in cousin mar-riage may have led to higher income: the weakening of kinship ties. Specifically, as described above, westudy the effects on labor supply, urbanization and geographic mobility.3.4.4 Labor supplyAn important channel through which the strength of kinship bonds has been linked to economic out-comes is through changes in female labor supply. We study this both along the intensive and extensive71It is not clear why the rate is lower in 1940 than 1930. Deinstitutionalization, the widespread closure of mental asylums,had not yet begun in 1940. The change may derive from differences in how particular institutions were classified across censusrounds.88margin: the number of weeks worked in the past year, and an indicator for having worked one or moreweeks. We present these results for men as well as women. There is no reason to believe that cousinmarriage would affect the labor supply decision of men in general, though Alesina and Giuliano (2014)find that stronger family ties are also correlated with lower labor force participation of the young andelderly. We use labor supply decisions of men aged between 14-18 and those above 51 along with ourmain sample of those between 18-50 to formally test for this.Interpreting results for women in our sample requires some clarification. Most of our regressionsuse outcomes only for men since their surnames can be linked back to their father, paternal grandfather,and so forth. The same is true for unmarried women. Married women, however, do not report theirpre-marital surnames in the census, making it impossible to trace their ancestors. Married women aretherefore linked to their husband\u2019s surname and husband\u2019s father\u2019s state of birth. For married women,then, the treatment should be interpreted as coming through their husband. A husband\u2019s family\u2019s rate ofcousin marriage could be linked to his wife\u2019s labor supply decision either through spousal selection (e.g.cultural homophily) or directly through his influence on her labor supply decisions.Columns 2-4 of Table 3.8 suggest that male labor supply is unrelated to rates of cousin marriage. Thisis true for both the extensive and intensive margins as well as for the young and the elderly. The evidencefor women is mixed. Column 1 suggests that, on the extensive margin, cousin marriage does not lead toan increased propensity to supply labor outside the household. Bans on cousin marriage did howeverincrease female labor supply on the intensive margin. Relative to a surname with one log point lowercousin marriage in the pre-period, an early ban leads to almost 1 additional week of work, from a meanof 15. These results come with the caveat that our ability to measure effects for women is less direct thanfor men, as discussed above.3.4.5 Geographic mobility and urbanizationAnother outcome linked in the literature to the strength of kinship bonds is the choice of where to live. AsAlesina et al. (2015) emphasize, strong family ties make moving away from home more costly. We studytwo sets of outcomes related to this decision which the census captures: the decision of whether to livein an urban area, and the decision to migrate across state lines.89Urbanization is measured firstly using a dummy variable for whether an individual in 1940 is codedas living in an urban, rather than a rural, location.72 Second, we use another dummy variable to denoteif an individual reported to be living on a farm. Third, we use a continuous measure of urbanization:the log of the population size of one\u2019s location of residence. Columns 1-6 of Table 3.9 show that ourtreatment variable strongly predicts increases in urbanization across all the three measures describedabove. That is, early bans on cousin marriage lead to disproportionately high likelihoods of urbanizationfor surnames with high initial rates of cousin marriage. Exposure to a ban leads to a 4.8 percentage pointincrease in urbanization, a 4 percentage points decrease in the probability of living on a farm, and a30 percent increase in the population size of one\u2019s locality of residence. These effects are substantial inmagnitude and may explain part of the increase in income from a reduction in cousin marriage.In columns 7-10, we test for increased inter-state migration. The coefficients suggest precise nulleffects on both 5-year migration as well as lifetime migration, defined as living outside one\u2019s state ofbirth. Overall, the results in this section suggest that bans on cousin marriage led to greater rural-to-urban migration within states, but no increase in inter-state migration.Why did bans on cousin marriage lead people to be more likely to live in urban areas? One poten-tial explanation is almost mechanical: If a large share of local potential marriage partners are your firstcousins, you may be forced to move to a larger population area to get married. We believe this channelis unlikely to be quantitatively important. Assuming a fertility rate of five (more than double the averagerate for Whites in 1940), a person seeking a marriage partner would have 40 first cousins. Over 99% ofindividuals in 1940 lived in counties with more than 5,000 inhabitants. While the effect of the ban onone\u2019s marriage pool depends on their age, sex and marital status, it seems unlikely that these bans had asubstantial effect on the raw number of potential local marriage partners. Instead, bans on cousin mar-riage, by weakening kinship bonds, may have reduced attachment to a family home and hence reducedthe perceived cost of moving to a nearby town or city to find work, as emphasized in Alesina et al. (2015);Munshi and Rosenzweig (2016); Greif and Tabellini (2017); Schulz (2019).72The Census Bureau considered cities and incorporated places of 2,500 inhabitants or more as urban. It also included otherlocal subdivisions with population of 10,000 and population density above 1000 per square mile. See Appendix B.1.4 for moredetails on this classification.903.4.6 RobustnessOur findings are robust to a wide range of placebos and robustness checks. First, while we believe that thelog of the cousin marriage rate is the appropriate measure for this analysis, we show that our results arenot driven by this transformation. We present our main results using the raw (untransformed) measureof cousin marriage in Table B.7. We confirm that being treated with an early ban on cousin marriage leadsto higher income, more schooling, more urbanization and increased female labor supply. In AppendixB.1.6 we also discuss our choice of \u03b5 threshold when censoring values of isonymy. We justify our choiceof threshold and provide results for alternative values in table B.8.We show that our results are also robust to dropping the most common and the least common sur-names from our sample (table B.9) as well as to the inclusion of all states in our sample, rather than justthose that eventually ban cousin marriage (table B.10). In this specification we treat states that neverbanned cousin marriage akin to those that banned after 1940, i.e., zero years of ban between 1859-1940.Furthermore, we show that our main results are robust to using 1930 census outcomes in table B.11.Next, we take up the discussion from section 3 on the determinants of state bans on cousin marriage.We test whether any of the following act as confounders in our regression results: the timing of state-hood, the degree of ethnic heterogeneity, and the willingness of state legislators to intercede in familydecisions. We measure the first using the number of years elapsed since achieving statehood by 1940, tomirror our treatment of the state bans. Ethnic heterogeneity is proxied using the state share of 1850 cen-sus respondents born outside the US. State legislation in family decisions is proxied using the numberof years elapsed since compulsory high school legislation was enacted by 1940. In each of these speci-fications we interact these state characteristics with our measures of pre-period surname-level cousinmarriage. State fixed effects in all our regressions control for the overall effects of any state charac-teristics. By adding these interactions to our regression specifications we test whether the differentialoutcomes of high-cousin marriage surnames in states that banned cousin marriage are partly driven byother state characteristics. We find no evidence for this \u2013 in each of the three cases our results do notchange substantially in magnitude or significance, as shown in tables B.12 to B.14.913.5 ConclusionThis paper uses 19th and 20th century U.S. state level bans on cousin marriage to provide causal micro-evidence of the impact of consanguineous marriages on a range of economic outcomes. Borrowing amethod from population genetics, we show that excess rates of same-surname marriages can providecredible estimates of cousin marriage rates by surname, by state, and over time. We show that bans onfirst-cousin marriage led to a reduction in the rate of those marriages, and also led to higher incomes,more schooling, rural-to-urban migration and increased female labor supply. These effects do not seemto be driven by the genetic impacts of cousin marriage. Instead, we argue that the economic gains wedocument are driven largely by changes in social relationships that stem from weakened kinship ties.These effects, while striking in magnitude, are consistent with work in anthropology and sociologythat studies the characteristics of strong kinship ties. Henrich (2020), for example, summarizes a largebody of ethnographic and historical research showing that tight (intensive) kinship is associated withgreater cooperation within a kin group, at the cost of geographic and social mobility and participationin anonymous markets and broader impersonal institutions. The results from this paper are consistentwith the view that kinship norms evolve as economic conditions change, but that they do so slowly, overthe course of many generations.While clearly of historical significance, we believe these results may also be relevant for contempo-rary development outcomes, since intensive kinship is still prevalent in many societies. Figure 3.2 showsestimated national contemporary rates of cousin marriage plotted against incomes per capita. Thesedata suggest high rates of cousin marriage in many countries, and a striking cross-country correlationwith development and political institutions (Schulz, 2019; Akbari et al., 2019; Woodley and Bell, 2013).The causal estimates in this paper of the impact of kinship are not directly applicable to such societies,where kinship ties may substitute for weak formal institutions. Nevertheless, our results do suggest thatas economies undergo structural transformation, leading to the development of better institutions, therecould be high returns from family structure transitions that weaken kinship ties.In future work, we plan to study the effect of cousin marriage on household formation and familystructure. A substantial literature has studied the gradual emergence of the \u201cEuropean Marriage Pattern\u201d(Hajnal, 1965) and whether this set of practices (notably late marriage and nuclear neolocal households)92was central to the economic success of Europe (e.g. Dennison and Ogilvie, 2014). We plan to test whetherthe decline of cousin marriage made this family structure more common, and its link to changes in mi-gration and human capital acquisition. Using street addresses on census returns, we also intend to studythe relationship between kinship tightness and geographical clustering. Do brothers migrating to cities,for example, tend to live near each other? Finally, does a decline in cousin marriage lead to fewer sonstaking on their father\u2019s first name? If we do observe fewer \u201cJr\u2019s,\u201d that suggests these naming practices canserve as easily-observed proxies of kinship in America (Taylor, 1974).3.6 Tables and figures3.6.1 TablesTable 3.1: Summary statistics: Marriage records1.2All marriage records Prior to first ban Post first ban(1800-1940) (1800-1858) (1859-1940)Number of marriages 17.73 million 3.45 million 14.28 millionIsonymous (same-surname) 0.0085 0.0120 0.0075Table 3.2: Calculating cousin marriage rates from isonymy, examples from TennesseeSurname Wallace Wheeler Green1859-1940 marriage records (post-period)Individuals with surname 648 4781 1696Married to same surname spouse 24 64 2Observed isonymy Ps 0.0370 0.0134 0.0012Random isonymy P rs 0.0004 0.0035 0.0011Nonrandom isonymy P ns 0.0367 0.0099 0.0001Cousin marriage rate 14.66% 3.97% 0.05%Cousin marriage rates are calculated using the following formula: Cousi nM ar rs = max{P ns ,0}\u00d74.93Table 3.3: Year of enactment of state laws banning first-cousin marriageState YearYears asof 1940State YearYears asof 1940Alabama Never ban - Nebraska 1911 29Arizona 1901 39 Nevada 1861 79Arkansas 1875 65 New Hampshire 1869 71California Never ban - New Jersey Never ban -Colorado 1864 76 New Mexico Never ban -Connecticut Never ban - New York Never ban -Delaware 1921 19 North Carolina Never ban -Florida Never ban - North Dakota 1862 78Georgia Never ban - Ohio 1869 71Idaho 1921 19 Oklahoma 1890 50Illinois 1887 53 Oregon 1893 47Indiana 1877 63 Pennsylvania 1902 38Iowa 1909 31 Rhode Island Never ban -Kansas 1858 82 South Carolina Never ban -Kentucky 1946 0 South Dakota 1862 78Louisiana 1900 40 Tennessee Never ban -Maine 1985 0 Texas 2005 0Maryland Never ban - Utah 1907 33Massachusetts Never ban - Vermont Never ban -Michigan 1903 37 Virginia Never ban -Minnesota 1911 29 Washington 1866 74Mississippi 1923 17 West Virginia 1917 23Missouri 1889 51 Wisconsin 1914 26Montana 1919 21 Wyoming 1869 71Source: Paul and Spencer (2016). \u2018Years as of 1940\u2019 refers to the number of years a state has had a banin place as of 1940. Alaska and Hawaii are omitted since they achieved statehood post-1940. Neitherhas ever banned first-cousin marriage, nor has Washington, D.C.94Table 3.4: Impact of bans on cousin marriage rates(1) (2)Log (CousinMarrpost ) CousinMarrpostYears Ban (Fraction) \u00d7 Log (CousinMarrpr e ) -0.307***(0.0709)Years Ban (Fraction) \u00d7 CousinMarrpr e -0.258***(0.0732)Mean Dep. Var. -2.75 0.0239N 1,207,523 1,207,523Adj. R2 0.450 0.458* p<0.10, ** p<0.05, *** p<0.010. Standard errors clustered at the surname-origin state (father\u2019s birthstate) level in parentheses. All regressions include surname, state-of-origin and state-of-residencefixed effects. Cousin marriage rates are calculated (as described in section 3.2.2) at the surname-level in the pre-period and surname-state level in the post period and linked at the surname-originstate (of father\u2019s birth) level with the 1940 Census records. Years Ban (Fraction) refers to the numberof years each state had a ban on cousin marriage in place by the year 1940, divided by 82, which isthe number of years that had passed since the first ban in Kansas in 1858. Sample includes Whitemales aged 18 to 50 in 1940 unless otherwise specified.95Table 3.5: Impact of cousin marriage bans on income and schoolingLog Wage Income (1940) Log Occupational Income (1940) Highest Grade Completed (1940) In School (1940)(1) (2) (3) (4) (5) (6) (7) (8)Years Ban (Fraction) \u00d7 Log (CousinMarrpr e ) 0.0605** 0.0542** 0.0392*** 0.0337** 0.246*** 0.200** 0.0170* 0.0176(0.0245) (0.0273) (0.0140) (0.0155) (0.0794) (0.0922) (0.00915) (0.0111)Surname-state pre-treatment controlsLog Occupational Income (1850) -0.00483 0.0330*** 0.188*** 0.0134***(0.0170) (0.0122) (0.0540) (0.00511)Log Urbanization (1850) 0.0423*** 0.0344*** 0.108*** 0.00999***(0.00461) (0.00340) (0.0147) (0.00147)Surname F.E. Yes Yes Yes Yes Yes Yes Yes YesState of Origin F.E. Yes Yes Yes Yes Yes Yes Yes YesState of Residence F.E. Yes Yes Yes Yes Yes Yes Yes YesSample White Males (18-50) White Males (18-50) White Males (18-50) White Males (12-18)Mean Dep. Var. 6.13 6.14 2.87 2.88 10.17 10.10 0.790 0.783N 682,847 617,084 976,414 885,324 1,187,725 1,071,133 1,129,743 991,424Adj. R2 0.247 0.244 0.122 0.122 0.120 0.119 0.225 0.229* p<0.10, ** p<0.05, *** p<0.010. Standard errors clustered at the surname-origin state (father\u2019s birth state) level in parentheses. Cousin marriage rates arecalculated (as described in section 3.2.2) at the surname-level in the pre-period and surname-state level in the post period and linked at the surname-originstate (of father\u2019s birth) level with the 1940 Census records. Years Ban (Fraction) refers to the number of years each state had a ban on cousin marriage inplace by the year 1940, divided by 82, which is the number of years that had passed since the first ban in Kansas in 1858. Sample includes White males aged18 to 50 in 1940 unless otherwise specified.96Table 3.6: Income, schooling and urbanization: Placebo regressions from 1850-1940 CensusesCensus 1850 1870 1900 1920 1940Fraction of treatment period (1859-1940) 0% (Placebo) 15% 51% 76% 100%Log Occupational IncomePanel A: IncomeYears Ban (Fraction) \u00d7 Log (CousinMarrpr e ) -0.0023 0.004 0.005 0.0185** 0.0392***(0.0121) (0.0088) (0.0076) (0.0082) (0.0139)Mean Dep. Var. 2.90 2.82 2.86 2.97 2.87N 643,809 1,129,136 1,983,051 2,649,824 976,414In School (12-18 year olds)Panel B: SchoolingYears Ban (Fraction) \u00d7 Log (CousinMarrpr e ) -0.00558 -0.0102 0.0284 0.00682 0.0165*(0.0152) (0.0130) (0.0446) (0.00764) (0.00914)Mean Dep. Var. 0.625 0.630 0.601 0.689 0.789N 337,692 602,610 41,869 1,119,576 1,130,714Log population size of locality of residencePanel C: UrbanizationYears Ban (Fraction) \u00d7 Log (CousinMarrpr e ) 0.0312 0.0489 0.0327 0.0814** 0.303***(0.03402) (0.0320) (0.0379) (0.0409) (0.0733)Mean Dep. Var. 6.59 6.91 7.57 8.28 8.27N 659,536 1,304,994 2,370,685 3,455,349 1,207,523Living on FarmPanel D: FarmYears Ban (Fraction) \u00d7 Log (CousinMarrpr e ) 0.00330 -0.00776 -0.0157** -0.0230*** -0.0388***(0.0127) (0.0100) (0.00782) (0.00697) (0.0113)Mean Dep. Var. 0.580 0.432 0.430 0.370 0.295N 729,480 1,304,979 2,370,685 3,455,349 1,209,997Surname F.E. Yes Yes Yes Yes YesState of Origin F.E. Yes Yes Yes Yes YesState of Residence F.E. Yes Yes Yes Yes Yes* p<0.10, ** p<0.05, *** p<0.010. Standard errors clustered at the surname-origin state level in parentheses.Cousin marriage rates are calculated (as described in section 3.2.2) at the state level in the pre-period andsurname-state level in the post period. These are linked at the surname-state (of own birth) level for censusrecords before 1900 and at the surname-state (of father\u2019s birth) level for records from 1900 onwards. Years Ban(Fraction) refers to the number of years each state had a ban on cousin marriage in place by the year 1940, di-vided by 82, which is the number of years that had passed since the first ban, in 1858. Sample includes Whitemales aged 18 to 50 unless otherwise specified.97Table 3.7: Impact cousin marriage bans on genetic outcomesLiving in Hospital, Mental Institution or Home for Physically Handicapped(1) (2) (3) (4) (5) (6)Years Ban (Fraction) 0.0004 0.0009 0.0001 0.0006 0.0010 0.0004\u00d7 Log (CousinMarrpr e ) (0.000601) (0.000674) (0.000296) (0.000598) (0.000636) (0.000347)Surname F.E. Yes Yes Yes Yes Yes YesState of Origin F.E. Yes Yes Yes Yes Yes YesState of Residence F.E. Yes Yes Yes Yes Yes YesPre-treatment controls (surname-state) No Yes Yes No Yes YesSample White Males (18-50) Whites (All) White Males (18-50) Whites (All)Year 1940 1940 1940 1930 1930 1930Mean Dep. Var. (% of population) 0.1% 0.1% 0.08% 0.37% 0.36% 0.26%N 1,207,523 1,087,102 3,686,601 4,021,199 3,790,663 7,945,497Adj. R2 0.001 0.001 0.002 0.002 0.002 0.002* p<0.10, ** p<0.05, *** p<0.010. Standard errors clustered at the surname-origin state (father\u2019s birth state) level in parentheses. Cousinmarriage rates are calculated (as described in section 3.2.2) at the surname-level in the pre-period and surname-state level in the post periodand linked at the surname-origin state (of father\u2019s birth) level with the 1940 Census records. Years Ban (Fraction) refers to the number ofyears each state had a ban on cousin marriage in place by the year 1940, divided by 82, which is the number of years that had passed sincethe first ban in Kansas in 1858. Surname-state pre-treatment controls include occupational income (logged) and population of locality ofresidence (logged) measured at the surname-state level from the 1850 census records. Sample includes White males aged 18 to 50 in 1940unless otherwise specified.98Table 3.8: Impact of cousin marriage bans on labor supply(1) (2) (3) (4)Sample Female (18-50) Male (18-50) Male (14-18) Male (51+)Panel A: Labor Force ParticipationDep Variable: Weeks worked > 0Years Ban (Fraction) \u00d7 Log (CousinMarrpr e ) 0.0144 -0.00246 -0.00724 0.00879(0.0113) (0.0102) (0.0112) (0.0258)Mean Dep. Var. 0.394 0.724 0.197 0.700N 853,731 1,087,102 701,232 90,637Adj. R2 0.039 0.106 0.127 0.206Panel B: Labor SupplyDep Variable: Number of weeks worked in the past yearYears Ban (Fraction) \u00d7 Log (CousinMarrpr e ) 0.948** 0.280 -0.207 -0.434(0.490) (0.492) (0.390) (1.412)Mean Dep. Var. 14.95 28.56 5.83 31.12N 853,731 1,087,102 701,232 90,637Adj. R2 0.055 0.154 0.108 0.166Surname F.E. Yes Yes Yes YesState of origin F.E. Yes Yes Yes YesState of Residence Yes Yes Yes YesSurname-state pre-treatment controls Yes Yes Yes Yes* p<0.10, ** p<0.05, *** p<0.010. Standard errors clustered at the surname-origin state (father\u2019s birth state)level in parentheses. Cousin marriage rates are calculated (as described in section 3.2.2) at the surname-level in the pre-period and surname-state level in the post period and linked at the surname-origin state (offather\u2019s birth) level with the 1940 Census records. Unmarried women are linked to their father\u2019s state of birthwhile married women to their husband\u2019s father\u2019s state of birth. Years Ban (Fraction) refers to the number ofyears each state had a ban on cousin marriage in place by the year 1940, divided by 82, which is the numberof years that had passed since the first ban in Kansas in 1858. Surname-state pre-treatment controls includeoccupational income (logged) and population of locality of residence (logged) measured at the surname-statelevel from the 1850 census records.99Table 3.9: Impact of cousin marriage bans on urbanizationLiving in Urban Living in Farm Log Urbanization Inter-state migration Inter-state migration5 years Lifetime(1) (2) (3) (4) (5) (6) (7) (8) (9) (10)Years Ban (Fraction) \u00d7 Log (CousinMarrpr e ) 0.0475*** 0.0329** -0.0397*** -0.0396*** 0.303*** 0.239*** -0.00203 -0.00540 0.00505 0.0127(0.0127) (0.0139) (0.0113) (0.0126) (0.0733) (0.0782) (0.00419) (0.00435) (0.00717) (0.00774)Surname F.E. Yes Yes Yes Yes Yes Yes Yes Yes Yes YesState of Origin F.E. Yes Yes Yes Yes Yes Yes Yes Yes Yes YesState of Residence F.E. Yes Yes Yes Yes Yes Yes Yes Yes Yes YesSurname-state pre-treatment controls No Yes No Yes No Yes No Yes No YesMean Dep. Var. 0.446 0.448 0.325 0.324 8.28 8.29 0.047 0.045 0.205 0.196N 1,207,523 1,087,102 1,207,523 1,087,102 1,207,523 1,087,102 1,156,740 1,041,639 1,203,588 1,083,999Adj. R2 0.097 0.101 0.117 0.121 0.132 0.134 0.058 0.059 0.246 0.257* p<0.10, ** p<0.05, *** p<0.010. Standard errors clustered at the surname-origin state (father\u2019s birth state) level in parentheses. Cousin marriage rates arecalculated (as described in section 3.2.2) at the surname-level in the pre-period and surname-state level in the post period and linked at the surname-originstate (of father\u2019s birth) level with the 1940 Census records. Years Ban (Fraction) refers to the number of years each state had a ban on cousin marriage inplace by the year 1940, divided by 82, which is the number of years that had passed since the first ban in Kansas in 1858. Surname-state pre-treatmentcontrols include occupational income (logged) and population of locality of residence (logged) measured at the surname-state level from the 1850 censusrecords. Sample includes White males aged 18 to 50 in 1940 unless otherwise specified.1003.6.2 FiguresFigure 3.1: Persistence in cousin marriage rates by surname0.02.04.06.08Post-period cousin marriage rate (1859-1940)0 .05 .1 .15 .2 .25 .3Pre-period cousin marriage rate (1800-1858)Note: This figure is a binscatter of surname-level rates of isonymy in the pre- and post-period.Figure 3.2: Consanguinity and income (Cross-country correlation)Sources: Data on consanguineous marriages is from consang.net (Bittles 2015). GDP per capita values are from the PennWorld Table 2000. Note: Consanguineous marriages here are defined in this series as marriages between first or second cousins.GDP per capita values are adjusted for purchasing power parity. Both series are displayed on a log scale.101Chapter 4Elections, Accidental Deaths andInsurgency: Recipe for India\u2019s ConflictMinerals4.1 IntroductionNatural resource extraction is often associated with conflict, severe corruption and high rent seeking inmany countries across the world. Unlocking the true potential of these sectors is crucial to propel devel-oping nations into higher growth paths. However, illegal and unsustainable practices due to the absenceand\/or weak enforcement of regulations, coupled with disregard for large sections of the poor directlyaffected by such actions, can often have negative consequences. This could, for example be in the formof environmental degradation and physical displacement of sections of the vulnerable population. Agrowing strand of literature is now studying these topics (see Burgess et al., 2011; Asher and Novosad,2018).A separate literature is motivated by the fact that incumbent politicians may manipulate policies overthe electoral cycle for political gains. While the focus has traditionally been on macroeconomic policiesin mature democracies, it is now shifting to nascent democracies, particularly focusing on electorallysensitive factors typical to countries in early stages of development. For example, Cole (2009) showsthe existence of political cycles in agricultural credit offered by public banks in India \u2013 he finds that theamount of credit offered gradually increases in years leading up to state elections. Bhattacharjee (2014)and Baskaran et al. (2015) also focus on India, and find similar cycles in public health provision and ruralelectrification respectively.102I construct a new state\/district-level dataset from India and bring these two strands of literature to-gether in this chapter. I first document the existence of opportunistic political cycles in mineral licens-ing, mining output and accidents at the state-level. In contrast to much of the existing literature, thecycles exhibit an inverted U-shaped pattern between state assembly elections, with the level of activityminimized in election years. Using district level data, I then examine how these patterns are affected byelectoral competition and local conflict, namely India\u2019s Naxalite insurgency, which is believed to be fu-elled significantly by extortion of mining revenues in mineral rich areas. I find that electoral competitionintensifies mining cycles, with politically competitive districts exhibiting larger reductions in fatalities,but only in election years. A similar pattern is observed in the conflict prone districts. I show that thisis driven by politicians\u2019 objective of minimizing the rebels\u2019 resource base during polls, since the lattersystematically threaten national and state assembly elections with violence. Finally, while average lev-els of violence across mining and non-mining districts within states are not significantly different, I findthat a reduction in mining intensity leads to reduced electoral violence in mining districts relative tonon-mining ones. This suggests strategic behavior on the part of politicians. Politicians do not directlyinfluence small businesses owners, contractors or even poor villagers who the rebels \u201ctax\" (Chakravarti,2014), but with their large scale involvement in the mineral industry in India (Asher and Novosad, 2018),they are able to manipulate activity in a way that suits their electoral agenda.This chapter makes three important contributions. It points to the existence of political cycles inan industry with both private and public organizations, suggesting collusive actions between politiciansand private firms in generating them. Majority of the previous work on political cycles considers policiesdirectly under the purview of either federal or local governments. Secondly, while much of the literatureon Naxalite violence only considers static predictors of conflict such as Scheduled Caste\/Scheduled Tribe(SC\/ST) population proportions,73 land inequality, presence of minerals, etc., this paper sheds light onthe dynamic nature of violence, in a context where realistically, the rebel groups can never achieve theirdeclared objective of overthrowing the Government of India through armed struggle. Such analyses elu-cidate behavioral aspects of rebellion intensity which are more relevant for conflict resolution strategies.Finally, this paper also contributes to the literature on myopic voting in a developing country context.73Scheduled Castes (SC) and Scheduled Tribes (ST) are officially designated groups of historical disadvantage as a result of the caste systemin India.103The fact that politicians respond to electoral competition by attempting to reduce mining fatalities onlyin election years, shows that the poor, who in general are likely to carry greater grievances, neverthelessevaluate the performance of politicians only over a short horizon.The findings of this chapter have important implications for policy aimed at diffusing opportunis-tic cycles in mining fatalities. In addition to my main results, I find mining cycles to be larger in districtswith greater Scheduled Tribe (ST) population and smaller in districts with higher literacy rates. These arenot unexpected results. A large proportion of mine workers belong to the Scheduled Tribes (Srivastava,2005), making mining accidents more electorally sensitive in districts with a large voter base belongingto the same caste. Higher literacy rates are usually associated with the demand for greater political ac-countability and less myopic voting behavior, leading to larger political costs of accidents and deaths ingeneral. In summary, this paper provides important new findings on electorally driven political behaviorin an industry marred with severe corruption in India, analyzes the effect of both fixed and time varyingfactors on such behavior, and also sheds light on the consequences of such behavior.The rest of the chapter is organized in the following manner. Section 4.2 briefly describes the con-textual setting, focusing on the mineral industry in India, the politics around it and also discusses thedevelopment of the Naxalite movement since it\u2019s emergence in 1967. Section 4.3 presents a concep-tual framework discussing the different channels that could generate political business cycles in mining.Section 4.4 describes the sources and construction of the dataset and presents summary statistics of keyvariables. Section 4.5 lays out estimation procedures and presents results from the state-level analysis,which shows the presence of election cycles in different aspects of mining activity over several decades.Section 4.6 is dedicated to the district-level analysis. It studies the effect of electoral competition andNaxalite conflict on the size of mining cycles. It also provides a comparative analysis of electoral cyclesin Naxal violence in mining versus non-mining districts. Robustness checks and caveats follow in section4.7. Finally, section 4.8 concludes.1044.2 Context4.2.1 Politics in IndiaIndia is a federal democracy with its states having considerable power over their own government andpolicies. State legislative bodies are elected every 5 years to carry out administration in the 29 states ofIndia. Every state had its first election in 1952, however for reasons such as coalition breaks, impositionof president\u2019s rule due to loss of confidence in the dispensation, midterm (unscheduled) elections havebeen held in many states leading to de-synchronization of the election cycles. From the point of viewof analyzing the impact of political cycles, this is ideal since it allows for both cross-sectional variationacross states\/districts and temporal variation in the outcomes of interest that can be exploited to addressmy question. Furthermore, midterm elections are often unexpected events, which provides the basis fora natural placebo test; studying whether effects differ across scheduled and unscheduled elections (seeAppendix Figure C.2 for an illustration). State elections are held at the constituency level, whereas thelowest administrative division at which I observe outcome measures are districts. The number of dis-tricts vary significantly across states, however each district on average is comprised of 9 constituencies.Therefore, in order to analyze heterogenous effects (of election cycles) generated by electoral competi-tion, some form of aggregation of constituency level election results up to districts is necessary. This isdiscussed in greater detail in section 4.6.4.2.2 Mining in IndiaMining is a significant economic activity in India, contributing approximately 3% to its GDP (Indian Bu-reau of Mines, 2016) from over 80 different types of minerals. While this might appear to be a smallcontribution as a whole, mining is the major economic activity in mineral rich areas accounting for largeshares of local incomes and generates significant employment. Nevertheless, large scale criminal activ-ity exists in the sector, primarily through collusion between firms and state legislators. Such activitiesinclude: mineral prospections without permits, kickbacks for state legislators in exchange for miningpermits, illegal extraction and violation of environmental and safety regulations. These activities are fa-cilitated to an extent by the structure of the legal regime associated with mining and the role that state105and central governments play in the extraction process. Indian states own all minerals within their geo-graphical boundaries and Members of State Legislative Assemblies (MLAs) have significant control overmajority of permits required before extraction can begin (Mohanty, 2017). While federal clearances arerequired for mining of some selected minerals, states have hold up power over these too. The royaltiesand taxes paid by mining companies go directly to the state and central governments. Furthermore, 7%of all mining leases in 2014 covered 75% of the total mining area, while 67% of leases covered only 8%of the area \u2013 and majority of these smaller areas are leased out to private enterprises (Mohanty, 2017).This is likely to ease collusion between firms and politicians. Indian mines also have an abysmal recordwhen it comes to workplace safety compared to other developing countries such as Brazil and SouthAfrica, making it one of the most dangerous professions in the country. A large proportion of accidentsand deaths are caused by roof\/side wall falls, events that are easily avoidable with better safety practices(Mandal and Sengupta, 2000).4.2.3 Naxal Violence: Origin, development and characteristicsIn this subsection, I offer a brief history of India\u2019s Naxalite conflict, and put forward arguments as towhy violence intensity could be tied to the electoral cycle. I also provide anecdotal evidence on theimportance of mining revenues as a tax base for the rebels.Origin and developmentIndia\u2019s Naxalite (Maoist) movement originated in a small village in rural West Bengal, \u201cNaxalbari\" in 1967,triggered by an attack on a tribal villager by local landlords. Thereafter, it gained momentum with sup-port from key members of the Communist Party of India (Marxist). The period since has been markedby high levels of conflict between separate Naxalite groups, who spread across various states. In 2003,two major factions which promoted the idea of \u201cAllegiance to armed struggle and non-participation inelections\", merged to form the Communist Party of India (Maoist), which significantly intensified lev-els of violence. The popularity and strength of the movement is perceived to stem from underdevel-opment in the affected communities. The Naxals are also believed to be banking on the grievances ofthe tribal population against mining activity, which has resulted in large-scale displacements in Maoist106strongholds (Kujur, 2009). The declared objective of the CPI (Maoist) is to overthrow the governmentof India through protracted armed struggle and establish a liberated zone in the centre of India (Kujur,2008). In 2006, the Naxalite problem was termed by the Indian Prime Minister Manmohan Singh, as the\u201cthe single biggest internal security challenge ever faced by our country\".Indian states have managed to deal with the problem to varying degrees. An outlier is Andhra Pradesh,which has undertaken a combination of effective development policies together with the use of spe-cialised police force to deal with the issue. At the other extreme, some states have also undertaken semi-legal measures to try to curb this problem. A prime example of this is \u201cSalwa Judum\", a militia mobilizedand deployed as part of anti-insurgency operations in Chhattisgarh with the government eager to flushthe area of Naxalites in order to allow smooth operation of the mining companies. \u201cSalwa Judum\" herdedvillagers and tribals into makeshift camps which were rife in human rights violation.74 In July 2011, theSupreme Court of India declared the militia to be illegal and unconstitutional and ordered it to be dis-banded.The Naxal affected areas qualify for multiple sources of central (federal) government funding for de-velopment purposes, such as the National Rural Employment Guarantee Scheme (NREGA) (which is anational scheme), as well as others that are specific only to the affected districts. This shows that theIndian government recognizes that underdevelopment constitutes an important aspect of this conflict.The extent to which state governments are able to use such funds however depends on the political ca-pability and stability of the governments itself (Kujur, 2009). While these measures have reduced thepotency of conflict in recent times, it still remains a significant challenge. Data released by the HomeMinistry in April 2018 reports 90 districts in 11 states to be still affected by the conflict, of which 35 wereidentified as the worst affected.75Relevant characteristicsElection cycles in mining intensity cannot be studied in isolation from the Naxalite conflict for multipledifferent reasons. I discuss important characteristics of the nature of conflict in this section to elucidatethis.74\u201cSalwa Judum victims assured of relief\". The Hindu. Chennai, India. 16 December 2008.75Indian Express. New Delhi, India. 17 April 2018.107First, mineral resources are an important component of the rebels\u2019 tax base in many mineral rich dis-tricts. This has been documented in previous works as well (see Vanden Eynde, 2016). The MaharashtraState Home Minister R.R. Patil in 2010 accused the mining industry of funding the Maoist movement.There are numerous newspaper reports showing anecdotal evidence of this:\u201cWhere there is mining, there is Maoism, because where there is mining, there is more rev-enue, and where there is more revenue, there is more extortion,\u201d he added.\u201cSome of thebest-known names in Indian industry are running businesses in the Maoist areas by payingoff the Maoists. I don\u2019t want to name names, but these are the biggest names in Indian in-dustry.\"(Interview of a local land rights activist in Hejda, Jharkhand, National GeographicMagazine, April 2015).\u201cAround 10 armed members of Jharkhand Prastuti Committee (JPC, Naxal Wing) torchedthree dumpers, damaged an SUV and beat up a guard at a mine of Central Coalfields Lim-ited (CCL) in the small hours today at Charhi, some 32km from the district headquarters,the second such attack in the area within a week. The JPC had been demanding levy fromthe company for some time and the incident seemed to have been orchestrated to mountpressure on authorities.\"(The Telegraph, February 2016).The rebels tax the mining sector in mineral rich districts through violence and mining companies are be-lieved to be susceptible to their demands. Therefore, to the extent that Naxals actively boycott electionsthrough both violent means and civilian collaboration, minimizing the resource base of the rebels mightbe an important consideration for politicians during elections.This brings me to the next important characteristic of the Naxalite violence, boycott of national andstate assembly elections:\u201cAs usual, we have appealed to people to boycott the elections because they are a farce. Elec-tions only renew five-year tenures of loot and torture by the elected representative in thepresent system. Like always, this time too, the government has deployed a huge numberof security forces in the name of conducting free and fair elections, which are already ex-ploiting and torturing people. Attacks on villages in the name of search operations, arrests,beating up people, fake encounters are consistently on. Therefore, I can only say that whenthe government tries to defuse our poll boycott movement through crackdown on the peo-ple, there will be certainly a counter to it\". (CPI Maoist Special Zonal Committee Secretaryto The Times of India, October 2013.)Lastly, the rebel groups at the same time levy harsh punishments on villagers for collaborating with thepolice :108\u201cMaoists killed a middle-aged couple suspecting them of being police informers and dumpedtheir bodies on a road in Madhubanthana area of Giridih district in the small hours of Friday.When villagers woke up in the morning, they found the bodies lying about a hundred metresfrom each other with their throats slit. The deceased have been identified as residents ofBanpura village in Madhubanthana area\". (The Telegraph, May 2018)In summary, mining revenues form an important component of the rebels\u2019 tax base in mineral rich areas,and they systematically appeal for the boycott of elections to civilians. The government on the otherhand makes efforts to counter this through collaboration with civilians, some of who become policeinformants. Reducing the tax base of the rebels during elections (when they are likely to value resourcesmore) therefore might help the government in their objective as well.4.3 Conceptual frameworkIn this section, I develop a brief conceptual framework to argue how the incentives faced by politi-cians\/state legislators could lead to political business cycles in mining. As described in the previoussection, state legislators have significant involvement in the mining sector, both due to the regulatorystructure of the industry as well as through collusion with mining firms. Mining is India\u2019s most danger-ous profession, with a death every third day in coal mines (Sasi, 2014). Anecdotal evidence suggests thatmining accidents affect the popularity of incumbent politicians with opposition parties often capitaliz-ing on such events (Ray, 2022; Jai, 2019). Incumbents may thus have the incentive to manipulate activ-ity in a way that maintains their rent-seeking ability but at the same time does not hurt their electoralprospects (by shifting activity away to earlier years in their term but not lowering overall activity). Politi-cians facing greater re-election threat would have higher incentives to undertake such manipulation.Therefore, we are likely to observe more pronounced cycles in areas that are electorally competitive, aswell as where the voter base is likely to be more sensitive to these events for e.g. in districts with a higherScheduled Tribe (ST) population, since a large share of mine workers tend to be from the same com-munity (Srivastava, 2005). Since mining is a capital-intensive industry (with large capital-labor ratios),the dis-employment effects of reduced activity is likely to be small too, giving politicians greater leverageover the degree of manipulation.Apart from minimizing accidents and fatalities, a second reason why incumbent politicians (in min-109eral rich areas) could benefit from lowering mining intensity during elections is because it might helpto reduce the intensity of Naxalite conflict. As described in section 4.2.3, the rebel groups target elec-tions with violence, and as a result are likely to put greater value on resources closer to elections to fundtheir activities. Extortion from mining companies constitutes an important part of their tax base. Fromthe perspective of an incumbent politician, being able to control such violence signals positively abouttheir ability to maintain law and order. I thus hypothesize that higher collaboration with civilians isincreasingly important for both the government and rebel groups during election years \u2013 leading to ten-sions between the two parties with respect to controlling the population. The government can reducethe rebels\u2019 resource base more effectively in mining districts compared to non-mining ones. This is be-cause in non-mining districts their resource base tends to be more disaggregated (for e.g. small businessowners, contractors and farmers). In equilibrium, non-mining districts are therefore likely to experiencemore violence before elections (relative to mining districts), since the tax base of rebel groups remainless affected in these areas. I test these predictions empirically in the district-level analysis.4.4 Data and descriptive statisticsI combine seven different sources of data, which are described in this section. Data on state-level vari-ables are generally available over a longer time series, whereas district-level measures for a shorter timehorizon. Nevertheless, this is mitigated by the fact that I observe elections in over a 100 districts, across15 states that are not synchronized with each other. An additional advantage of having a large numberof districts is the inclusion of district fixed effects, which only a few past papers include.State-level mining output data from 16 major Indian states (between 1960-2000) are obtained fromEOPP Indian States Data (Besley and Burgess, 2004), which I supplemented with additional data fromthe Department of Statistics, Planning Commission of India. I digitized mining lease data from 23 states(including the 16 for which I have output data) between 1995-2004 from the website of the Indian Bureauof Mines. Finally, I obtained state-level data (for 21 of the 23 states with mining lease data) on fatal min-ing accidents between 1998-2015 from the Ministry of Labour and Employment, which I also digitized.While the state-level analysis is important in understanding whether the impact of the electoral cycle issignificant enough for the effects to show up on aggregate, analysis only at such a high political juris-110diction level severely limits understanding of heterogeneous effects of crucial factors such as electoralcompetition and conflict propensity. Therefore, I focus on the district-level data for this analysis.The Directorate General of Mines Safety (DGMS), Ministry of Labour and Employment, records in-juries and deaths as a result of both serious and fatal accidents at the district-level for both coal andnon-coal mines in India. These are made available online in a yearly issue, \u201cStatistics of Mines\", that Ihave digitized for the period 2010-2015.76 Figure 4.1 shows all districts included in the empirical analysis.State elections data at the constituency level come from the Election Commission of India\u2019s (ECI) web-site. These data include information on election results and candidate characteristics such as names,caste, wealth and criminal history. Finally, I obtained geocoded data on Naxalite violence intensity at thedistrict level between 2005-2017 from the Uppsala Conflict Data Program (UCDP) and South Asia Terror-ism Portal (SATP). These include information on civilian, security forces and rebel deaths resulting fromclashes between rebel groups and security forces. I consider the construction of this data set, particularlyof the data on mining fatalities and leases, an important contribution of this work.Sub-figure (a) includes all districts included in the analysis of election cycles in mining fatalities.Amongst these, districts seriously affected by Maoist violence (as classified by the Union Ministry ofHome Affairs in 2008)77 have been marked in red and the rest in green. In the empirical analysis, I studywhether mining cycles are larger in Maoist affected districts, since the cost of more mining closer toelections is likely to be higher in these areas, owing to the greater threat of violence. I only use pre-sample classification to avoid confounding by the fact that greater mining activity over the sample periodcould in turn intensify violence in these areas. Note that the government does not update the list ofaffected districts in a consistent manner. Updates are made only when there are substantial changes inthe number of affected districts and therefore the classification in sub-figure (a) is the latest update Iwas able to find before 2010. Sub-figure (b) marks all districts with at least one reported death resultingfrom clashes between security forces and rebels between 2005-2017. Amongst these, mining districts aremarked in orange. Data on each event (clash) at the district level were obtained from UCDP, and thenaggregated to the district-year level. This sample is used to study election cycles in violence and howthey might different across mining and non-mining districts. Table 4.1 provides summary statistics of76Versions of the \u201cStatistics of Mines\u201d are not available in a consistent manner before this period.77LWE Violence\/Under Influence Districts, 2008 (http:\/\/www.satp.org.)111key variables for both, the state- and district-level analyses.4.5 State-level analysisThis section first presents estimating equations for the state-level analysis and then empirical results onthe impact of the election cycle on three different measures of mining activity: mineral licensing, min-ing output and fatalities. In order to estimate the impact of elections on mining intensity the followingsimple model can be run,Yst =\u03c6Est +\u03b1s +\u03b3t +\u03b4s t +ust (4.1)where Yst is the outcome of interest in state s at time t . Est is a dummy taking the value of 1 if thereis an election in the state s in year t , and 0 otherwise. \u03b1s is a state fixed effect, \u03b3t is a year effect and\u03b4s t is a state-time trend. The impact of elections is given by \u03c6. This model however is too simple andunlikely to be very informative for a couple of reasons. Firstly, elections in Indian states are not strictlyscheduled for a specific time of the year every cycle. Majority of the outcomes of interest, such as miningfatalities and output could rise immediately in the post-election period within the election year, whichcould potentially be confounding. Secondly, and more importantly, this model does not allow estimationof the impact of the entire political cycle, which is important. A simple extension to equation (1) canachieve this. The specification is,Yst =\u22121\u2211k=\u22124\u03c6k Ekst +\u03b1s +\u03b3t +\u03b4s t +ust (4.2)where I include dummies for each year of the four years before a state election, omitting the year ofelection to avoid multicollinearity. All results should therefore be interpreted as relative to the electionyear. While this model is able to deal with the two caveats mentioned earlier, a potential endogeneityconcern still remains. Chief Ministers of Indian states have the authority to move elections early withina year from the scheduled month. Such decisions are non-random and could be correlated with thestate of the economy. This is generally a problem for questions that deal with politicians manipulatingpolicies to stimulate the economy during elections, because if Chief Ministers move elections dates ac-112cording to the state of the economy, it could lead to a spurious relationship between elections and theoutcomes of interest. This is much less of a concern in my case, since decisions regarding mineral li-censing and production happen at local administrative levels, are unlikely to be coordinated amongstpoliticians across constituencies\/districts and therefore not affect major political decisions such as elec-tion dates. Moreover, my results, in contrast to previous works, find the shape of the cycle to be exactlyopposite to those existing in the literature alleviating concerns of a spurious relationship between elec-tions and factors positively correlated with a booming economy. One could nevertheless think of analternative story where moving elections to a later date might be beneficial in the aftermath of a min-ing accident. Elections however cannot be postponed and therefore such situations are much less of aconcern. Nevertheless, I discuss three possible ways to deal with this endogeneity issue, all using instru-ments. For each state, a placebo election cycle can be used to instrument the actual observed cycle. Callts the year in which an election was held in state s before the state appears in the sample. The placebocycle would assign elections to ts + 5, ts + 10 and so on. The placebo cycle can then be used to instrumentthe actual cycle to obtain causal estimates.The alternate strategy, suggested by Khemani (2004), similar in vein to the previous strategy is to \u201cup-date\" the placebo cycle suggested above, every time there is an off-cycle election (call this the scheduledcycle). For example, if state s had elections in years 0, 5, 9 and 11, the placebo cycle will take the value1 in years 0, 5, 10, 14 and 16. This provides considerably more first stage power and therefore has more\u201crelevance\" as an instrument.Alternatively, the scheduled cycle itself can be used as the right hand side variable. It is equivalentto using the scheduled cycle as an instrument for the actual cycle. It is worth mentioning at this pointthat majority of my results are insensitive to any of these choices (Scheduled or IV). Furthermore, theOLS and IV results are similar for most of my specifications. The most relevant outcome for which endo-geneity of elections might be a concern is mineral licensing, since a booming economy could lead to aspurious relationship between licensing and election timing. I therefore present, OLS, IV and scheduledcycle results for election cycles in licensing, but do not find large differences in this case either. In othercases, I report results using the scheduled cycle as my right hand-side variable, since in general it is moreefficient than the IV estimator.7878In the few instances where results from the IV approach are different from using the scheduled cycle itself as the main regressor, the113The results are reported in Table 2. Political cycles in mineral licensing are clearly observable. Notethat the outcome variables have been logged and therefore the coefficients should be interpreted as per-centage change over election levels. Across majority of the specifications, there is a statistically and eco-nomically significant negative effect of the penultimate year of the election cycle on the total numberof active mining leases (logged) in a state. The results are robust to the addition of state specific timetrends. Since the state-level analysis comprises of a small number of clusters (23), I also present wildcluster bootstrap p-values along with state-clustered standard errors. The statistical significance of theresults at the 1%, 5% or 10% level are determined by the bootstrap p-values. The most important take-away from this analysis is the fact that the extensive margin (mining leases) is important in generatingmining cycles.Table 4.3 reports the effect of political cycles on mining output at the state level. Mining output datafrom 16 major Indian states over the period 1960-2000 are used for this analysis. I report results for logof total output and output per capita. The trends are robust across all the specifications. Results in Table4.3 show mining output to increase sharply after an election (4 or 3 years from the next election), andthis effect attenuates leading up to the next election. The inclusion of state-specific time trends reducesthe magnitude of the coefficients; but the effects remain economically significant.Finally, to conclude the state-level analysis, I present evidence of election cycles in mining fatalitiesin Table 4. The sample used for this comprises of 21 of the 23 states featuring in the analysis of miningleases (including all 16 used for the output tables), but the Ministry of Labor and Employment have onlymade data on state-level mining fatalities available from 1998 and therefore the sample includes obser-vations from 1998-2015. I use Poisson regressions since these are count outcomes. A similar patternis observed. Results show significantly fewer accidents in the penultimate year of the term, which arerobust to bootstrapping the standard errors (Kline and Santos, 2012 score bootstrap).While the effects 4 years away from a scheduled election were positive and significant for some out-comes with respect to state-clustered standard errors, bootstrap p-values make them statistically in-significant. Nevertheless, the marginal effects are economically significant.Marginal effects imply an additional 4 fatal accidents on average in the year after an election andestimates are more conservative in the latter case. This is not an issue in the district-level analysis since there was no off-cycle election over thetime period considered.114a reduction of approximately 5 fatal accidents in the year immediately before an election, relative tothe election year. Given an average death toll of 28 (see Table 4.1, Panel A) conditional on at least oneaccident in a state in a year, this is an fairly large effect. The results for mining fatalities are robust toa OLS model with the outcome variables log transformed (Appendix Table C.1). Overall, the findingsfrom this section point to the presence of political cycles in different aspects of mining activity betweenIndian state elections, laying a strong foundation for the district-level analysis aimed at understandingthe mechanisms generating these patterns.4.6 District-level analysisIn this section, I explore different factors that may explain election cycles in mining in India. The unit ofanalysis is districts, which is equivalent to a U.S. county in terms of geographic coverage. There are twomain advantages of performing this analysis at the district level. Firstly, greater electoral competition onaggregate at the state-level might not be a significant determinant of the size of mining cycles, owing tothe decentralized structure of India\u2019s mining sector, as described in section 4.2.2. Therefore, focusing onthe mining districts is necessary. Secondly, there is significant variation within states with respect to theproportion of districts that are affected by the Naxalite conflict, whereby only a state-level study of theimpact of conflict on mining cycles will lead to loss of important within state variation. Digitization andcleaning of mining accidents and ancillary electoral outcomes data is still a work in progress. I restrictthe analysis of mining cycles at the district level to the years 2010-2015 in order to ensure the use of aconsistent, balanced panel. None of the 15 states included in the district level analysis had a off-cycleelection between 2010-2015 whereby scheduled cycles and actual cycles are equivalent in this case. I firstreport results on the size of mining cycles at the district level and then proceed to the analysis of factorsdriving these cycles.The specification used for this analysis is,Yd st =\u03b1d +\u22121\u2211k=\u22124\u03c6k Ekst +\u03bbRt +ud st (4.3)115where Yd st is the outcome variable of interest in district d of state s at time t . \u03b1d is a district fixed effectand\u2211\u22121k=\u22124 Ekst are dummies denoting years to the next scheduled election in state s at time t . Onceagain, the election year is omitted. I include region-year fixed effects (\u03bbRt ) in the district level analysis.79The states of India are divided into six regions by the Reserve Bank of India. Region-year fixed effects(\u03bbRt ) control for macroeconomic fluctuations that could affect mineral production differently acrossregions. Results from a total of 104 districts are reported in Table 4.5. The standard errors are clusteredat the state-year level.80 In Column (1), the outcome variable \u201cAny Bad Event\" is a dummy coded 1 ifat least one person was either seriously injured or killed in a mining field in a district in a given year.Coefficients imply up to 24 percentage points increase in the probability of such an event in the threeyears immediately after an election relative to the election year. The effect in the penultimate year of theterm is much smaller and statistically insignificant. Columns (2)-(5) consider the intensive margin. Theoutcome variables are total accidents and total casualties (deaths and serious injuries). The results arerobust to considering both a OLS and Poisson framework as shown. In the OLS specifications, outcomevariables are logged and coefficients should therefore also be interpreted as percentage point changesover election levels.81 Marginal effects from the Poisson model imply 3 additional accidents in the yearimmediately after an election which is similar to the OLS estimate.82 Overall, I find a large impact of thepolitical cycle on mining fatalities at the district level, that aggregates to states.4.6.1 Electoral competition and mining cyclesWhen studying factors that determine the size of mining cycles, it is important to consider district char-acteristics that are both fixed and time varying. I first examine whether electoral competition is a deter-mining factor and thereafter consider fixed factors that are likely to be important. Given that electionsare the basis for mining cycles, electoral competition should be a strong predictor of the size of cycles. Asmentioned earlier, the lowest administrative level at which outcomes are observed are districts, whereasstate-level elections are held at the constituency level and therefore, some form of aggregation is neces-sary. MLAs (Members of State Legislative Assemblies) have significant control over granting of mineral79State-year effects are of course collinear with political cycle dummies.80State-year is the treatment level since it determines the year of the political cycle a district is at.81Since the outcome variables are logged, the coefficients can be interpreted approximately as percentage changes.82In order to ensure that I do not drop observations with 0 values, I add 1 to each observation before the log-transformation. Adding smallernumbers does not affect the results.116licenses and are also likely to be able to manipulate mining activity, irrespective of whether they belongto the state ruling party or not (Mohanty, 2017; Asher and Novosad, 2018). I thus create a variable \u201cCloseElection Proportion\" (Cd st ), which denotes the proportion of constituencies within a district where themargin of victory in the previous election was no more than a certain threshold level. I then modify Equa-tion (3) in the following manner to first examine whether political competition affects mining accidentsin general (i.e. on average; call this the \u201clevel effect\"),Yd st =\u03b1d +\u22121\u2211k=\u22124\u03c6k Ekst +\u03c0Cd st +\u03bbRt +ud st (4.4)where Yd st , \u03b1d , Ekst and \u03bbRt are defined exactly as before. Cd st is the proportion of close elections in adistrict in the previous state assembly election. The variable Cd st is constructed in the following manner.I first denote an election to be close if the victory margin of the winning candidate in a constituency wasno more than 10% of total polled votes83(all results are robust to considering this threshold to be anyvalue between 5%-10%) and then calculate the proportion of constituencies in each district that satisfythis criteria. The value of Cd st for a district is therefore,Cd st =1NcdNcd\u2211k=11(M ar g i nkt < 10%) (4.5)where, Ncd is the number of constituencies in district d , and M ar g i nkt denotes the margin of victoryin constituency k in the previous election. I choose the 10% threshold because the distribution of closeelections that this generates is not too skewed in any direction since that could lead to the results beingdriven by extreme values. As mentioned, the results are not sensitive to this choice. The average winmargin in constituencies that are considered to have had close elections by this criteria is about 4%. Thedistrict-level distribution of close elections is shown in Figure 4.2.The specification in equation 4.4 is restrictive in the sense that it will not detect concentration ofmining fatalities in particular years of the political term. To the extent that voters are myopic, makingmining fatalities more costly during elections, politically competitive districts could simply concentrategreater activity to earlier years of the electoral term as opposed to a reduction in intensity uniformly over83The average margin of victory at the constituency level across all districts in my sample is 13%.117the term (\u201cshape effect\"). In order to elucidate whether this is the case I also run the following model,Yd st =\u03b1d +\u22121\u2211k=\u22124\u03c6k Ekst + \u03c0\u02dcCd st +\u22121\u2211k=\u22124\u03b3k (Ekst \u00d7Cd st )+\u03bbRt +ud st (4.6)where I interact Cd st with each of the political cycle dummies. This allows for a different relationshipbetween political strength and mining accidents for every year of the electoral term.There are 7 districts for which I could not find election results for all constituencies, consistentlyover multiple elections. I do not include them in this analysis. The results are presented in Table 4.6.Once again, standard errors are clustered at the state-year level. The outcome variable in each case isthe total number of events in a district-year (logged). I choose to present my results in this form for eas-ier interpretation of the coefficients. As shown in Table 4.5, marginal effects from a Poisson model arevery similar. In each case, I also present baseline results for comparison. The baseline coefficients arehowever not significantly different from those in Table 4.5, as can be observed in Columns (1) and (4) ofTable 4.6. In columns (2) and (4), the coefficient on Cd st , \u03c0 (from specification 4.4), is estimated to be0, ruling out the possibility that electoral competition affects average levels of fatalities over the politicalcycle. This is important since it implies that electorally competitive districts are not inherently differentin terms of characteristics that affect mining intensity in general. I discuss this in more detail at the endof the section.Columns (3) and (6) present results based on specification 4.6. These estimates however clearly showthat political cycles in fatalities are significantly larger in districts that experienced greater competitionin the previous elections. Note that the overall effect in any year of the term is given by the sum (\u03c6k +\u03c0\u02dc + \u03b3k ). The coefficients (\u03b3k ) on the interaction between Cd st and the political cycle dummies are pos-itive, statistically significant and larger than the coefficient on Cd st (\u03c0\u02dc) alone in the earlier years of thecycle, implying larger positive changes in fatalities from the election year in competitive districts. Thecoefficients on the interactions are however much smaller than \u03c0\u02dc and statistically insignificant in the lasttwo years of the term whereby competitive districts also exhibit a sharper drop in fatalities as the nextelections approach. The coefficient \u03c0\u02dc alone in this specification estimates the impact in the next sched-uled election year, which is negative and significant for both outcomes. The largest difference generatedby political competition is observed in the year immediately after an election and in the next scheduled118election year, pointing to tactical manipulation by authorities responsible for mining operations. This isstrong evidence of a setting where voters are myopic. Authorities take advantage of this and manipulatemining activity in a way that is likely to minimize electoral loss.The results in Table 4.6 are best presented through event study graphs that provide a visual represen-tation. In Figures 4.3 and 4.4, I present log predicted values of accidents and casualties in mines over theelectoral cycle; these are based on the model in equation 4.6. The dotted lines represent 95% confidenceintervals. I present a comparative analysis in each case between a notional district with 0% close elec-tions and one with 50% close elections84 in the previous state assembly polls. Figures 3 and 4, based onresults from Columns (3) and (6) of Table 4.6 respectively, show a significantly larger increase in fatalitiesin the post-election period in the district with 50% close elections compared to the district that had noclose elections in the past cycle; relative to their respective election levels. In fact, log predicted numberof accidents is also larger in the former. However, in the years leading up to the next election, the drop infatalities in the district with 50% close elections is much sharper and overall accidents are fewer as well.In sum, figures 4.3 and 4.4 clearly show that electoral competition magnifies the size of mining cycles.A couple of observations from these graphs merit additional discussion. To the extent that districtswith high electoral competition are characteristically different in unobservables from those with lowcompetition (time varying factors that are not accounted for through fixed effects), particularly with re-spect to factors such as \u201cability\" to conduct mineral prospections, licensing with lesser opposition (po-litical) pressure, one could expect a \u201clevel effect\" of electoral competition on mining intensity over theelectoral term. I do not find evidence of this. However, larger mining cycles in competitive districts(\u201cshape effect\"), without a significant difference in the overall level of intensity cannot be attributed tosuch \u201cability\u201d factors. The dynamics are therefore important in suggesting that there is indeed a be-havioral effect generated by electoral competition; one where competitive districts concentrate greateractivity to earlier years of the political cycle and undertake additional measures to avoid fatalities onlyduring elections.84Please refer to Appendix Figures C.8 and C.9 for a comparison with a notional district with 90% close elections.1194.6.2 Mining cycles in the Red CorridorThe \u201cRed Corridor\" of India is comprised of districts that are affected by the Maoist insurgency. Theyare also some of the most mineral rich districts in India, and as motivated in section 4.2.3, access to keymineral resources is an important source of funding for the Maoists. With the declared agenda of over-throwing the Indian government through armed struggle, boycotting elections form a core componentof the Maoist agenda. Therefore, whether mining districts are part of the Red Corridor or not seems to bean important characteristic to consider when studying the size of mining cycles. I address this questionin this section.Why should one ex-ante believe that mining cycles may be different in the Red Corridor comparedto other districts? The mining industry in India is particularly vulnerable to manipulation by local politi-cians and to the extent that rebel groups value resources more during elections, governments could op-timally try to shut this channel of funding down to reduce violence. In comparison to other sources ofextortion such as small industrialists, contractors, and even poor villagers,85 which politicians do notdirectly control, mineral extraction can be reduced more effectively. Therefore, controlling for the meanlevel of mining intensity across districts, those in the Red Corridor should on average concentrate greatermining activity to years away from elections. Table 4.7 formally tests this. I classify districts to be partof the Red Corridor (a dummy variable) if they were declared in 2008 to be amongst the Maoist affecteddistricts by the Union Ministry of Home Affairs. I use pre-sample classification to avoid the possibilitythat mining activity over the sample period could intensify violence, which in turn could lead to the in-clusion of certain districts into this group, creating an endogeneity issue. Figure 4.1(a) marks miningdistricts that are part of the Red Corridor in red. The effect of being in the Red Corridor on the size ofmining cycles is estimated in exactly the same way as that of electoral competition; except that it is afixed district characteristic and I therefore only include interactions with election cycle dummies whendistrict fixed effects are included (the main effect is of course absorbed in the district effects) but add aseparate dummy for Red Corridor with state fixed effects. The specification (with district fixed effects) is,Yd st =\u03b1d +\u22121\u2211k=\u22124\u03c6k Ekst +\u22121\u2211k=\u22124\u03b3k (Ekst \u00d7RCd )+\u03bbRt +\u03f5d st (4.7)85Srivastava (2009) \u201cExtortnomics : Maoists raise Rs 2000 crore every year\".120where RCd takes the value 1 if the district is classified as part of the Red Corridor and 0 otherwise. Allother variables are defined exactly as before. Table 4.7 presents results with total accidents and total ca-sualties (logged) as the outcome variables respectively.The first important result in Table 4.7 is that mining cycles exist in districts that are not classified aspart of the Red Corridor. Hence, the objective of minimizing fatalities around elections is significant onits own in generating these cycles. Second, the hypothesis that districts in the Red Corridor are likelyto observe greater concentration of mining activity in years away from elections (larger cycles) is alsoobserved to be true.In columns (2) and (5) (specifications with district fixed effects), interactions between the Red Cor-ridor dummy and the political cycle dummies are positive and statistically significant in earlier years ofthe cycle, implying a larger cycle on average in districts of the Red Corridor. Though positive, the coeffi-cient on the interaction term One Y ear \u00d7 Red Cor r i dor is much smaller and statistically insignificant.Note that this is not mechanically driven by the fact that districts in the Red Corridor have higher miningintensity in general. The dependent variable (casualties or accidents) is in logs and therefore coefficientsrepresent percentage point changes over election years. Figure 4.5, based on column (3) of Table 4.7 de-picts this. In each case log predicted accidents in the election year has been normalized to 0 and y-axisvalues in each year of the political cycle represent changes from election levels. Districts in the Red Cor-ridor experience a significantly larger increase in the number of accidents in the years immediately afteran election compared to other districts. In the penultimate year of the term however, the difference inthe relative changes over the election year is insignificant across the two sets of districts.86A similar pattern is observed in the specifications with state-fixed effects (Columns (3) and (6)). Sincethere is variation within states with respect whether districts are part of the Red Corridor or not (refer toAppendix Figure C.3), I include a dummy for Red Corridor (in order to estimate its overall effect), in addi-tion to it\u2019s interaction with election cycle dummies. Note that the interaction terms are positive, thoughstatistically insignificant and reduce in magnitude over the electoral cycle, whereby the coefficient onthe Red Corridor dummy alone (which is negative and significant), dominates (when they are summed)as elections approach. This implies larger cycles in districts of the Red Corridor i.e., they experience86The equality of the coefficients One Y ear and (One Y ear + One Y ear \u00d7 Red Cor r i dor ) cannot be rejected.121a larger drop in fatalities in the pre-election period and a sharper increase in the post-election period(please refer to Appendix figures C.4 and C.5 for a visual representation).Overall, I find strong evidence of the size of the mining cycle to be significantly larger in districts inthe Red Corridor, which is consistent with the hypothesis that constraints on mining activity closer toelections are on average greater in Naxal affected areas.4.6.3 Election cycles and Naxalite conflict intensityWhy are mining cycles larger in the Red Corridor? To answer this question it is first necessary to under-stand the dynamics of Naxalite conflict intensity over state electoral cycles. As motivated in section 4.2.3,the rebels traditionally follow a election boycott strategy, often through the use of violence and it is there-fore likely that levels of violence increase as elections approach. To the extent that governments are moresensitive about their reputation in the election season, increased levels of violence during this period islikely to benefit the Maoist agenda. Marginal value of resources is thus likely to be higher for rebel groupsduring polls, leading to greater conflict in pursuit of acquiring more resources.87 In this sub-section, Ifirst show empirical results supporting this hypothesis and then study whether the intensity of electoralviolence is different across mining districts and non-mining districts.Table 8 presents results from poisson regressions of different measures of conflict intensity on thepolitical cycle dummies. In columns (2),(5) and (8), I include all districts (mining and non-mining) withat least one reported casualty as a result of clashes between rebels and security forces between 2005-2017. In Column (2) the outcome variable total deaths is the sum of security forces, rebel and civiliandeaths from all clashes in a district in a particular year.88 A large and statistically significant increase intotal deaths can be observed in the penultimate year of the term. As mentioned previously, elections inIndian states could be held in any month of the year, whereby regressions of conflict outcomes on a elec-tion dummy alone might not be the best measure of the effect of elections. This is especially importantin this case, since unlike other studies that consider government policies which are fixed over the year(fiscal policy, agricultural credit), there could be large variations within a year in the intensity of conflict.87A large proportion of weapons that Maoists acquire are through attacks on security forces (Prakash, 2014).88Civilians are not the intended targets of rebel groups in these particular clashes but casualties are caused if they are caught in the crossfire.122The one year before effect is thus likely to be \u201ccleaner\".89 Empirically, a regression of conflict outcomeson the election dummy alone shows no significant effect of the election year, however a dummy for thepenultimate year alone is positive and highly significant across all measures of conflict between securityforces and rebels. Columns (5) and (8) show effects on the number of rebel deaths and security forcesdeaths respectively. Similar to Column (2), large positive effects can be observed in the penultimate year.Note that there is no statistically significant difference in average intensity of violence across mining andnon-mining districts within states. In Columns (1), (4) and (7) I regress different measures of conflictintensity on a \u201cMineral Dummy\" coded 1 if the district has mineral deposits and 0 otherwise. I includestate-fixed effects thereby comparing districts within each state. None of the coefficients are preciselyestimated. This result is not to be confused with previous results in the literature that find mineral pres-ence to be a determinant of conflict onset and intensity. Previous works such as Hoelscher et al. (2012)consider the extensive margin of conflict and show that in general, districts that have mineral depositsare more prone to the presence of Naxals compared to districts that do not. My results are closer toGhatak and Eynde (2017) who show that within affected states, mineral presence does not significantlyaffect conflict intensity. In fact, the analysis here goes a step further. I find no significant difference inthe levels of violence, comparing only affected districts within states, but with and without mineral pres-ence.In columns (3), (6) and (9) I interact each of the political cycle dummies with the \u201cMineral Dummy\".The coefficients on the interaction terms One Y ear \u00d7Mi ner al Dummy are negative and significant fortotal deaths and security forces deaths. The null hypothesis of a zero net effect for none of the conflictoutcome measures can be rejected in the penultimate year of the political cycle (relative to the electionyear) in mining districts (H0 : One Y ear + One Y ear \u00d7 Mi ner al Dummy = 0; p-values 0.715, 0.728 and0.178 respectively). However, the coefficients on the One Y ear dummy alone remain strongly significantand also increase in magnitude across all the different measures of conflict intensity. Overall, the resultsshow that as elections approach the increase in levels of violence is significantly stronger in non-miningdistricts. In other words, mining districts exhibit a smaller cycle of violence.89Violence levels are likely to increase until elections are over and not continue in the months after. Therefore, the effect in the penultimateyear is likely to be uncontaminated. Furthermore, to the extent that increased clashes between rebel groups and security forces are over thecapture of resources required to boycott elections (weapons, explosives etc.), the effect in the penultimate year is likely to be larger. It would ofcourse be different for clashes between civilians and rebels with the latter trying to physically prevent voters from voting.123Figure 4.6 plots log predicted total deaths (security forces, rebels and civilians) over the electoral cy-cle in mining and non-mining districts (Please refer to figures C.6 and C.7 in the Appendix for plots withrebel and security forces casualties as separate outcomes). It clearly shows that conflict intensity is sig-nificantly higher in the year before elections but only in non-mining districts. In mining districts, logpredicted total deaths is not significantly in the election year from any other year of the political term.A pattern consistent with the idea that governments undertake active measures to minimize therebels\u2019 resource base during elections, emerges from the analyses in Tables 4.7 and 4.8. As describedearlier, politicians are likely to be able to control mining activity more than other sources of extortion ofrebels, and therefore optimally reduce mining intensity during elections to minimize disruptive activitiesby rebel groups. Not only do the rebels levy monetary taxes on mineral companies, anecdotal evidenceof them looting explosives from mining fields also exist,\u201cNaxal guerillas raided a mining facility of Steel Authority of India Limited (SAIL) in Chhat-tisgarh\u2019s Durg district late Thursday evening and looted about two tonnes of explosives.\u201d(Business Standard, 2013)Government officials, aware of the rebels\u2019 targets have considered removing mining explosives from pub-lic sector mining fields.90 In Table 4.9, using data on kilograms of explosives used in coal mines over theperiod 2010-2015 across 38 major coal mining districts in India (obtained from the Directorate Generalof Mines Safety, Ministry of Labour and Employment), I find significant reductions in the use of coal ex-plosives in the election year as well the one before that, but only in districts of the Red Corridor. Noteonce again that the results are not mechanically driven by greater use of explosives in the Red Corridorin general, since point estimates denote percentage changes over other years. 38 districts are unfortu-nately not enough to estimate the impact of the entire political cycle. I only add year effects instead ofregion-year fixed effects in this case, since regional variation in the location of major coal mines in Indiais not large.91 The coefficients on the interactions (El ect i on\u22121 \u00d7 Red Cor r i dor ) are negative and largerthan those on the El ect i on\u22121 dummies across all outcomes. They are significant for log detonators andnon-permitted explosives,92 implying a reduction in the use of coal mine explosives in Maoist affected90\u201cMining Explosives Attract Maoists\" (https:\/\/www.downtoearth.org.in\/news\/mining-3510).91Results are nevertheless robust to the inclusion of region-year effects.92\u201cPermitted explosives are especially designed to produce a flame of low volume, short duration, and low temperature\u201d(U.S. Bureau ofMines).124districts before elections.93 Though weak, positive coefficients on the El ect i on\u22121 dummy alone couldbe driven by the fact that explosives are moved to districts without Maoist influence.In summary, the empirical findings from this section are consistent with existing anecdotal evidenceand provide strong support for my hypothesis that the objective of minimizing Maoist activity duringelections is an important determinant of the size of mining cycles. The resource base of rebel groups isdifferent across mining and non-mining districts and the government is better equipped to affect theirfunding base in regions with key mineral presence. A reduction in mining intensity around electionstherefore results in less increase in violence in mining districts.4.7 Extensions4.7.1 RobustnessIn this section, I perform robustness checks to ensure that the results are not sensitive to the choice ofeconometric models and also provide additional evidence that strengthens my main findings.Since specifications with mining fatalities and conflict casualties as the left hand-side variable in-volve count outcomes, it is important to ensure that the results are not sensitive to either the choice ofa Poisson or OLS framework. In Table 4.5, I show district level cycles in mining fatalities are robust toconsidering both a Poisson and OLS model. In Table C.1 of the Appendix, I show that results from Table4.4 (state-level cycles in fatal accidents) are also robust to a OLS framework with the outcome variableslog transformed. While Table 4.8 estimates political cycles in Naxalite violence using a Poisson frame-work, Figures 4.6, C.6 and C.7 plot results from OLS specifications with logged outcome variables. Thepatterns remain robust. Finally, unlike previous works, it is not obvious that the election year shouldbe the reference category in this study, as discussed earlier. In Table C.2 (Appendix) I run specificationswith dummies for the election year and the years immediately before and after, in order to estimate theimpact of the political cycle. The overall results and marginal effects are largely similar.A large proportion of the population affected by mining activity, both in terms of mining inducedphysical displacement and mining casualties by virtue of being mine workers, belong to the ScheduledTribes (ST) (Srivastava, 2005). Therefore, districts with a high proportion of ST population can be ex-93A zero net effect however cannot be rejected for Non-permitted explosives (p-value 0.32).125pected to have larger mining cycles, since mining fatalities will be more electorally sensitive in con-stituencies with a large base of ST voters. Note however that the proportion of ST population in districtshas been documented to be a strong predictor of Maoist violence (Gomes, 2015; Hoelscher et al., 2012)whereby a larger cycle in these areas could simply driven by ST population shares acting as a proxy forMaoist violence and\/or an interaction of both of these effects.94I cannot differentiate between these channels or comment on the relative importance of each; but atthe least, larger cycles in districts with high ST population proportions would act as a robustness checkof the results in Table 4.7 and potentially also imply that the composition of voter base matters as a de-termining factor. Table C.3 in the appendix tests this. I present results for both accidents and casualties.In each case, I first show the impact of elections on outcomes alone (election dummy) and then includean interaction between the election dummy and the proportion of ST population (obtained from the2011 Census of India) in each district. While this is after my sample for fatalities begin, it is not a ma-jor concern since caste compositions are fairly stable across districts in India and are unlikely to havechanged significantly over such a short period of time. The coefficients should be interpreted as per-centage changes over non-election years.95 For both accidents and casualties, the interaction terms arenegative and economically significant (though statistically insignificant),96 implying a sharper drop infatalities in districts with greater ST population. This is important since it adds credibility to both, theeffect of electoral competition and conflict on mining cycles. It acts as a robustness check for larger min-ing cycles in the Red Corridor, and potentially shows that voter demographics are also important.Another factor to naturally consider as important in determining the size of mining cycles is literacyrates. The mining districts in India are amongst the worst performing in terms of socio-economic out-comes, which can facilitate larger cycles if politicians are not adequately held accountable for accidents.Literate voters might be less myopic in their voting behavior whereby accidents in general are likely to bepenalized irrespective of when they occur. Districts with high literacy rates should therefore experiencesmaller cycles. This is exactly what is observed in Table C.3. In columns (3) and (6), I include interactionsbetween the election dummy and the proportion of population in each district that is literate. These94The mean of ST population percentages across districts in the Red Corridor is 23%, compared to only 14% in the other districts in mysample.95The coefficient on the interaction term must be multiplied by the proportion of Scheduled Tribes in a district to obtain the overall marginaleffect.96For other outcomes such as deaths and fatal accidents it is significant (results not reported).126data were also obtained from the 2011 Census of India. The coefficients on the election dummies aloneare large, negative and statistically significant, whereas those on the interaction terms are positive andsignificant implying smaller cycles in districts with higher literacy rates.In summary, the results from Table C.3 provide strong support for my main findings and in addi-tion have implications for policy aimed at diffusing opportunistic cycles in mining fatalities, primarilythrough means that increase political accountability.Given the claim that the rebels bank on local grievances against mining activity in qualitative stud-ies (Kujur, 2009), it is possible that mine accidents, especially deaths, aggravate grievances that rebelsutilize to propagate their agenda. An important way of doing this would be through increased recruit-ment to the group. A larger recruitment base is thus likely to help facilitate this process. In Table C.4 ofthe appendix, I first show mining fatalities in districts to be positively correlated with conflict onset andintensity. Thereafter in columns (2), (5) and (6), I interact mining fatalities with the proportion of ST pop-ulation in districts, documented to be a strong predictor of Maoist violence primarily though increasedopportunity of recruitment to groups (Gomes, 2015; Hoelscher et al., 2012). I find this correlation to bestronger in districts that have a higher share of ST population. The coefficients on the triple interactionterm between fatalities, ST proportion and the election dummies are negative and significant implyinga weakening of this correlation in the election year, which concurs with my main results. These coeffi-cients should not be interpreted as causal estimates. However, they do provide correlational evidence ofthe fact that political costs of mining accidents are on average greater in districts that have higher con-flict propensity due to their demographic composition and characteristics.Overall through the range of robustness checks performed, I find strong evidence in support of thetwo primary channels I hypothesize are at play in generating mining cycles. Additionally, the analysispoints to possible interaction of these two mechanisms, which would be interesting to address in futurework.4.7.2 DiscussionI note two potential limitations to the analysis in this paper. In the district level analysis, I only use min-ing fatalities data as proxy for mining intensity, primarily because it is the objective of reducing fatalities,127as I show, that is important for politicians during elections. Fatalities data are obtained from govern-ment sources and one can potentially argue that there is deliberate underreporting of accidents closerto elections, which is driving my results. However, this is unlikely for two reasons. The data for each yearare not released until after the end of the year. Thus, to the extent that elections are the basis of miningcycles, there is no incentive to simply underreport fatalities, unless they actually reduce. It is difficult tosuppress the spread of information on deaths and accidents locally at the constituency level, especiallysince opposition party candidates are likely to use them as campaigning tools. Therefore, underreportingis unlikely to be the first order consideration for incumbent politicians. Note that the results on the effectof electoral competition on the size of mining cycles (Table 4.6) in such a situation would imply greaterunderreporting in a consistent manner in electorally competitive districts relative to non-competitiveones, but only as elections approach. This is also unlikely. Furthermore, the effects are observed for out-put and mineral licensing as well, when aggregated at the state-level. The government might actually betempted to overreport activity during elections, at least when it comes to these two measures. The factthat the same pattern is observed across all three measures provides strong evidence against a situationwhere the results would be generated simply by systematic underreporting during elections.The effect of electoral competition on the size of mining cycles is analyzed using election outcomesover at least two elections for every district in the sample. This could potentially lead to an endogeneityproblem, if there is a spurious relationship between mine accidents and election results. One way aroundthis problem would be to restrict the analysis to only one election cycle per district. However, with a littleover 100 districts, this would mean significant loss of power leading to less precise estimates. Further-more, since elections are not synchronized, it would also mean using different panel sizes for districtsin each state, which is not ideal. It is possible to use the same panel size and at the same time consideronly one election outcome per district, using variation from districts within states (using state fixed ef-fects). I have tried this. However, this leads to a sample that is not representative, since it entails using atime period over which a large proportion of states in the sample did not have elections. Nevertheless,it might be possible to use past election results to observe behavior in the years immediately after theelection, and predicted margin of victory in the second half of the political term. This is dependent onthe availability of consistent and reliable data on opinion polls.1284.8 ConclusionFocusing on India, this chapter documents the presence of opportunistic political cycles in several as-pects of mining activity, different from the ones traditionally observed in the developed or the developingworld. While political cycles in economic activity generally exhibit a U-shape pattern over electoral cy-cles, with greater activity during elections, I show that mining in India follows a counter cyclical patternwith mineral extraction minimized in election years.The analysis in this chapter makes two factors driving these patterns apparent. Mining fatalities arepolitically unfavourable and electorally competitive districts undertake additional measures to minimizeaccidents compared to non-competitive ones during elections. This could stem from reduced outputand\/or better safety practices, especially because studies have found fatality records in Indian mines tofare poorly even when scaled for output compared to records in the U.S.A or developing countries suchas South Africa (Mandal and Sengupta, 2000). I do not address the mechanisms directly in this paper, butit remains an important area of future work. However, the fact that accidents are reduced significantlyin competitive districts (relative to non-competitive ones) only in election years, is evidence that miningfatalities are electorally sensitive, but also that voters are myopic and politicians therefore address thisonly during polls. Additionally, the fact that cycles are smaller in districts with higher literacy and largerin districts with greater Scheduled Tribe (ST) population showcase strategic behavior on the part of au-thorities responsible for mining operations.The second factor driving mining cycles, also electorally tied, is the propensity of Maoist conflict.Based on anecdotal evidence and previous works that show extortion of mining revenues constitute animportant revenue base for rebels, I hypothesize that minimizing this source of funding is important forpoliticians during elections, since rebel groups target the electoral process to spread their agenda. Con-sistent with this hypothesis, I find mining cycles to be larger in the Red Corridor, with greater reductionsin activity in conflict prone districts during elections. This in turn results in smaller cycles of violence inMaoist affected mining districts relative to non-mining ones.My results have important implications for addressing political cycles in mining fatalities and alsofor conflict resolution strategies. Fatalities in mining fields need to be addressed systematically, and alarger share of the population with basic education, by being less myopic in their voting behavior can129help reduce the magnitude of these cycles. Furthermore, given that a large proportion of mine workersbelong to the Scheduled Tribes (ST), political reservation for ST candidates in mineral rich areas couldresult in greater attention to the issue. Related to this, if rebels do bank on grievances generated as aresult of mining deaths, reservation could also lead to reduced violence intensity in these areas. This isanother important area I plan to focus on in future work.Election cycles in violence, as documented in Table 8 clearly point to the time varying nature of thevalue of resources to rebel groups. This has implications for deployment of security personnel to protectlegitimate mining activity. This is also true with respect to rebels\u2019 tax base is non-mining districts; how-ever further research is required into first identifying and thereafter understanding policy that would beeffective in achieving this. Furthermore, while policies such as subsidised rainfall insurance and guaran-teed employment schemes have been successful in reducing rebel recruitment in the past, the findingsof this paper suggest that their effectiveness is likely to vary over the electoral cycle. This is not to sug-gest intensifying such schemes during elections, but solely from the objective of minimizing violence,greater government responsiveness to income shocks at times when rebels value recruitment more, isimportant. Future work could focus on building a theoretical framework to formalize the different chan-nels generating mining cycles. More importantly, a model will allow counterfactual policy analysis whichis key. Will greater political reservation for backward classes reduce violence and conflict in mineral richareas ? Will it affect the size of mining cycles? Can changes to the regulatory structure of the miningsector reduce political cycles in accidents? These are questions of vital importance, answers to whichcan help fix large-scale market failures in India\u2019s mining industry \u2013 unlocking its true potential could addUSD 250 billion to India\u2019s GDP creating 13-15 million jobs through both direct and indirect contributionby 2025.9797Strategy Plan for Ministry of Mines 2015 (https:\/\/mines.gov.in\/writereaddata\/UploadFile\/Strategy.pdf)1304.9 Tables and figures4.9.1 TablesTable 4.1: Summary statistics of key variablesVariable Mean Standard Deviation NMineral Output\/Accidents\/LeasesLog Mining Output (1960-2000) 8.05 2.31 592Mining\u2019s Share of State Output .032 .028 592Fatal Mining Accidents (1998-2015) 16.71 33.89 350Deaths from Fatal Accidents 16.67 33.79 350Deaths from Fatal Accidents (Accidents >0) 28.50 40.29 350Log Number of Mining Leases (1995-2004) 5.01 1.78 221Political Variables (for Output)Election Year 0.22 0.42 592Scheduled Election Year 0.23 0.42 592Four Years from Scheduled Election 0.22 0.42 592Three Years from Scheduled Election 0.20 0.41 592Two Years from Scheduled Election 0.16 0.34 592One Year from Scheduled Election 0.19 0.38 592Political Variables (for Accidents)Election Year 0.22 0.41 350Scheduled Election Year 0.20 0.40 350Four Years from Scheduled Election 0.19 0.40 350Three Years from Scheduled Election 0.20 0.40 350Two Years from Scheduled Election 0.18 0.38 350One Year from Scheduled Election 0.23 0.42 350Political Variables (for Leases)Election Year 0.21 0.41 221Scheduled Election Year 0.20 0.39 221Four Years from Scheduled Election 0.20 0.40 221Three Years from Scheduled Election 0.20 0.41 221Two Years from Scheduled Election 0.19 0.39 221One Year from Scheduled Election 0.20 0.40 221(a) Panel A: State-year levelVariable Mean Standard Deviation NMining Fatalities (2010 - 2015)Total Accidents 6.10 16.96 605Fatal Accidents 1.08 1.84 605Serious Accidents 5.02 16.08 605Total Serious Injuries 5.15 16.67 605Total Deaths 1.36 2.36 605Naxalite Conflict (2005 - 2017)Security Forces Deaths from Naxalite Conflict 1.10 5.94 1417Rebel Deaths from Naxalite Conflict 1.01 3.63 1417Political Variables (for Fatalities)Scheduled Election Year\/ Election Year 0.17 0.37 605Four Years from Scheduled Election 0.22 0.42 605Three Years from Scheduled Election 0.23 0.42 605Two Years from Scheduled Election 0.18 0.38 605One Year from Scheduled Election 0.19 0.39 605(b) Panel B: District-year levelNotes: The unit of observation in Panel A is a state-year. The output values are normalized with respect to 1973 prices. Mining fatalities and leasedata are obtained from 23 states (including the 16 for output) between periods 1998-2015 and 1995-2004 respectively. Political variables aredummies for each year of the political cycle. The unit of observation in Panel B is a district-year. All values reported are averages across districtsbut over different time periods as mentioned in the table.131Table 4.2: Mining lease distribution and years to scheduled electionOLS IV Scheduled Cycle(1) (2) (3) (4) (5) (6)Four Years 0.0439 0.022 -0.038 -0.130 0.000 -0.047(0.0447) (0.0370) (0.101) (0.0967) (0.0424) (0.035)[0.359] [0.484] [0.716] [0.151] [0.924] [0.124]Three Years -0.0696 0.007 0.000 -0.065 0.005 -0.039(0.0476) (0.0287) (0.0935) (0.0420) (0.0563) (0.029)[0.157] [0.790] [0.997] [0.189] [0.925] [0.137]Two Years -0.0631 0.0186 -0.029 -0.093 -0.014 -0.060(0.0375) (0.0338) (0.113) (0.0814) (0.0648) (0.0553)[0.167] [0.507] [0.815] [0.309] [0.802] [0.215]One Year -0.117*** -0.057** -0.070 -0.178*** -0.042 -0.125**(0.041) (0.028) (0.118) (0.091) (0.055) (0.043)[0.004] [0.023] [0.594] [0.007] [0.564] [0.012]Outcome Mean 5.01 5.01 5.01 5.01 5.01 5.01(1.78) (1.78) (1.78) (1.78) (1.78) (1.78)State Effects Yes Yes Yes Yes Yes YesYear Effects Yes Yes Yes Yes Yes YesState Time Trends No Yes No Yes No YesN 221 221 221 221 221 221R2 0.986 0.992 0.986 0.991 0.986 0.992Notes : * p<0.10, ** p<0.05, *** p<0.010 with respect to wild cluster bootstrap p-values. State-Year Levelobservations between 1995-2004. Dependent variable is log number of active leases in a given state ina year. Standard Errors clustered at the state level in parenthesis. P-values from Wild cluster Bootstrap(Davidson and MacKinnon, 2010 for IV specifications) with 1000 replications presented in square [] brack-ets. Scheduled cycles used as IV for actual cycles.132Table 4.3: Mining output and years to scheduled electionLog Per Capita Log Output(1) (2) (3) (4)Four Years 0.114** 0.0613* 0.112** 0.0569(0.0414) (0.0343) (0.0446) (0.0363)[0.0210] [0.0870] [0.0400] [0.1210]Three years 0.170** 0.100** 0.170** 0.0952*(0.0609) (0.0455) (0.0647) (0.0482)[0.0260] [0.0450] [0.0280] [0.0680]Two Years 0.150* 0.0776 0.146 0.0663(0.0736) (0.0560) (0.0786) (0.0629)[0.0520] [0.2050] [0.1200] [0.3250]One Year 0.114 0.0427 0.116 0.0393(0.0658) (0.0400) (0.0578) (0.0414)[0.1510] [0.294] [0.1510] [0.3625]Outcome Mean -2.31 -2.31 8.05 8.05(1.87) (1.87) (2.30) (2.30)State Effects Yes Yes Yes YesYear Effects Yes Yes Yes YesState Time Trends No Yes No YesN 590 590 592 592R2 0.893 0.936 0.921 0.954Notes : * p<0.10, ** p<0.05, *** p<0.010 with respect to wild cluster bootstrap p-values. State-Year level observa-tions covering 16 major Indian states between 1960-2000. Standard errors clustered at the state-level reported inparenthesis. Wild cluster bootstrap p-values with 1000 replications in square [] brackets. \u201cLog Per capita\u201d refersto log of per capita mining output. \u201cLog Output\" refers to log of total mining output. Output values normalizedwith respect to 1973 prices.133Table 4.4: Fatal mining accidents and years to scheduled election (Poisson)Accidents Injuries Deaths(1) (2) (3) (4) (5) (6)Four Years 0.213 0.227 0.646 0.928 0.205 0.225(0.191) (0.222) (0.419) (0.512) (0.179) (0.198)[0.296] [0.391] [0.240] [0.178] [0.325] [0.338]Three Years 0.285 0.275 0.469 0.704 0.277 0.270(0.388) (0.420) (0.460) (0.551) (0.374) (0.400)[0.805] [0.905] [0.340] [0.252] [0.676] [0.757]Two Years -0.0510 -0.154 0.0586 0.0822 -0.193 -0.297(0.190) (0.176) (0.259) (0.336) (0.246) (0.234)[0.823] [0.412] [0.818] [0.825] [0.491] [0.260]One Year -0.233* -0.340** -0.952** -0.949* -0.197* -0.304**(0.122) (0.129) (0.374) (0.393) (0.120) (0.131)[0.087] [0.027] [0.046] [0.085] [0.100] [0.042]Outcome Mean 16.71 16.71 3.02 3.02 16.67 16.67(33.89) (33.89) (7.05) (7.05) (33.79) (33.79)State Effects Yes Yes Yes Yes Yes YesYear Effects Yes Yes Yes Yes Yes YesState Time Trends No Yes No Yes No YesN 350 350 350 350 350 350Log-Likelihood -1186 -1018 -385 -306 -1382 -1206Notes: * p<0.10, ** p<0.05, *** p<0.010 with respect to Kline and Santos (2012) score bootstrap p-values. State-YearLevel observations between 1998-2015. Only fatal accidents (accidents with at least one death) feature in this sample.Dependent variables are the number of events in a year in a given state. Standard errors clustered at the state levelreported in parenthesis. P-values from Wild cluster Bootstrap with 1000 replications presented in square [] brackets.The sample used for this analysis includes data on 21 Indian states.134Table 4.5: Mining fatalities and years to scheduled election (district-level)Any Bad Event Accidents Casualties(1) (2) (3) (4) (5)Four Years 0.236*** 0.214*** 0.475*** 0.234*** 0.506***(0.0758) (0.0511) (0.138) (0.0600) (0.153)Three Years 0.179*** 0.207*** 0.402*** 0.203*** 0.384**(0.0656) (0.0547) (0.131) (0.0693) (0.157)Two Years 0.222*** 0.199*** 0.508*** 0.211*** 0.532***(0.0616) (0.0530) (0.141) (0.0691) (0.167)One Year 0.0930 0.0385 0.179 0.0478 0.196(0.0608) (0.0651) (0.160) (0.0717) (0.171)Outcome Mean 0.64 6.10 6.10 6.50 6.50(0.49) (16.96) (16.96) (17.61) (17.61)District Effects Yes Yes Yes Yes YesRegion-Year Effects Yes Yes Yes Yes YesN 605 605 605 605 605R2\/Log \u2212Li kel i hood 0.535 0.880 -1063 0.853 -1124Estimation OLS OLS Poisson OLS PoissonNotes : * p<0.10, ** p<0.05, *** p<0.010. District-Year level observations covering 104 districts across 15 states be-tween 2010-2015. Standard errors clustered at the state-year level reported in parenthesis. Standard deviations foroutcome means are reported in parenthesis. \u201cAny Bad Event\" is a dummy variable coded 1 if at least one person waseither seriously injured or died in a mining field. \u201cAccidents\" refer to the sum of both fatal and serious accident and\u201cCasualties\" refer to the total number of peopled killed and injured in mining fields in a district in a given year. Out-comes Casualties and Accidents for OLS regressions are subject to a log (x+1) transformation.135Table 4.6: Electoral cycle, political competition and mining fatalitiesLog Accidents Log Casualties(1) (2) (3) (4) (5) (6)Four Years 0.237*** 0.237*** -0.0224 0.268*** 0.269*** -0.065(0.0594) (0.0603) (0.115) (0.0680) (0.0690) (0.124)Three Years 0.339*** 0.338*** 0.178* 0.357*** 0.356*** 0.147(0.0750) (0.0764) (0.105) (0.0891) (0.0895) (0.121)Two Years 0.244*** 0.243*** 0.169* 0.271*** 0.270*** 0.165(0.0687) (0.0701) (0.102) (0.0860) (0.0877) (0.129)One Year 0.0477 0.0467 -0.0652 0.0667 0.0656 -0.0434(0.0749) (0.0762) (0.0926) (0.0832) (0.0841) (0.104)Close Election Proportion 0.020 -0.286** 0.021 -0.366**(0.0959) (0.139) (0.104) (0.148)Four Years \u00d7 Close Election Proportion 0.556*** 0.717***(0.213) (0.214)Three Years \u00d7 Close Election Proportion 0.349** 0.451**(0.178) (0.189)Two Years \u00d7 Close Election Proportion 0.165 0.240(0.187) (0.205)One Year \u00d7 Close Election Proportion 0.266 0.270(0.172) (0.182)Outcome Mean 6.36 6.36 6.36 6.89 6.89 6.89(17.59) (17.59) (17.59) (18.27) (18.27) (18.27)District Effects Yes Yes Yes Yes Yes YesRegion-Year Effects Yes Yes Yes Yes Yes YesN 558 558 558 558 558 558R2 0.849 0.849 0.885 0.817 0.817 0.861* p<0.10, ** p<0.05, *** p<0.010. District-Year Level observations between 2010-2015 covering 97 districts. Standarderrors clustered at state-year level in parenthesis. The outcome means reported are the actual means and not log values.Standard deviations for outcome means are reported in parenthesis. Log Accidents refer to the natural log of the totalnumber of accidents (both serious and fatal) in a district in a particular year. Log Casualties refer to the natural logarithmof total deaths and injuries in mining fields in a given district in a year. Outcome variables are subject to a log (x + 1)transformation.136Table 4.7: Electoral cycle, Red Corridor and mining fatalitiesLog Accidents Log Casualties(1) (2) (3) (4) (5) (6)Four Years 0.214*** 0.188*** 0.183* 0.234*** 0.223*** 0.218**(0.0521) (0.0556) (0.0954) (0.0610) (0.0637) (0.101)Three Years 0.207*** 0.151** 0.143 0.203*** 0.147** 0.139(0.0549) (0.0608) (0.0939) (0.0695) (0.0718) (0.103)Two Years 0.199*** 0.122** 0.106 0.211*** 0.135* 0.122(0.0530) (0.0594) (0.0929) (0.0691) (0.0742) (0.106)One Year 0.0385 -0.0101 -0.00388 0.0478 -0.0120 -0.00218(0.0653) (0.0677) (0.102) (0.0720) (0.0725) (0.106)Red Corridor -0.383* -0.389*(0.231) (0.235)Four Years \u00d7 Red Corridor 0.0972 0.116 0.0401 0.0590(0.0969) (0.249) (0.109) (0.252)Three Years \u00d7 Red Corridor 0.191** 0.242 0.185** 0.237(0.0884) (0.243) (0.0911) (0.246)Two Years \u00d7 Red Corridor 0.243*** 0.252 0.230** 0.238(0.0887) (0.255) (0.0975) (0.264)One Year \u00d7 Red Corridor 0.171 0.142 0.189 0.149(0.122) (0.296) (0.129) (0.306)Outcome Mean 6.10 6.10 6.10 6.50 6.50 6.50(16.96) (16.96) (16.96) (17.61) (17.61) (17.61)State Effects No Yes No No Yes NoDistrict Effects Yes No Yes Yes No YesRegion-Year Effects Yes Yes Yes Yes Yes YesN 605 605 605 605 605 605R2 0.844 0.196 0.844 0.811 0.192 0.811* p<0.10, ** p<0.05, *** p<0.010. District-Year Level observations covering 104 districts between 2010-2015. Standard errorsclustered at state-year level in parenthesis. The outcome variables are the number of accidents and the sum of deaths andinjuries in mining fields in a district-year (logged) respectively. The actual mean values (not logged) are reported for theoutcome variables. \u201cRed Corridor\" is a dummy variable coded 1 if a district had been classified by the Union Ministry ofHome Affairs to be part of the areas affected by the Naxalite conflict in 2008, which is prior to the beginning of the fatalitiessample. Figure 4.1(a) marks all such districts in red and those that are not part of the \u201cRed Corridor\" in green. Outcomevariables are subject to a log (x+1) transformation.137Table 4.8: Election cycles and Naxalite conflict (Poisson regressions)Total Deaths Security Forces Deaths Rebel Deaths(1) (2) (3) (4) (5) (6) (7) (8) (9)Mineral Dummy -0.0462 0.0335 -0.212(0.508) (0.594) (0.416)Four Years -0.322 -0.244 -1.039*** -0.941** 0.220 0.203(0.238) (0.329) (0.293) (0.431) (0.282) (0.305)Three years 0.174 0.0290 0.143 -0.129 0.311 0.290(0.224) (0.320) (0.318) (0.427) (0.339) (0.360)Two Years 0.234 0.0248 0.318 0.0335 0.123 -0.0873(0.370) (0.485) (0.423) (0.584) (0.507) (0.579)One Year 0.812** 1.106*** 0.673* 1.002** 1.012** 1.193***(0.320) (0.363) (0.368) (0.445) (0.434) (0.423)Four Years \u00d7 Mineral Dummy -0.128 -0.194 0.0663(0.468) (0.646) (0.446)Three Years \u00d7 Mineral Dummy 0.122 0.269 -0.00811(0.492) (0.576) (0.432)Two Years \u00d7 Mineral Dummy 0.208 0.330 0.282(0.431) (0.554) (0.418)One Year \u00d7 Mineral Dummy -0.969** -1.183* -0.590(0.496) (0.707) (0.389)p-value (One Y ear+ One Y ear \u00d7 Mi ner al Dummy = 0) 0.715 0.728 0.178Outcome Mean 2.16 2.16 2.16 1.10 1.10 1.10 1.01 1.01 1.01(9.09) (9.09) (9.09) (5.94) (5.94) (5.94) (3.63) (3.63) (3.63)State Effects Yes Yes YesDistrict Effects No Yes Yes No Yes Yes No Yes YesRegion-Year Effects Yes Yes Yes Yes Yes Yes Yes Yes YesN 1417 1417 1417 1417 1417 1417 1417 1417 1417Log-Likelihood -4851 -2457 -2388 -2901 -1443 -1381 -2480 -1370 -1358* p<0.10, ** p<0.05, *** p<0.010. District-Year Level observations covering 2005-2017. Standard errors clustered at state-year level in parenthesis exceptfor regressions in Columns (1), (4) and (7) where I cluster standard errors at the district level. Standard deviations for outcome means are reportedin parenthesis. The outcome variable in columns (1)-(3) is the total number of deaths from clashes between security forces and naxal rebels. Thesealso include civilians who died in these clashes. In columns (4)-(6) and (7)-(9), the outcome variables are number of rebel and security forces deathsrespectively. There are 109 districts in these regressions.138Table 4.9: Elections and coal mine explosivesLog Detonators Log Total Explosives Log Non-Permitted(1) (2) (3) (4) (5) (6)El ect i on -0.0148 0.0170 0.0661 0.156 0.0867 0.155(0.126) (0.166) (0.0807) (0.121) (0.0961) (0.127)El ect i on\u22121 -0.0226 0.176 0.0625 0.140 0.139 0.259**(0.136) (0.126) (0.0923) (0.114) (0.0899) (0.0989)Election \u00d7 Red Corridor -0.263* -0.273** -0.287**(0.147) (0.128) (0.129)El ect i on\u22121 \u00d7 Red Corridor -0.583*** -0.158 -0.310**(0.161) (0.117) (0.121)Outcome Mean 12.85 12.85 15.27 15.27 15.21 15.21(2.51) (2.51) (1.78) (1.78) (1.85) (1.85)District Effects Yes Yes Yes Yes Yes YesYear Effects Yes Yes Yes Yes Yes YesN 220 220 221 221 207 207Adj. R2 0.928 0.929 0.923 0.924 0.919 0.920* p<0.10, ** p<0.05, *** p<0.010. District-Year level observations for covering 38 major coal mining districts inIndia between 2010-2015. Standard errors clustered at the state-year level reported in parenthesis. Standarddeviations for outcome means are reported in parenthesis. Each district reports total kilograms of explosivesand detonators used in a year. The mean of the logged values have been reported for each outcome variable.\u201cElection\u22121\" is a dummy variable denoting whether the state which a district belongs to, is scheduled to havea election in the following year. \u201cRed Corridor\" is a dummy variable taking the value 1 if a district had beenclassified by the Union Ministry of Home Affairs as affected by Naxal violence in 2008. Non-permitted explo-sives are less environmentally friendly and \u201cshould not be used in underground coal mines where there is anypossible risk of igniting combustible gases or coal dust\" (U.S. Bureau of Mines).1394.9.2 FiguresFigure 4.1: Sample for district-level study(a) Mining Districts(b) Naxal Affected Districts (2005-2017)Note: This figure marks all the districts that form the entire sample for the district level study. Sub-figure (a) includes all themining districts in my sample. The Naxal affected districts in 2008 are marked in red in sub-figure (a). Sub-figure (b) includesall districts where at least one death has been reported between 2005-2017 as a result of clashes between Naxalite rebels andgovernment security forces. The mining districts are marked in orange.140Figure 4.2: Distribution of close elections0.511.52Density0 .2 .4 .6 .8 1Close Election ProportionDistrict Level Distribution of Close ElectionsNote: This figure shows the distribution of close elections across all the districts in my sample. An election is considered to beclose if the win margin in a constituency within a district was less than 10 % of total polled votes.Figure 4.3: Accident cycles and electoral competitionNote: This diagram plots log predicted accidents in mines over the next electoral cycle for notional districts with 0% and 50%close elections in the previous elections respectively. It is based on Column (3) of Table 4.5. Note that the value in election yearis 0 by construction for a district with no close elections. Dotted lines represent 95% confidence intervals.141Figure 4.4: Fatality cycles and electoral competitionNote: This diagram plots log predicted casualties in mines over the next electoral cycle for notional districts with 0% and 50%close elections in the previous elections respectively. It is based on Column (6) of Table 4.5. Note that the value in election yearis 0 by construction for a district with no close elections. Dotted lines represent 95% confidence intervals.Figure 4.6: Total conflict deaths over the electoral cycleNote: This figure plots log predicted total deaths from clashes between naxal rebels and security forces over the electoral cyclein mining and non-mining districts. The value in the election year is normalized to 0 in each case. It is based on specificationsof the form in Table 8 Columns (3), (6) and (9) but from a OLS model with logged outcome variable. Mining districts are thosethat feature in my sample of mining fatalities. Dotted lines show 95% confidence intervals.142Figure 4.5: Accident cycles and Red CorridorNote: This figure plots log predicted accidents in mining fields over the electoral cycle for a district in the red corridor (redline) and a district that is not in the red corridor (blue line) based on equation (6) with district fixed effects. The value in theelection year is normalized to 0 in each case. I use pre-sample classification of districts into the Red Corridor (fixed districtcharacteristic). Hence, equation (6) only includes interactions between RC and the electoral cycle dummies. This figure isbased on results from Column (3) of Table 4.7. Dotted lines show 95% confidence intervals.143Chapter 5ConclusionThis thesis consists of three distinct chapters at the frontier of research in development economics.Chapter 2 shows that the effects of religious diversity on team productivity and worker attitudes in afirm depends on the type of production technology in use. I partnered with a large processed food man-ufacturing plant in West Bengal, India and randomly allocated its Hindu and Muslim workers to be ineither religiously mixed (Hindus and Muslims) or homogeneous (Hindus only) teams. There are multi-ple production tasks at the factory. I classify these tasks into high- (HD) and low-Dependency (LD) typeswith time-use data on the degree of continuous coordination required amongst teammates to ensureuninterrupted production and the dependence on teammates for breaks.I find that while religious mixing leads to a loss in output in high-dependency tasks, it has no effect inlow-dependency work. Consistent with this, worker surveys reveal more frictions amongst workers frommixing in high-dependency work: there are greater accusations, more inter-group blame and lower teamcohesion in general relative to homogeneous teams, as well as relative to mixed low-dependency teams.However, the negative effects on output in high-dependency tasks attenuate over time and dissipatecompletely in four months. The improvements in production are accompanied by improved inter-grouprelations as well. In low-dependency tasks, while there is no negative output shock from religious mix-ing, there are little or no positive effects on inter-group relations. Overall, this pattern of results suggeststhat technology that incentivizes individuals to learn to work together is important in overcoming ex-isting intergroup differences \u2013 and leads to improved relations and team performance. However, morespeculatively, the tension between the goal of maximizing short-run productivity and that of improvingintergroup relations might explain why (in equilibrium) we could see a lot of integration (at work) with-out intergroup relations improving \u2014 the integration might only occur in contexts where it is sociallyineffective.I hope to now conduct a large-scale survey with firm owners and workers across India to under-144stand how firms with different production technologies deal with (the effects of) diversity. Do high-dependency firms segregate workers based on caste and religion? Do low-dependency firms integrateworkers but without inter-group relations improving? Which exact aspects of high-dependency tasksmake diversity costly? Can some of these interactions be substituted with low-dependency work? Adeeper analysis of the role that technology plays in determining the effects of diversity can help us un-derstand how the costs of diversity might change as economies undergo structural transformation. Mynext steps will be aimed at understanding how the interaction between production technology and eth-nic diversity matters for broader economic change.Chapter 3 uses 19th and 20th century state-level bans on cousin marriage in the US to provide causalmicro-evidence of the impact of consanguineous marriages on a range of socio-economic outcomes.We borrow a method from population genetics and show that excess rates of same-surname marriagesprovide credible estimates of cousin marriage rates by surname, by state as well as over time. Our mainresults show that bans on first-cousin marriage led to a reduction in the rate of such marriages, led tohigher incomes, more schooling, greater female labor force supply and rural-urban migration. We arguethat these effects are driven by the weakening of family ties rather than a genetic channel.Our findings are consistent with recent work in anthropology and sociology that studies the charac-teristics of kin-based societies. A large body of ethnographic and historical research shows that intensivekinship is associated with greater cooperation within a group, but it comes at the cost of geographicand social mobility, as well as participation in mainstream institutions (Henrich, 2020). Our results areconsistent with the view that kinship norms evolve simultaneously with economic conditions, but theydo so slowly over multiple generations. Finally, while clearly of historical significance, we feel our re-sults might be relevant for contemporary development outcomes, since tight kinship is still prevalentin many societies. While the causal estimates of the of effect of kinship are not directly applicable tosuch societies, our results do suggest that as economies undergo structural transformation, leading tothe development of better institutions, the returns to family structure transitions that weaken kinshipties could potentially be quite high.While the first two chapters, broadly speaking, study the effects of social relations\/integration on eco-nomic outcomes chapter, 4 focuses on political business cycles in the mining industry in India. I study145several aspects of mining intensity (output, licensing and accidents) and find that in contrast to majorityof other economic activities that track the electoral cycle, mining exhibits an inverted U-shaped patternbetween state assembly elections, with the level of activity minimized in election years. I present evi-dence that the magnitude of these cycles are determined primarily by two factors: electoral competitionand the intensity of Naxalite conflict, an ongoing left-wing insurgency against the Indian government.While mining accidents are costly during elections in general, I show that cycles in conflict prone areasare exacerbated in order to minimize the tax base of rebel groups, who thrive on extortion of miningrevenues and target elections with violence. Overall, these results suggest that we might observe a de-coupling of the usual relationship between economic activity and election timing for high-risk industrialactivities or for those that increase the propensity of civil conflict.146BibliographyA.Churchill, S. and M. Danquah (2020). Ethnic diversity and informal work in Ghana. Technical report,WIDER Working Paper.Afridi, F., A. Dhillon, S. X. Li, and S. Sharma (2020). 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Therefore, the religious composi-tion of line-section-level teams was constrained by the overall number of Hindus and Muslims in theline at baseline. Since the proportion of Muslim workers in each line was very close to the overall shareof Muslims in the factory, mixed sections (both HD and LD) ended up with roughly 35%-40% Muslimworkers after randomization.Step 1: Section ShiftingSuppose 2 additional Muslim workers are required in a section to achieve the desired religious com-position (35%-40% Muslims in mixed teams). Then the following steps are taken:a) Randomly order workers within section \u00d7 religion \u00d7 skillb) Find a section with enough Muslimsc) Randomly pick 2 Muslim workers to shift ind) Randomly pick 2 Hindu workers to shift out161This step is perhaps the most crucial in order to achieve the desired line-level treatment types describedin Figure 2.3. At baseline, not all sections of all lines (across all 3 cohorts) had enough Muslim workersto achieve 35%-40% Muslim workers in mixed line-section-level teams post randomization. Therefore,workers were moved across sections in this manner to achieve that. This also meant that only the mini-mum number of workers required were moved, satisfying the firm\u2019s requirement of minimizing section-switching.Step 2: Re-randomizea) Randomly order within new section \u00d7 religion \u00d7 skill levelb) Allocate workers into mixed vs homogeneous teams as pre-specifiedc) Randomly allocate teams (lines) to shifts\/supervisorsIn Step 2, workers were sorted by their new section (only workers who were moved in Step 1 had a dif-ferent section than at baseline), religion and skill and allocated to line-section-level teams (recall thatthere are three teams per section in a line \u2013 one for each shift). The line-section-level teams were thenaggregated to form line-level teams in accordance with two different line-level team structures (treat-ment types), as in Figure 2.3 (i.e HD-Mixed lines or LD-Mixed lines). Finally, the line-level teams wererandomly allocated to the three shifts and the usual weekly shift rotations were introduced. Figure A.1provides a visual representation of these steps.162Figure A.1: Randomized steps (From baseline structure to randomized teams)Step 0: Aggregate workers across all cohorts and       decide the final number of Hindus and Muslims to  be allocated to each section in order to achieve overall line-level team structuresRandomly chosen Muslim workers shifted inLD HD HDLD HD HDLD HD HDLD HD HD    Step 1a: Sort - Section X Religion X SkillSteps 1b, 1c and 1d: Section-Shifting      Step 2a: Sort - New Section X Religion X  Skill             Step 2b: Randomly allocate workers into treatment               (line-section-level teams) to achive desired line-level team types                Step 2c: Randomly allocate desired line-level teams                to shiftsHD-Mixed LineLD-Mixed LineComposition at Baseline (All 3 cohorts)LD HD HD HD-Mixed LineLD HD HDLD HD HDLD HD HDRandomization StepsCohort 1Cohort 2Cohort 3Proportion shaded in each box denotes the share of Muslim workers in the line-section-level team.LDLDLDLDLDLDLDLDRandomly chosen Hindu workers shifted inRandomly chosen Muslim workers shifted inRandomly chosen Hindu workers shifted inNote: This figure illustrates the steps involved in the randomization process \u2013 from how given the religious composition ofsections at baseline the desired line-level team types are achieved. The figure is based on the description of the steps discussedin section A.1.1. A production line with only four sections is considered for simplicity.163A.1.2 Quasi-random allocation of workers to tasks at baselineHiring at the factory occurs on a rolling basis as and when vacancies become available for each positionon a production line. The HR manager always has a pool of job applicants at hand who are called uponon a first-come-first-served basis. As a result, workers do not have the option to choose their area ofwork when they join. It is possible that workers quit at a different rate across the two types of tasks (HDand LD), leading to possible selection bias. However, if that were the case, this would be reflected in theaverage tenure of workers in HD and LD sections. As shown in Table A.5, this is not the case - tenure isbalanced between workers in HD and LD sections.Table A.1: Dependency switchesFirst Job\/Final Job Low-Dependency High-Dependency TotalLow-Dependency 148 35 183High-Dependency 59 344 403Total 207 379 586Note: This matrix reports the number of workers who, from when they firstjoined the factory until before the intervention, switched jobs that also in-volved switching dependencies. 35 workers (5.9%) switched from low- to high-dependency, while 59 workers (10%) switched from high- to low-dependency.While 15.9% of the workers switched jobs at least once, 6.85% of them held oneor more job between their first and final job at the factory.While selection into jobs is therefore unlikely at hiring, it is possible that over time, workers are ableto sort into their sections of choice. In order to assess if that is the case workers were asked to report theirfirst job at the factory and their final job immediately before the intervention began. They were alsoasked to report any other job that they held for a period of more than six months at the factory. Table A.1reports a matrix of job switches between HD and LD sections. Only 94 out of 586 workers (16%) reportedto be currently in jobs that involved switching dependency from their first job. Only 6.85% of the workersreported to switch jobs more than once, whereby majority of the workers who switched jobs did so onlyonce. Additionally, many of these changes resulted from a closure of one production line at the factoryin 2018. As a result, workers from that line were reallocated, typically to similar jobs, in the same shift,but to other existing lines and an additional line which was bought around the same time.164Table A.2: Dependency sorting(1) (2) (3)Switched High to Low Low to HighDependencyAge 0.0040 -0.0029 -0.0011(0.0020) (0.0018) (0.0011)Tenure 0.0016 -0.0040 0.0023(0.0067) (0.0048) (0.0038)Schooling (Highest grade) 0.0046 -0.0024 -0.0022(0.0032) (0.0026) (0.0019)Muslim -0.0070 0.0154 -0.0084(0.0388) (0.0258) (0.0279)Worker SkillSemi-Skilled -0.201 0.288 -0.0867(0.207) (0.175) (0.0509)Operator -0.0423 0.0946** -0.0523(0.0542) (0.0374) (0.0317)Line \u00d7 Section F.E. (First Job) Yes Yes YesN 579 579 579Adj. R2 0.068 0.094 0.284* p<0.10, ** p<0.05, *** p<0.010. The unit of observation is an individual worker. Workers wereasked to report their first job at the factory and their last job before the intervention began. Stan-dard errors clustered at the worker\u2019s first line-section-level. \u201cSwitched Dependency\" refers towhether the move between the first and last job (if any) involved changing dependency as well.Workers were also asked to report if they held any other job in between. Only 7.2 % reported thatthey did. Workers are categorized into the the following skill categories: unskilled, semi-skilled oroperators. Unskilled workers are the omitted group.Overall, this suggests that only a small share of workers switched jobs from when they first joined,until the time of the intervention. This rules out systematic sorting into tasks over time and possibleselection bias resulting from it. Nevertheless, in Table A.2, I test whether observable characteristics ofthe workers are correlated with the probability of moving across task types, based on the few moves thathave occurred, as shown in Table A.1. As observed, none of the factors (age, tenure, schooling, religion)which could potentially affect sorting over time, are statistically significant in Column (1). In Columns(2) and (3), I split up job switches from HD to LD and LD to HD sections. Again, the coefficients on thethe usual factors are small in magnitude and not statistically significant. In Column (2) however, it canbe seen that workers who are currently Operators are likely to have switched from HD to LD tasks at ahigher rate than workers of other skill-levels.165Table A.3: Dependency sorting: Omitting workers shifted from shut productionline(1) (2) (3)Switched High to Low Low to HighDependencyAge 0.0050* -0.0035 -0.0015(0.0022) (0.0021) (0.0016)Tenure -0.0092 0.0035 0.0057(0.0059) (0.0043) (0.0043)Schooling (Highest Grade) 0.0036 -0.0019 -0.0017(0.0034) (0.0028) (0.0021)Muslim -0.0268 0.0051 0.0217(0.0350) (0.0260) (0.0229)Worker SkillSemi-Skilled 0.0455 0.0474 -0.0929(0.0832) (0.0668) (0.0536)Operator 0.0097 0.0570 -0.0668(0.0628) (0.0427) (0.0394)Line \u00d7 Section F.E. (First Job) Yes Yes YesN 470 470 470Adj. R2 0.044 0.000 0.266* p<0.10, ** p<0.05, *** p<0.010. The unit of observation is an individual worker. Workers wereasked to report their first job at the factory and their last job before the intervention began. Stan-dard errors clustered at the worker\u2019s first line-section-level. \u201cSwitched Dependency\" refers towhether the move between the first and last job (if any) involved changing dependency as well.Workers were also asked to report if they held any other job in between. Only 7.2 % reported thatthey did. Workers are categorized into the the following skill categories: unskilled, semi-skilled oroperators. Unskilled workers are the omitted group.Table A.3 shows that this is actually a result of the one-time move of workers from the line that wasshut in 2018. If I leave this set of workers out of the analysis (as in Table A.3), Operators are no more likelyto have switched from HD to LD tasks than other workers. This is understandable since Operators in theline that has now been shut were all in Packing sections, which was a HD section in that line.98 However,Packing sections in the six production lines which are part of this experiment are a combination of bothHD and LD types. As a result, some Operators mechanically moved from HD to LD jobs when this changeoccurred, despite continuing to be Packing Operators in terms of their specific role in the productionline.Table A.4 shows that the share of Muslim workers was balanced across HD and LD tasks after ran-98To determine this I asked supervisors to compare the Packing task in the line that has been shut to Packing tasks in linesthat are currently operative.166domization. This is important to rule out that the different effects of religious mixing in HD and LD tasksare caused by different \u201cdegrees\" of mixing rather than the effects being driven by the production tech-nology. Finally, in Table A.5, I report balance in work characteristics across treatment arms without theinclusion of line \u00d7 section fixed effects. Therefore, unlike in Table 2.3, the main effect of being in HDversus LD section is identified. If workers were able to systematically sort into HD and LD tasks based oncertain observable characteristics, then the main effect of HD versus LD should pick these differencesup. This however is not the case, it can be observed that worker characteristics are balanced betweenHD and LD sections overall.Table A.4: Balance in proportion Muslim(1)Proportion MuslimHD vs LD mixed sections 0.0416(0.0455)Mean Dep. Var. 0.36Line F.E. YesN 56Adj. R2 0.235* p<0.10, ** p<0.05, *** p<0.010. The unit of observation is a line-section. Standard errors clustered at the production line-level. Thistable shows that the proportion of Muslim workers in mixed teams wasbalanced across HD and LD sections after randomization.167Table A.5: Randomization checkPanel A: Outcomes relevant at work Panel B: Other outcomesTenure Muslim co-workers Taking Communicating Age Schooling Trust Altruism Inter-religious cont-Hindus Orders act outside work(1) (2) (3) (4) (5) (6) (7) (8) (9)Mixed 0.0224 0.0144 0.0480 0.0676 1.3496 -0.0283 0.6070 0.0765 0.0368(0.4650) (0.0219) (0.0587) (0.0686) (1.5003) (0.6409) (0.3815) (0.2438) (0.0520)HD -0.5837 0.0187 0.0012 0.0037 1.2019 -0.4931 0.2631 0.1540 0.0148(0.4017) (0.0158) (0.0618) (0.0652) (1.1706) (0.4945) (0.3774) (0.2155) (0.0501)Mixed \u00d7 HD -0.0575 -0.0039 -0.0505 -0.1149 -0.6911 0.4797 -0.6483 -0.0911 -0.0290(0.5627) (0.0286) (0.0879) (0.0881) (1.7033) (0.7258) (0.4823) (0.2781) (0.0654)Mean Dep Var. 4.45 0.12 0.73 0.53 34.47 7.84 3.79 6.65 0.45Production Line F.E. Yes Yes Yes Yes Yes Yes Yes Yes YesReligion F.E. Yes Yes Yes Yes Yes Yes Yes Yes YesN 586 478 586 586 586 586 586 586 586Adj. R2 0.089 0.046 0.008 0.025 0.024 0.021 0.002 0.003 0.109* p<0.10, ** p<0.05, *** p<0.010. The unit of observation is an individual worker. Standard errors clustered at the line-section-level team. \"Tenure\"and \"Schooling\" are measured in years and as highest grade completed respectively. \"Taking Orders\" is a dummy variable coded 1 if the respondentreported to be always comfortable taking orders from non-coreligionists and 0 if they reported to be sometimes or always uncomfortable. \"Commu-nicating\" is coded 1, 0.5 and 0 for the responses \u201cAlways comfortable\u201d, \u201cSometimes uncomfortable\u201d and \u201cAlways uncomfortable\u201d when asked aboutbeing comfortable communicating with non-coreligionists. Survey questions on \u201cTrust\" and \u201cAltruism\" are used from the World Value Survey (WVS).The dependent variable \"Inter-religious contact\" refers to the degree of cross-religion interaction that workers had at baseline, outside of work. Thevariable is coded 1, 0.5 and 0 if a worker mentioned that during the daily course of their life they: 1) interact with more than 5 non-coreligionists 2)interact with 1 to 5 non-coreligionists, or 3) do not interact with anyone outside their religion, respectively.168Table A.6: Randomization check (Line-level treatment indicator)Panel A: Outcomes relevant at work Panel B: General characteristics and attributesTenure Muslim co-workers Taking Communicating Age Schooling Trust Altruism Inter-religious con-Hindus Orders tact outside work(1) (2) (3) (4) (5) (6) (7) (8) (9)HD-Mixed Line vs -0.0471 0.0070 -0.0178 0.0680* -0.2390 0.0147 -0.1808 0.0111 -0.0085LD-Mixed Line (0.4473) (0.0099) (0.0265) (0.0268) (1.1653) (0.2386) (0.3178) (0.1253) (0.0366)Bootstrap [-1.29, 2.13] [-0.025, 0.029] [-0.088, 0.046] [-0.026, 0.156] [-2.522, 3.758] [-0.678, 0.475] [-1.297, 0.544] [-0.292, 0.422] [-0.175, 0.070](Wild Cluster) C.I.Mean Dep. Var 4.41 0.12 0.73 0.47 33.88 7.92 3.88 6.68 0.45Production Line F.E. Yes Yes Yes Yes Yes Yes Yes Yes YesReligion F.E. Yes Yes Yes Yes Yes Yes Yes Yes YesObservations 557 459 557 557 557 557 554 554 557* p<0.10, ** p<0.05, *** p<0.010. The unit of observation is an individual worker. Standard errors clustered at the line-level. \"Tenure\" and \"Schooling\" are measuredin years and as highest grade completed respectively. \"Taking Orders\" is a dummy variable coded 1 if the respondent reported to be always comfortable takingorders from non-coreligionists and 0 if they reported to be sometimes or always uncomfortable. \"Communicating\" is coded 1, 0.5 and 0 for the responses \u201cAlwayscomfortable\u201d, \u201cSometimes uncomfortable\u201d and \u201cAlways uncomfortable\u201d when asked about being comfortable communicating with non-coreligionists. Surveyquestions on \u201cTrust\" and \u201cAltruism\" are used from the World Value Survey (WVS). The dependent variable \"Inter-religious contact\" refers to the degree of cross-religion interaction that workers had at baseline, outside of work. The variable is coded 1, 0.5 and 0 if a worker mentioned that during the daily course of their lifethey: 1) interact with more than 5 non-coreligionists 2) interact with 1 to 5 non-coreligionists, or 3) do not interact with anyone outside their religion, respectively.This sample excludes individuals who work in common sections (\u201cEgg\" and \u201cFlour\") that cater to all production lines, but themselves are not part of any particularline.169A.2 Treatment effect on standard output and output gapSupervisors keep records of standard (expected) output against actual output produced, in each shift foreach line. This measure is based on inputs used in the production process; negative deviations from thestandard level of output imply lower productivity and higher raw material wastage. In Table A.7 (Col-umn 2), I use percentage deviation of actual output from standard output as the outcome variable. Theformula for \u201cOutput Gap\" is ActualOut put\u2212St and ar dOut putSt and ar dOut put \u2217100. The coefficient estimate shows that onaverage, HD-Mixed lines fall short of their expected target by a greater degree than LD-Mixed lines. Thishappens despite the fact that on average HD-Mixed lines receive lower targets (Column 1), though thisdifference is not statistically significant (i.e. the treatment effect on standard output is not significant).This suggests that the treatment effects in Table 2.4 indeed result from under-performance of workers inHD-Mixed lines and are not simply a bi-product of differential target setting across treatment groups.In Figure A.2, I plot histograms of deviation from standard output for each team type. There are acouple of important things to be observed in this figure. First, LD-Mixed lines have lower variance in de-viation from standard output relative to HD-Mixed lines. Second, in HD-Mixed lines, negative deviationsfrom standard output occur with greater frequency. At the same time however, large positive deviationsfrom standard output are not completely unusual. This suggests that religious diversity leads to greateruncertainty (in terms of achieving daily targets) in HD mixed sections relative to LD mixed ones. Adition-ally, this points to the fact that output in mixed teams might be more susceptible to idiosyncratic shocks(religious events, conflict etc.) in HD sections due to the tight-knit nature of intergroup contact. This isformally tested in Table A.8. I generate rolling standard deviation measures of the Output Gap variableand report that standard deviation in Output Gap is higher in HD-Mixed (LD Non-Mixed) lines. I showrobustness to a range of window sizes in generating the rolling standard deviation measures. In FigureA.3, I plot cdfs of deviation of actual output from standard output (by line-level team type) and showthat the probability that actual output is greater than standard output is higher throughout, in LD-Mixedlines.170Table A.7: Treatment effect on line-level standard output(1) (2)Log Standard Output Output GapHD-Mixed vs LD-Mixed Line -0.0223 -1.669***(0.0300) (0.479)Bootstrap Wild cluster C.I. [-0.082, -0.0152] [-3.833, -0.690]Day F.E. Yes YesShift F.E. Yes YesProduction Line F.E. Yes YesN 1045 1019Adj. R2 0.640 0.0488* p<0.10, ** p<0.05, *** p<0.010. Observations are at the line-cohort-daylevel. Standard errors clustered at the line-level team in parenthesis. Wildcluster bootstrap confidence intervals in [] brackets. HD-Mixed Line is adummy coded 1 for a line-level team with all HD sections religiously mixedand LD sections non-mixed, and 0 for exactly the opposite line-level struc-ture (LD-Mixed Line). Standard Output is calculated from the amount of in-puts used (batches mixed) in a shift and is determined before the shift begins.Output Gap gap is a measure of deviation from standard output and is calcu-lated asActualOut put\u2212St and ar dOut putSt and ar dOut put \u2217100.Figure A.2: Percentage deviation from standard outputNote: This figure shows percentage deviation from standard (expected) output for HD-Mixed and LD-Mixed lines. Observationsare at the line-cohort-day level.171Table A.8: Treatment effect on standard deviation of output gapStandard Deviation of Output Gap(1) (2) (3)Rolling Window 10 days 15 days 20 daysMin. Observations 5 10 15HD Mixed vs LD-Mixed Line 0.954 2.784* 3.221**(0.857) (1.358) (1.342)Bootstrap Wild cluster C.I. [-1.38, 3.227] [-1.394, 5.993] [-1.583, 9.907]Shift F.E. Yes Yes YesProduction Line F.E. Yes Yes YesDay F.E. Yes Yes YesMean Dep Var. 4.77 5.00 5.34(7.01) (6.89) (6.84)N 755 404 231Adj. R2 0.374 0.552 0.668* p<0.10, ** p<0.05, *** p<0.010. Observations are at the line-cohort-day level. Stan-dard errors clustered at the line-level team in parenthesis. Wild cluster bootstrap(Cameron et al., 2008) confidence intervals in square brackets. HD-Mixed Line is adummy coded 1 for a line-level team with all HD sections religiously mixed and LD sec-tions non-mixed, and 0 for exactly the opposite line-level structure (LD-Mixed Line).Rolling Window refers to the number of consecutive production days used to gener-ate the standard deviation measure. Min. observations denote the lower bound on thenumber of observations in each window.Figure A.3: Deviation from standard outputNote: This figure presents CDFs of the \u201cOutput Gap\" measure (which is defined as the percentage deviation from expectedoutput) by line-level team type. HD-Mixed lines fall short of expected output with higher probability than LD-Mixed lines.172A.3 Additional tables referred to in the main textA.3.1 Summary statisticsTable A.9 presents summary statistics of key characteristics of Hindu and Muslim workers described insection 2.2.Table A.9: Summary statistics: Hindu and Muslim workersVariable Hindu Muslim Diff (2) - (1)Panel A: DependencyHigh Dependency (share of workers) 0.610 0.660 0.048(0.02) (0.05) (0.052)Panel B: Schooling and TenureSchooling (Grade) 8.08 6.83 -1.250***(0.16) (0.34) (0.370)Tenure 4.81 2.75 -2.059***(0.15) (0.28) (0.353)Panel C: Cross-religion interaction and attitudesCross-religion interaction (outside work) 0.39 0.73 0.343***(0.02) (0.03) (0.040)Comfortable taking orders from non-coreligionists 0.73 0.76 0.032(0.02) (0.040) (0.047)Would live next door to non-coreligionists 0.57 0.88 0.307***(0.02) (0.02) (0.038)Equally comfortable communicating with non-coreligionists 0.49 0.68 0.191***(0.02) (0.04) (0.047)Panel D: PoliticalSupports National Registrar of Citizens (NRC) 0.32 0.19 -0.132***(0.02) (0.04) (0.049)N 480 106 586Panel E: SkillProportion Semi-skilled\/Operator 0.22 0.16 -0.064(0.02) (0.03) (0.041)N 575 116 691* p<0.10, ** p<0.05, *** p<0.010. Standard errors in parentheses. \"Cross-religion interaction (outsidework)\" is a categorical variable coded 1, 0.5 and 0 if an individual reported to come in contact with greaterthan 5, between 1 and 5 or 0 non-coreligionists respectively in their daily life outside of work. \"Comfort-able taking orders from non-coreligionists\" is a dummy variable coded 1 if the respondent reported to bealways comfortable taking orders from non-coreligionists and 0 if they reported to be sometimes or alwaysuncomfortable. \"Equally comfortable communicating with non-coreligionists\" is coded 1, 0.5 and 0 for theresponses \u201cAlways comfortable\u201d, \u201cSometimes uncomfortable\u201d and \u201cAlways uncomfortable\u201d respectively.The number of workers interviewed at baseline is larger than the number of workers that actually par-ticipated in the study. This is because the firm decided to lay off some workers after the baseline survey(but before the intervention began) due to low product demand in two of the production lines (which iswhy there are only 15 line-level teams). The table includes only those that were part of the experiment(except for the data on worker-skill).173Table A.10 presents summary statistics of key aspects of the physical environment of HD and LDsections. Please refer to section 2.2 for a detailed description of this table.Table A.10: Summary statistics: Mean differences (physical environment)Variable Low-Dependency High-Dependency Diff (2) - (1)Panel A: Interaction (Minutes out of 10)Direct Dependency 2.22 9.50 7.283***(0.63) (0.11) (0.688)Non-work interaction 0.89 1.14 0.249(0.22) (0.25) (0.329)Panel B: Noise Level (Decibels)Avg Noise (Db) 78.47 77.53 -0.941(1.42) (1.66) (2.170)Max Noise (Db) 87.46 85.40 -2.055(1.72) (1.65) (2.394)Panel C: Temperature (Celsius)Section Temperature (\u00b0C) 29.08 31.42 2.341*(0.92) (0.72) (1.197)N 22 20 42* p<0.10, ** p<0.05, *** p<0.010. This table reports mean differences in characteris-tics of HD and LD tasks. In some cases, certain sections can have more than one task,with their degrees of dependency highly correlated. Sections are classified based onthe average dependency minutes in each section.174A.3.2 Robustness checks and additional resultsTable A.11: Treatment effect on output (Line\u00d7 Variety fixed effects)(1) (2)Log Output (Pieces) Log Output (Boxes)HD-Mixed vs LD-Mixed Line -0.0473*** -0.0552***(0.0137) (0.0121)Bootstrap Wild cluster C.I. [-0.082, -0.0152] [-0.080, -0.021]Day F.E. Yes YesShift F.E. Yes YesProduction Line \u00d7 Variety F.E. Yes YesMean Dep Var 10.80 6.97(1.24) (0.943)N 1045 1045Adj. R2 0.885 0.851* p<0.10, ** p<0.05, *** p<0.010. Observations are daily output produced by line-level teams. Standard errors clustered at the line-level team in parenthesis. Wildcluster bootstrap confidence intervals in square brackets. HD-Mixed Line is adummy coded 1 for a line-level team with all HD sections religiously mixed andLD sections non-mixed, and 0 for exactly the opposite line-level structure (LD-Mixed Line).Table A.12: Treatment effect on output (Line \u00d7 Day fixed effects)(1) (2)Log Output (Pieces) Log Output (Boxes)HD-Mixed Line (LD Non-Mixed) -0.0520** -0.0546*(0.0185) (0.0264)Bootstrap Wild cluster C.I. [-0.092, -0.005] [-0.111, 0.012]Shift F.E. Yes YesProduction Line \u00d7 Day F.E. Yes YesMean Dep. Var. 10.80 6.27(1.24) (0.943)N 1045 1045Adj. R2 0.900 0.827* p<0.10, ** p<0.05, *** p<0.010. Observations are daily output produced by line-level teams. Standard errors clustered at the line-level team in parenthesis. Wildcluster bootstrap confidence intervals in square brackets. HD-Mixed Line is adummy coded 1 for a line-level team with all HD sections religiously mixed and LDsections non-mixed, and 0 for exactly the opposite line-level structure (LD-MixedLine).175Table A.13: Treatment effect on section ratingsHD Sections LD SectionsRating Rating > Median Rating Rating > Median(1) (2) (3) (4)Mixed -0.0496*** -0.0499*** -0.0005 -0.0024(0.0184) (0.0113) (0.0142) (0.0124)Mean Dep. Var. 3.86 0.47 3.81 0.41(0.68) (0.50) (0.64) (0.49)Education and Tenure Controls Yes Yes Yes YesDay F.E. Yes Yes Yes YesShift F.E. Yes Yes Yes YesLine \u00d7 Section F.E. Yes Yes Yes YesN 3466 3466 3443 3443Adj. R2 0.609 0.385 0.595 0.324* p<0.10, ** p<0.05, *** p<0.010. Observations are daily ratings received by line-section-level teams. Standard errors clustered at the line-section-level team. \u201cMixed\" is a dummyvariable coded 1 if the line-section-level team is religiously mixed. Education and tenurecontrol for the mean of schooling and tenure of workers in the line-section-level team.In this table, the sample is split into HD and LD sections and it can be observed thatwhile religious mixing leads to lower ratings in HD sections, the effects are small and notstatistically significant in LD.176Table A.14: Treatment effect on section ratings (without controls collinear withreligion)Rating (Raw) Rating>Median(1) (2) (3) (4)Mixed -0.0239** -0.0245***(0.0114) (0.00846)Mixed \u00d7 LD -0.0084 -0.0040(0.0150) (0.0126)Mixed \u00d7 HD -0.0394** -0.0449***(0.0175) (0.0113)p(Mixed \u00d7 HD = Mixed \u00d7 LD) 0.184 0.017Mean Dep. Var. 3.82 3.82 0.44 0.44(0.83) (0.83) (0.50) (0.50)Education and Tenure Controls No No No NoDay F.E. Yes Yes Yes YesShift F.E. Yes Yes Yes YesLine \u00d7 Section F.E. Yes Yes Yes YesN 6909 6909 6909 6909Adj. R2 0.600 0.600 0.358 0.358* p<0.10, ** p<0.05, *** p<0.010. Observations are daily ratings received by line-section-levelteams. Standard errors clustered at the line-section-level team. \u201cMixed\" is a dummy variablecoded 1 if the line-section-level team is religiously mixed. Line \u00d7 Sections fixed effects are in-cluded in the all specifications; as a result the main effect of HD versus LD is not separately iden-tified in columns (2) and (4). Education and tenure control for the mean of schooling and tenureof workers in the line-section-level team.177Table A.15: Treatment effect on section ratings: Event studyRaw RatingsHD Sections LD Sections(1) (2) (3) (4)Mixed -0.0496*** -0.0005(0.0184) (0.0142)Mixed \u00d7 0-25 days -0.1050* 0.0525(0.0675) (0.0615)Mixed \u00d7 26-50 days -0.0716** -0.1030(0.0355) (0.0724)Mixed \u00d7 51-75 days 0.0279 -0.0134(0.0340) (0.0400)Mixed \u00d7 76-100 days -0.0647** 0.0579*(0.0319) (0.0286)Mixed \u00d7 101-120 days -0.0247 -0.0542(0.0532) (0.0446)Mean Dep. Var. 3.85 3.85 3.80 3.80(0.68) (0.68) (0.64) (0.64)Education and Tenure Controls Yes Yes Yes YesDay F.E. Yes Yes Yes YesShift F.E. Yes Yes Yes YesLine \u00d7 Section F.E. Yes Yes Yes YesN 3466 3466 3443 3443Adj. R2 0.609 0.609 0.595 0.596* p<0.10, ** p<0.05, *** p<0.010. Observations are daily ratings received by line-section-level teams.Standard errors clustered at the line-section-level team. \u201cMixed\" is a dummy variable coded 1 if the line-section-level team is religiously mixed. Line \u00d7 Sections fixed effects are included in the all specifications;as a result the main effect of HD versus LD is not separately identified. Education and tenure controlfor the mean of schooling and tenure of workers in the line-section-level team. This table is based onspecification 2.2; interactions of \u201cMixed\" with day bins are added.178Table A.16: Treatment effect on worker interactions: Hindus respondentsonlyIdentified teammate as Blamed Unwilling to give upcontributing low effort by teammate relief time(1) (2) (3) (4) (5) (6)Mixed 0.0399*** 0.0393** 0.0565(0.0139) (0.0165) (0.0369)Mixed \u00d7 LD 0.0309 0.0656** 0.0317(0.0274) (0.0260) (0.0636)Mixed \u00d7 HD 0.0421*** 0.0330* 0.0631(0.0159) (0.0191) (0.0441)p(Mixed \u00d7 LD = Mixed \u00d7 HD) 0.665 0.282 0.573Mean. Dep. Var. 0.14 0.14 0.08 0.08 0.24 0.24Worker skill F.E. Yes Yes Yes Yes Yes YesLine \u00d7 Section F.E. Yes Yes Yes Yes Yes YesN 3020 3020 3009 3009 3056 3056Adj. R2 0.015 0.015 0.013 0.013 0.079 0.079** p<0.10, ** p<0.05, *** p<0.010. Observations are at the worker-teammate level for line-section-level teams i.e. there are (N-1) observations per worker, where N denotes the numberof workers in the section. Standard errors clustered at the line-section-level team. Workerswere asked to choose teammates who they: (1) think have not contributed sufficient effort atany point during the intervention (2) have been blamed by during the intervention and (3)would give (or already have) up their relief time for.179Table A.17: Treatment effect on section ratings: Adding key controlsRating (Raw)(1) (2) (3) (4)Mixed \u00d7 LD -0.0068 -0.0210 -0.122** -0.173***(0.0144) (0.0179) (0.0507) (0.0603)Mixed \u00d7 HD -0.0349** -0.0609** -0.164*** -0.216***(0.0185) (0.0264) (0.0522) (0.0614)Mixed \u00d7 Group Size 0.0040 0.0078** 0.0067*(0.0034) (0.0038) (0.0040)Mixed \u00d7 Tenure 0.0169** 0.0119(0.0075) (0.0085)Mixed \u00d7 Schooling 0.0102(0.0072)p(Mixed \u00d7 HD = Mixed \u00d7 LD) 0.229 0.112 0.069 0.075Mean Dep. Var. 3.82 3.82 3.82 3.82(0.83) (0.83) (0.83) (0.83)Education and Tenure Controls Yes Yes Yes YesDay F.E. Yes Yes Yes YesShift F.E. Yes Yes Yes YesLine \u00d7 Section F.E. Yes Yes Yes YesN 6909 6909 6909 6909Adj. R2 0.600 0.600 0.600 0.600* p<0.10, ** p<0.05, *** p<0.010. Observations are daily ratings received by line-section-levelteams. Standard errors clustered at the line-section-level team. \u201cMixed\" is a dummy variablecoded 1 if the line-section-level team is religiously mixed. Line \u00d7 Sections fixed effects are in-cluded in the all specifications; as a result the main effect of HD versus LD is not separatelyidentified. Education and tenure control for the mean of schooling and tenure of workers inthe line-section-level team.180Table A.18: Proportion of old teammatesProportion of old teammates(1) (2)Mixed -0.0115(0.0163)Mixed \u00d7 LD -0.0312(0.0321)Mixed \u00d7 HD -0.0006(0.0193)p(Mixed \u00d7 HD = Mixed \u00d7 LD) 0.442Mean Dep. Var. 0.34 0.34Religion F.E. Yes YesLine \u00d7 Section F.E. Yes YesN 577 577Adj. R2 0.599 0.600* p<0.10, ** p<0.05, *** p<0.010. The unit of observation is an individual worker.Standard errors clustered at the line-section-level team. The outcome variable inthese regressions is the share of co-workers in each individual\u2019s line-section-levelteam that were also in their team at baseline. \u201cMixed\" is a dummy variable coded1 if the line-section-level team is religiously mixed. Line \u00d7 Sections fixed effects areincluded in the all specifications; as a result the main effect of HD versus LD is notseparately identified in column (2).Table A.19: Section change and treatment statusChanged Section(1) (2) (3) (4)Mixed -0.0338 -0.0288(0.0277) (0.0249)Mixed \u00d7 LD -0.0353 0.0188(0.0538) (0.0351)Mixed \u00d7 HD -0.0329 -0.0551*(0.0361) (0.0322)Mean Dep. Var. 0.079 0.079 0.079 0.079Religion F.E. Yes Yes Yes YesLine \u00d7 Section F.E. No Yes No YesLine \u00d7 Old Section F.E. Yes No Yes NoN 586 586 586 586Adj. R2 0.043 0.030 0.041 0.033* p<0.10, ** p<0.05, *** p<0.010. The unit of observation is an individual worker.Standard errors clustered at the line-section-level team. \u201cMixed\" is a dummy vari-able coded 1 if the line-section-level team is religiously mixed. Line \u00d7 Sections fixedeffects are included in the all specifications; as a result the main effect of HD versusLD is not separately identified in columns (3) and (4). These are individual worker-level regressions. The outcome variable is a dummy coded 1 if after the randomiza-tion process the worker was in a different section (task) than their section of work atbaseline.181Table A.20: Heterogeneous attenuation by characteristics of Hindus at baseline (LD section ratings)Sample: Full Contact at Baseline Tenure at Baseline Support for BJP and NRC(1) (2) (3) (4) (5) (6) (7)Above Median Below Median Above Median Below Median Above Median Below MedianMixed \u00d7 0-60 days -0.0157 -0.0034 -0.0542 -0.0020 -0.0436 -0.0286 0.0086(0.0376) (0.0542) (0.0538) (0.0598) (0.0511) (0.0499) (0.0459)Mixed \u00d7 61-120 days 0.0117 -0.0499 0.0467 0.0038 -0.0079 0.0088 -0.0194(0.0233) (0.0413) (0.0360) (0.0318) (0.0326) (0.0289) (0.0382)Mean Dep. Var 3.81 3.74 3.87 3.86 3.74 3.8 3.82Education and Tenure Controls Yes Yes Yes Yes Yes Yes YesDay F.E. Yes Yes Yes Yes Yes Yes YesShift F.E. Yes Yes Yes Yes Yes Yes YesLine \u00d7 Section F.E. Yes Yes Yes Yes Yes Yes YesObservations 3443 1607 1836 1945 1498 2430 1013Adj. R2 0.595 0.622 0.563 0.584 0.606 0.588 0.614* p<0.10, ** p<0.05, *** p<0.010. Observations are daily ratings received by line-section-level teams. Standard errors clustered at the line-section-level team. \u201cMixed\" is a dummy variable coded 1 if the line-section-level team is religiously mixed. In column (2), the sample consistsof all line-section-level teams in which the share of Muslim teammates, that Hindus in that team had at baseline, is above median. In column(3), the sample consists of all line-section-level teams in which the share of Muslim teammates, that Hindus in that team had at baseline,is below median. In columns (4) and (5) teams are split by median tenure of Hindus at baseline. In column (6), the sample consists of allline-section-level teams with above median support for the BJP or the NRC (averaged across all Hindu workers in the team). In Column (6),the sample consists of all line-section-level teams with below median support for the BJP or the NRC (averaged across all Hindu workers inthe team).182Table A.21: Treatment effect on worker interactions: Decomposition (Mixed teamsby dependency)Identified teammate as Blamed Unwilling to give upcontributing low effort by teammate relief time(1) (2) (3) (4) (5) (6)Panel A: HD SectionsTarget Muslim 0.0711*** 0.0987*** -0.0139 0.0056 0.0534** 0.0325(0.0185) (0.0276) (0.0145) (0.0360) (0.0215) (0.0410)Respondent Muslim -0.0202 0.0053 -0.0147 0.0081 -0.0423 -0.0620(0.0274) (0.0328) (0.0255) (0.0252) (0.0408) (0.0438)Target Muslim \u00d7 -0.0829 -0.0656 0.0624Respondent Muslim (0.0609) (0.0495) (0.0815)Mean Dep. Var. 0.16 0.16 0.09 0.09 0.31 0.31N 1576 1576 1584 1584 1568 1568Adj. R2 0.023 0.025 0.019 0.021 0.107 0.107Panel B: LD SectionsTarget Muslim 0.0008 0.0502* 0.0392* 0.0672* 0.0290 -0.0635*(0.0276) (0.0284) (0.0205) (0.0371) (0.0291) (0.0321)Respondent Muslim -0.0080 0.0462 -0.0196 0.0055 0.0505 -0.1538***(0.0336) (0.0382) (0.0250) (0.0357) (0.0386) (0.0290)Target Muslim m \u00d7 -0.1443** -0.0726 0.2665***Respondent Muslim (0.0512) (0.0628) (0.0754)Mean Dep. Var 0.13 0.13 0.12 0.12 0.19 0.19N 457 457 445 445 467 467Adj. R2 0.01 0.02 0.01 0.01 -0.01 0.02* p<0.10, ** p<0.05, *** p<0.010. Observations are at the worker-teammate level for line-section-levelteams i.e. there are (N-1) observations per worker, where N denotes the number of workers in thesection. Standard errors clustered at the line-section-level team. Workers were asked to choose team-mates who they: (1) think have not contributed sufficient effort at any point during the intervention (2)have been blamed by during the intervention and (3) would give (or already have) up their relief timefor. All regressions include Worker skill F.E. and Line \u00d7 Section F.E.183Table A.22: Religious violence and section ratingsHD Sections LD Sections(1) (2) (3) (4)Mixed -0.0496*** -0.0006(0.0184) (0.0142)Mixed \u00d7 No Violence -0.0466** 0.0112(0.0190) (0.0164)Mixed \u00d7 Violence -0.0749** -0.0951**(0.0376) (0.0434)p(Mixed \u00d7 No Violence = Mixed \u00d7 Violence) 0.457 0.038Mean Dep. Var. 3.86 3.86 3.81 3.81(0.68) (0.68) (0.64) (0.64)Education and Tenure Controls Yes Yes Yes YesDay Effects Yes Yes Yes YesShift Effects Yes Yes Yes YesLine \u00d7 Section Effects Yes Yes Yes YesN 3466 3466 3443 3443Adj. R2 0.609 0.609 0.595 0.595* p<0.10, ** p<0.05, *** p<0.010. Observations are daily ratings received by line-section-level teams.Standard errors clustered at the line-section-level team. \u201cMixed\" is a dummy variable coded 1 if theline-section-level team is religiously mixed. Line\u00d7 Sections fixed effects are included in the all specifi-cations; as a result the main effect of HD versus LD is not separately identified. Education and tenurecontrol for the mean of schooling and tenure of workers in the line-section-level team. Between 13th-18th December 2019, immediately after the passing of the Citizenship Amendment Act (CAA) violentprotests erupted in the district of West Bengal where the factory is located. Hindu-Muslim riots oc-curred in Delhi between 23rd-28th Feb 2020 during protests against the CAA as well. These days arecoded as violent days in these regressions.Table A.23: Treatment effect on line-level performance(aggregated section ratings)Raw Rating Rating > Median(1) (2)HD-Mixed vs LD-Mixed Line -0.0126 -0.0224**(0.0200) (0.0118)Bootstrap (Wild Cluster) C.I. [-0.072, 0.038] [-0.061, 0.005]Day F.E. Yes YesShift F.E. Yes YesProduction Line F.E. Yes YesMean Dep. Var 3.87 0.47N 1012 1012Adj. R2 0.734 0.621* p<0.10, ** p<0.05, *** p<0.010. The dependent variable is dailyline-section-level team ratings aggregated to line-level teams (averagingacross all sections). Standard errors clustered at the line-level team inparenthesis. Wild cluster bootstrap (Cameron et al., 2008) confidenceintervals in square brackets. HD-Mixed Line is a dummy coded 1 for aline-level team with all HD sections religiously mixed and LD sectionsnon-mixed, and 0 for exactly the opposite line-level structure (LD-MixedLine).184Table A.24: Inter-religious contact (outside work) and section ratingsHD Sections LD Sections(1) (2) (3) (4)Mixed -0.0496*** -0.0236 -0.0006 0.0121(0.0184) (0.0409) (0.0142) (0.0217)Inter-religious contact (outside work) 0.0092 0.0165(0.0749) (0.0466)Mixed \u00d7 Inter-religious contact (outside work) -0.0621 -0.0365(0.0948) (0.0567)Mean Dep. Var. 3.86 3.86 3.81 3.81Education and Tenure Controls Yes Yes Yes YesDay Effects Yes Yes Yes YesShift Effects Yes Yes Yes YesLine \u00d7 Section Effects Yes Yes Yes YesN 3466 3466 3443 3368Adj. R2 0.609 0.609 0.595 0.595* p<0.10, ** p<0.05, *** p<0.010. Observations are daily ratings received by line-section-level teams.Standard errors clustered at the line-section-level team. \u201cMixed\" is a dummy variable coded 1 if theline-section-level team is religiously mixed. Line\u00d7 Sections fixed effects are included in the all specifi-cations; as a result the main effect of HD versus LD is not separately identified. Education and tenurecontrol for the mean of schooling and tenure of workers in the line-section-level team. \"Inter-religiouscontact\" refers to the degree of cross-religion interaction that workers had at baseline, outside of work.The variable is coded 1, 0.5 and 0 if a worker mentioned that during the daily course of their life they:1) interact with more than 5 non-coreligionists 2) interact with 1 to 5 non-coreligionists, or 3) do notinteract with anyone outside their religion, respectively. For these regressions the average value of thisvariable across all Hindus in a line-section-level team is used.Table A.25: AttritionAttrited Attrited(1) (2)Mixed -0.0164(0.0223)Mixed \u00d7 LD 0.0069(0.0279)Mixed \u00d7 HD -0.0292(0.0296)p(Mixed X HD = Mixed X LD) 0.35Mean Dep. Var 0.05 0.05Religion Effects Yes YesLine \u00d7 Section Effects Yes YesObservations 586 586* p<0.10, ** p<0.05, *** p<0.010. The unit of observation is an in-dividual worker. The outcome variable is coded 1 for individualswho left the firm before the end of the experiment. Note that thetotal number of workers who left the firm is actually lower thanthe number interviewed at endline. A handful of workers couldnot be reached by phone during the endline survey.A.3.3 SpilloversOne concern with the analysis of the treatment effects on output is that there could be spillover effectsfrom upstream to downstream sections, potentially biasing my estimates (even though supervisors tried185to each section based solely on it\u2019s performance). To understand how this could affect the main findings,I restrict attention to the following two sub-samples (as shown in Figure A.4)1. Only the first two sections of every line (black dashed-dotted portion)2. Lines where all HD sections come after all LD sections (blue dashed portion)Figure A.4: Sub-sample analysisHigh DepedendencyLine 3Line 5Mixing (4) Deposit (11) Oven (2) Tray\/Cooling (4) Depanning (4) Cfc (5)Deposit (10) Oven (2) Injector (3) Depanning (11) Packing (4) Cfc (5)Mixing (2) Oven (2) Cooling (5) Packing (6) Cfc (3)Mixing (3) Oven (3) Cream (6) Packing (5) Box Machine (2)Box FIlling (14) Cfc (5)Mixing (3) Oven (3) Cream (6) Packing (5) Box Machine (2)Box FIlling (14) Cfc (5)Line 1Line 2Line 6Line 4Mixing (3) 1st Line (3) 2nd Line (12) Oven (2) Tray Wash (4) Injector (3) Depanning (4) Packing (4) Cfc (11)f ( )Packing (8)Mixing (3)Low DepedendencyNote: This figure shows all sections of all lines at the factory split into HD and LD types. Direct Dependency is measured asdescribed in section 2.2.3. The two relevant sub-samples used for analysis in this section are highlighted by the black dashed-dotted lines and blue dashed lines.With sub-sample 1, I first show that there is no effect of religious mixing in the first section which isalways a low-dependency section (and by definition cannot be affected by spillovers) (see columns (1)and (2) of Table A.26.). This is consistent with the main results. Furthermore, this suggests that religiousmixing is unlikely to cause differential spillover effects from the first section to the second based ontreatment status. Finally, once the second section of each line is added to the sample, the main sectionlevel results (Table 2.5) are replicated \u2013 the magnitude of the effects are also very similar.186Table A.26: Treatment effect on line-section-level ratingsOnly first section (Mixing, only LD) First two sectionsRatings Ratings > Median Ratings Ratings > Median(1) (2) (3) (4)Mixed \u00d7 LD -0.0033 0.0085 -0.0082 -0.0032(0.0396) (0.0260) (0.0299) (0.0206)Mixed \u00d7 HD -0.0318 -0.0461***(0.0373) (0.0131)p(Mixed X HD = Mixed X LD) 0.63 0.09Mean Dep. Var 3.74 3.74 3.74 3.74Day Effects Yes Yes Yes YesShift Effects Yes Yes Yes YesLine \u00d7 Section Effects Yes Yes Yes YesObservations 964 964 1929 1929* p<0.10, ** p<0.05, *** p<0.010. Observations are daily ratings received by line-section-level teams. Standarderrors clustered at the line-section-level team. \u201cMixed\" is a dummy variable coded 1 if the line-section-levelteam is religiously mixed. Line\u00d7 Sections fixed effects are included in the all specifications; as a result the maineffect of HD versus LD is not separately identified in columns (2) and (4). Education and tenure control for themean of schooling and tenure of workers in the line-section-level team.In Table A.27, I show that the main results are replicated with sub-sample 2 as well. This sampleis unique in the sense that it only has production lines where all the HD sections come after the LDsections. I once again find that there is no effect of religious mixing in LD sections. The HD sections atthe end of the line are therefore unlikely to be affected differentially by spillovers from LD sections (basedon whether they are religiously mixed or not). In HD sections, a negative, large and statically significanteffect of religious mixing can still be observed. Taken together, the sub-sample analysis is re-assuringin that they convey the same findings as the core results \u2014 which is that religious mixing leads to lowerteam performance but only in HD tasks.How should we expect line-section-level spillovers to affect the overall line-level treatment effectestimates (Table 2.4)? Notice that on average production lines have LD sections earlier in the line whileHD sections come later. For the line-level effects to be overestimated (in other words the difference inoutput between HD-Mixed lines and LD-Mixed lines to be more negative than it actually is), it mustbe the case that there are larger negative spillovers from LD Non-mixed sections to HD-Mixed sectionsthan from LD-Mixed sections to HD Non-Mixed sections, which is unlikely. Therefore, if anything, theline-level results are likely to be underestimated.187Table A.27: Treatment effect on section ratings (HD af-ter LD)Ratings Ratings(1) (2)Mixed -0.0391*(0.0195)Mixed \u00d7 LD -0.0042(0.0263)Mixed \u00d7 HD -0.0898***(0.0317)p(Mixed X HD = Mixed X LD) 0.05Mean Dep. Var. 3.93 3.93Day Effects Yes YesShift Effects Yes YesLine \u00d7 Section Effects Yes YesObservations 1799 1799* p<0.10, ** p<0.05, *** p<0.010. Observations are daily ratings receivedby line-section-level teams. Standard errors clustered at the line-section-level team. \u201cMixed\" is a dummy variable coded 1 if the line-section-levelteam is religiously mixed. Line \u00d7 Sections fixed effects are included in theall specifications; as a result the main effect of HD versus LD is not sep-arately identified in columns (2) and (4). Education and tenure controlfor the mean of schooling and tenure of workers in the line-section-levelteam.A.4 Additional figures referred to in the main textFigure A.5: Structure of production linesLine 3Line 4Line 5Mixing (4) Deposit (11) Oven (2) Tray\/Cooling (4) Depanning (4) Packing (8) Cfc (5)Mixing (3) Deposit (10) Oven (2) Injector (3) Depanning (11) Packing (4) Cfc (5)Mixing (3) 1st Line (3) 2nd Line (12) Oven (2) Tray Wash (4) Inject (3) Depanning (4) Packing (4) Cfc (11)Mixing (2) Oven (2) Cooling (5) Packing (6) Cfc (3)Mixing (3) Oven (3) Cream (6) Packing (5) Box Machine (2)Box FIlling (14) Cfc (5)Mixing (3) Oven (3) Cream (6) Packing (5) Box Machine (2)Box FIlling (14) Cfc (5)Line 1Line 2Line 6Note: This figure shows the structure of all six production lines in the factory. The numbers in parentheses denote the count ofworkers in each section per cohort. Each production line has three cohorts working on it in each of the three shifts in a day.188Figure A.6: High- and Low-Dependency sectionsHigh DepedendencyLine 3Line 5Mixing (4) Deposit (11) Oven (2) Tray\/Cooling (4) Depanning (4) Cfc (5)Deposit (10) Oven (2) Injector (3) Depanning (11) Packing (4) Cfc (5)Mixing (2) Oven (2) Cooling (5) Packing (6) Cfc (3)Mixing (3) Oven (3) Cream (6) Packing (5) Box Machine (2)Box FIlling (14) Cfc (5)Mixing (3) Oven (3) Cream (6) Packing (5) Box Machine (2)Box FIlling (14) Cfc (5)Line 1Line 2Line 6Line 4Mixing (3) 1st Line (3) 2nd Line (12) Oven (2) Tray Wash (4) Injector (3) Depanning (4) Packing (4) Cfc (11)f ( )Packing (8)Mixing (3)Low DepedendencyNote: This figure shows all sections of all lines at the factory split into HD and LD types. Direct Dependency is measured asdescribed in section 2.2.3.189Figure A.7: Religious composition of lines and cohorts at baseline-.3-.2-.10.1.2Coefficient on Hindu DummyLine 1 Line 2 Line 3 Line 4 Line 5 Line 6 Egg FlourReligious Composition of Production Lines at Baseline(a) This figure plots coefficients from worker-level regressions. Theoutcome variable is a dummy coded 1 if the religion of the worker isHindu and the independent variables are a set of dummy variablesdenoting each production line. \u201cEgg\" and \u201cFlour\" refer to productionareas where raw materials (eggs and flour) are processed. These pro-duction areas are common to all production lines.-.1-.050.05.1Coefficient on Hindu DummyCohort 1 Cohort 2 Cohort 3Religious Composition of Cohorts at Baseline(b) This figure plots coefficients from worker-level regressions. Theoutcome variable is a dummy coded 1 if the religion of the worker isHindu and the independent variables are dummies denoting cohorts(groups of workers who work at the factory at the same time).190Figure A.8: High- and Low-Dependency tasks(a) High-Dependency ( b) Low-DependencyNote: This figure illustrates some key differences between HD and LD tasks. Sub-figure (a) is an example of a HD task. Workersare stood next to each other beside a fast moving conveyor belt. As a group they have to ensure each individual product is putinto small packets before they go onto the next stage of production. If the team cannot coordinate and ensure the same, thesupervisor has to reduce the speed of the belt to prevent wastage, which in turn would reduce output. Sub-figure (b) is a picturefrom a mixing room, which is a LD task. One worker is using the weighing scale to weigh raw materials, a second worker isarranging flour buckets and finally a third worker is operating the mixing machine. These workers have to coordinate as well tocomplete the process, but the frequency of interaction is intermittent and the degree of coordination is much lower relative tothe HD task.191Figure A.9: Treatment effect on standard output (Event study)Note: This figure is generated from binned regressions using exactly the same controls variables as in Table 2.4. The treatmentperiod is divided into 5 equal sized bins. The outcome variable is standard output (logged), which denotes the expected amountof output given inputs used.Figure A.10: Distribution of actual line output and section ratingsNote: This figure presents the distribution of raw ratings given by production supervisors to line-section-level teams aggregatedup to the line-level as well as actual log output at the line-level.192Figure A.11: Line output and section ratings1010.51111.5Log Output2 2.5 3 3.5 4 4.5Mean Rating Across all SectionsNote: Production line fixed effects are included in this binscatter plot. The variable on the y-axis is daily output (logged) pro-duced by a line-level team, and on the x-axis it is the average value of supervisor ratings received by sections in that line-levelteam.Figure A.12: Correlating IAT scores with survey responsesNote: This figure correlates Implicit Association Test scores (where workers were asked to associate Hindu and Muslim nameswith positions in the firm\u2019s hierarchy) with self-reported survey outcomes of the workers. In the top two figures, the outcomevariable on the y-axis is willingness to take orders from non-coreligionists, while in the bottom two figures it is the workers\u2019reported level of comfort in communicating with non-coreligionists. Positive IAT scores denote a bias towards having Hindusin higher positions while a negative value denotes a bias towards Muslims.193A.4.1 Figures from firm surveyFigure A.13: Characteristics of HD and LD tasksNote: This figure reports the percentage of respondents who picked each option for the following questions: (1) respondentswere asked to pick the task that they thought requires greater continuous coordination and communication amongst workers(blue dots), and (2) they were to pick the one that is likely to cause more frictions and arguments amongst workers (pink dots).Figure A.14: Religious mixing and productivity by task typeNote: This figure reports supervisors\u2019 perception of which type of team (religiously homogeneous or mixed) would be moreproductive in HD vs LD tasks. It reports percentage of respondents who picked each option when they were asked whether areligiously mixed or a homogeneous team would be more productive separately for HD (blue dots) and LD tasks (pink dots).194Figure A.15: Willingness to segregate workers by religion\/ageNote: This figure presents responses of supervisors when asked if they are willing to segregate workers based on certain demo-graphic dimensions. Percentage of respondents who chose each option for age and religion are denoted by pink dots and bluedots respectively.195Appendix BAppendix to Chapter 3B.1 Marriage recordsOur marriages dataset consists of marriage records, mostly from local governments or church parishes,which have been transcribed and made available online by Family- Search. We retrieved this data for allUS states between 1800 and 1940. Most states that banned cousin marriage did so over this period. Anexample of a marriage certificate is shown in Figure B.1.Figure B.1: Marriage certificateSource: familysearch.com196The transcribed marriage records typically include the following information: names of both spouses,their age, and location and date of marriage. The transcribed records often contain duplicates. We con-sidered observations to be duplicates if the names of both spouses, location and date of marriage wereexactly the same and dropped these from our analysis. However, despite this, our dataset is likely toinclude some duplicate marriages due to misspelled names, as well as discrepancies in the date and lo-cation of marriages within duplicate observations. In many of these cases it is difficult to be certain thattwo records refer to the same marriage, making it difficult to systematically remove all duplicates. As analternative conservative approach, we dropped multiple marriages where both spouses have the samename and the marriage took place in the same state and year, and re-ran our analysis. Our results arerobust to this restriction. These results are available upon request.B.1.1 Genealogical recordsTo complement our measure of cousin marriage using marriage records, we present an alternative datasetthat includes a direct measure of kinship ties between spouses. This comes from anonymised, publiclyavailable family trees from the Familinx database (Kaplanis et al., 2018), downloadable at familinx.org.This dataset provides exact ancestral links of individuals derived from family trees that have been createdand managed by users of the geni.com website, who are mostly amateur genealogists researching theirown family trees. The website allows independent trees to be merged and automatically suggests doingso when it detects sufficient overlap. Kaplanis et al. (2018) have cleaned this dataset and removed obvi-ous errors (such as someone having three parents or being both the descendent and ancestor of anotherindividual). The largest tree in this dataset, once cleaned, includes 13 million individuals.This individual-level dataset includes the following variables for a large share of entries: gender, yearand place of birth and death. However, we do not directly observe marriages. We instead simply assumethat the two parents of any individual were married. Since the date and place of marriage are almostalways absent, we proxy for these using the year and birthplace of the firstborn child of a given pair. Thisintroduces some error in our measure of consanguinity over time and place, since we cannot measure thedelay between marriage and the birth of the first child. It also means that we ignore childless marriages,and treat unmarried parents as having been married. Note that since we wish to focus on US marriages,197we keep only couples where the first child was born in the US. Their ancestors, of course, may have beenborn abroad, which potentially allows us to identify cousin marriage among first or second generationimmigrants.A limitation of this dataset is that family trees are often incomplete \u2013 few individuals in the data havethe full complement of eight great-grandparents. This is problematic since finding common ancestorsof a husband and wife requires going back at least two generations in the case of first cousins (great-grandparents of the couple\u2019s child), and three generations for second cousins (great-great-grandparents).Figure B.2 presents summary statistics describing the nature and degree of non-missing links for indi-viduals in the Familinx data. Each bar\u2019s horizontal length represents the number of people who have atleast as many ancestors in the dataset as the bar\u2019s rank within its generation (vertically from top). Forexample, for grandparents, the top bar shows the number of individuals who have at least one grandpar-ent link, the second bar shows the number of individuals with at least 2 grandparents, and so on. Theblack horizontal bars separate generations: grandparents, great grandparents and great great grandpar-ents. Despite the large number of missing links, this genealogical data includes many ancestral links for alarge number of individuals, which allows us to compare this data with isonymy rates from the marriagerecords, and also confirm the impact of bans on cousin marriage rates.B.1.2 Types of first-cousin marriages, and implications for measures of isonymyIn this section, we discuss the type of first-cousin marriages that isonymy rates proxy for, the types itcannot capture and what this means for the type of effects identified in our main results. We also directlycompare the distribution of cousin marriage rates in the 19th century with isonymy rates over the sameperiod of time.Recall, from section 2, that there are four different types of first-cousin marriage from a male\u2019s per-spective:1. Marrying father\u2019s brother\u2019s daughter (Type 1)2. Marrying father\u2019s sister\u2019s daughter (Type 2)3. Marrying mother\u2019s brother\u2019s daughter (Type 3)198Figure B.2: Individuals with non-missing ancestral links (genealogical data)Grandparents (4)Great grandparents (8)Great great grandparents (16)0 250k 500k 750k 1 million 1.25 million 1.5 millionIndividuals with non-missing ancestral links (geni data)Note: This figure shows the number of observations (individuals) in the Familinx data who have a given number of ancestrallinks. For example, for grandparents, the first bar (vertically top) shows the number of individuals who have at least one grand-parent link, the second bar shows the number of individuals with at least 2 grandparents so on and so forth. The pattern issimilarly followed for great grandparents and great great grandparents.4. Marrying mother\u2019s sister\u2019s daughter (Type 4)In societies with patrilineal naming systems, surnames are inherited along the male line. This impliesisonymy only captures the first type from the above list. This is because only in the first case will thefemale in the marriage be given the common family surname, resulting in an isonymous marriage. Whileeach of the other cases are also first-cousin marriages, isonymy rates by construction will not be able tocapture those. This is illustrated in figure B.3.This implies some measurement error in our rate of cousin marriage. If all four types of first-cousinmarriages are equally preferred, we would be capturing a quarter of the true cousin marriage rates, in ex-pectation. Fortunately, the genealogical data, by allowing us to identify exact ancestral links, can speak to199Figure B.3: Cousin marriage and isonymyGeneration n (siblings)Generation n+1 (married pair)Brother-Brother Sister-SisterMale FemaleInherits surnameDoes not inherit surnameType 1(Patrilateral parallel cousins)Type 2(Matrilateral parallel cousins)Type 3(Matrilateral cross cousins)Type 4(Patrilateral   cross cousins)Sister-Brother Brother-SisterLegendNote: This figure illustrates why only one of the four types of cousin marriage leads to isonymy. The solid shapes represent theoffspring of someone from generation n who carries their surname (in a patrilateral society, where children inherit the surnameof their father). Hollow shapes do not. Hence only marriage between the first type of cousins (the offspring of brothers) leadsto isonymy.this. We calculate rates of all four types of first-cousin marriage using Familinx data and plot their sharesbetween 1800 and 1940 in Figure B.4. The type of first-cousin marriages that isonymy rates capture isdenoted by the blue line in the figure\u2014it hovers between 25% to 35% throughout the period. Overall,while there does seem to have been a slight preference for parallel cousin marriage, the share of eachtype is roughly constant over time. We further show in the next section that bans on cousin marriage didnot affect the proportion of marriages that are isonymous.We next compare the rate of isonymous marriages from marriage records to the rate of cousin mar-riages from Familinx. Table B.1 reports results from regressions at the state-year level\u2014the outcome200Figure B.4: Types of first-cousin marriages.1.2.3.41800 1850 1900 1950Year (10 year bins)Father's Brother's Daughter Father's Sister's Daughter Mother's Brother's Daughter Mother's Sister's DaughterTypes of First Cousin Marriage over Time (Shares)variable is the proportion of isonymous marriages in the marriage records. The Familinx-derived inde-pendent variables are, in column (1), the proportion of marriages with any overlap in family trees, and incolumn (2), the proportion of marriages between first cousins. We restrict the sample to state-year pairsin the period 1800-1940 with at least 100 marriages in both datasets. Both columns report a positive andstatistically significant correlation between isonymy and cousin marriage rates.201Table B.1: Genealogical data and IsonymyIsonymous MarriageSource: Marriage records(1) (2)Consanguineous marriage 0.0421*Source: Genealogical records (0.0224)First-cousin marriage 0.0563*Source: Genealogical records (0.0340)N 2314 2314Adj. R2 0.256 0.256* p<0.10, ** p<0.05, *** p<0.010. Robust standard errors in paren-theses. Data on consanguineous marriages from genealogical records(Familinx). Isonymous marriages from marriage records. Observa-tions are at the state-year level. Sample for state-year level observa-tions is restricted to those years with at least 100 marriages both in theFamilinx data and in the marriage records.We now compare isonymy rates and Type 1 first-cousin marriage rates (as a percentage of all mar-riages in the U.S.) over time. If isonymy rates capture Type 1 first-cousin marriages we should expectthese rates to evolve in a similar pattern over time. We indeed observe this in Figure B.5 throughout the120 year period between 1800 to 1940.Both isonymy and Type 1 first-cousin marriage rates decreased gradually from 1800 to 1940 (from1.5%-2% to about 0.6%). There is however an increase in both of these rates from around 1840 untilabout 1860, after which they continued to fall throughout the rest of the period.To summarize, in this section we have specified the relationship between isonymy and first-cousinmarriages. Then, using genealogical data, we inferred rates over time for the particular type of first-cousin marriage identified by isonymy. We have shown these rates are closely correlated with isonymyrates calculated from the marriage records data. These data patterns strengthen the case for usingisonymy as a measure of consanguinity.B.1.3 Cousin marriage bans: Evidence from genealogical recordsIn table B.2, we provide evidence that bans on cousin marriage led to the reduction in consanguineousunions, using genealogical data. Marriage-level observations are collapsed to create a state-year panel of202Figure B.5: Type 1 first-cousin marriages (Familinx) and isonymy (marriage records).005.01.015.02Type 1 first cousin marriages (marrying father's brother's daughter)1800 1830 1860 1890 1920 1950Year90% CI lpoly smoothkernel = epanechnikov, degree = 0, bandwidth = 11.36, pwidth = 17.04Type 1 first cousin marriages (geni).005.01.015.02Isonymous Marriages1800 1830 1860 1890 1920 1950Year95% CI lpoly smoothkernel = epanechnikov, degree = 0, bandwidth = 8.16, pwidth = 12.24Isonymous Marriages (Marriage Records)cousin marriage rates, where state refers to the couple\u2019s state of residence (inferred from the birth stateof their first child). The main regressor is a dummy coded 1 if the state already had a ban in place in thatyear, 0 otherwise. We include state and year fixed effects, whereby the coefficients can be interpreted asdifference-in-difference estimates. The coefficients show that cousin marriage rates fell by about half instates with a ban on cousin marriage, which is consistent with our main results.203Table B.2: Effect of bans on cousin marriage rates (genealogical records)Consanguineous marriagesState-year ban -0.0385***(0.0101)State F.E. YesYear F.E. YesN 1335Adj. R2 0.338Mean Dep Var. 0.074* p<0.10, ** p<0.05, *** p<0.010. Robust standard errorsin parentheses. Data on consanguineous marriages fromgenealogical records (Familinx). Observations are at thestate-year level. Any state-year with fewer than 25 mar-riages are dropped. Regressions include state and yearfixed effects. The sample includes all individuals with atleast one non-missing great-grandparent from each par-ent\u2019s side.Using this genealogical dataset we also test a key assumption that underlies our results using mar-riage records: that bans on cousin marriage did not change the fraction of cousin marriages that areisonymous. Recall that our calculation of cousin marriage rates assumes that a quarter of cousin mar-riages are between the children of two brothers. These are the only such marriages that are isonymous(since women do not pass on their surname), and hence the only type we can observe through maritalisonymy. However, this type of cousin marriage may be easier to observe, given the shared surnames,and therefore may be disproportionately affected by a ban on cousin marriage. This would lead us tooverstate the effect of such a ban since our marriage records only allow us to measure this type of ban.The genealogical data allows us to test for this directly.Specifically, table B.3 tests whether the ratio of isonymous (FBD, or \u201cFather\u2019s brother\u2019s daughter\u201d)cousin marriages relative to the other three types changes post-ban. We find no evidence for a differentialeffect on this type of cousin marriage, which suggests that our ability to infer overall rates of cousinmarriage using isonymy is consistent pre- and post-ban.204Table B.3: DID Regressions: Impact of bans on ratio of cousin marriage types(1) (2) (3) (4)F BDF SDF BDMBDF BDMSDF BDF SD+MSD+MBDState-year ban -0.00345 0.00261 -0.0132 -0.0187(0.00543) (0.00201) (0.0111) (0.0124)State F.E. Yes Yes Yes YesYear F.E. Yes Yes Yes YesN 5429 5429 5429 5429Adj. R2 0.026 0.006 0.052 0.057* p<0.10, ** p<0.05, *** p<0.010. This table estimates the impact of bans on first-cousin mar-riages on the frequency type-1 first-cousin marriages (FBD marriages) as a proportion of othertypes (FSD, MBD and MSD). Standard errors are clustered at the state-level in parentheses. All re-gressions include state and year fixed effects. The ratio in each column is coded to be 0 if neithertype of marriage is recorded in the state in that year.B.1.4 Census variable definitionsIn this section, we provide definitions of the main census outcome variables, from the US census, asobtained from IPUMS. We also describe how (in some cases) we construct other variables from these.The census rounds from which we use a particular variable are mentioned below its description. Thevariable names in uppercase letters refer to the IPUMS labels, and the ones in italics are those used inthe paper.Income1. Log Occupational Income \u2014 OCCSCORE is a constructed variable that assigns each occupation anincome score. It assigns each occupation in all years a value that represents median total income(in hundreds of 1950 dollars) of all persons with that particular occupation in 1950. We use log ofthis variable as our outcome. We drop observations with missing values from our analysis.Census Rounds: 1850, 1870, 1900, 1920, 1930, 19402. Log Wage Income \u2014 INCWAGE is a respondent\u2019s total pre-tax wage and income from salary - inother words it is money received as an employee in the previous year. The following are includedin INCWAGE: wages, salaries, commissions, cash bonuses, tips, and any other money income re-205ceived from an employer. In-kind payments or reimbursements for business expenses are not in-cluded in this. We use log of this variable as outcome dropping observations with missing values.Census Rounds: 1940Schooling1. Grade \u2014 HIGRADE is a continuous variable denoting the highest grade of school attended or com-pleted by the respondent. The general code for this variable denotes the highest grade that hasbeen completed. We use this variable to denote the highest level of schooling attained by an indi-vidual.Census Rounds: 19402. In School \u2014 SCHOOL is a binary variable that indicates whether a person attended school duringa specified time period in the past. The period varies across censuses, but is typically within 3months to a year from when the person was being surveyed.Census Rounds: 1850, 1870, 1900 (5%), 1920, 1940Genetic Effects1. Living in Hospital, Mental Institution, or Home for Physically Handicapped \u2014 This is a dummy vari-able constructed from the GQTYPE variable, which denotes the type of group-quarter within whichthe respondent resided in. Most respondents reside in private households, rather than group quar-ters. The variable takes the value 1 if the respondent resided in a hospital, in a mental institutionor in homes, hospitals or schools for the physically handicapped.Census Rounds: 1930, 1940Urbanization1. Urban \u2014 URBAN indicates whether the location of residence of a household is urban or rural. It iswidely used but it does have some problems. Definitions of \u201curban\u201d vary slightly from year to year- but it typically denotes all cities and incorporated places which have more than 2500 inhabitants.Census Rounds: 1850, 1870, 1900, 1920, 1930, 19402062. Farm Household \u2014 FARM identifies all farm households. Based on the census round such house-holds are identified either by the occupation of the household members or whether their housewas located on a farm. All group quarters are coded as non-farm. We use a dummy variable coded1 to indicate a farm household.Census Rounds: 1850, 1870, 1900, 1920, 19403. Log Population Size \u2014 SIZEPL reports the population of a municipality in bins of different sizes.Unidentified locations are grouped as \u201cUnder 1,000 or unincorporated\u201d. We use the log of the mid-point of each bin as our outcome, Log Population Size.Census Rounds: 1850, 1870, 1900, 1920, 1930, 1940Labor Supply1. Weeks worked \u2014 WKSWORK1 in the IPUMS data is the total number of weeks that a respondentworked during the previous year for profit, pay, including unpaid work.Census Rounds: 19402. Weeks Worked > 0 \u2014 A dummy variable which takes a value of 1 if WKSWORK1 > 0Census Rounds: 1940207B.1.5 Predictors of state bans on cousin marriageThis section explores differences across states in the timing of bans on first-cousin marriage. We do notargue that the timing of these bans was random. This is in part why we rely on variation within states,comparing surnames with high versus low rates of cousin marriage in the pre-period. However it maystill be that predictors of earlier bans on cousin marriage have differential effects on high versus lowcousin marriage families.Table B.4 presents differences between early and late ban states for a range of factors which historianshave pointed to as possible drivers of these bans on cousin marriage. We categorize states that bannedcousin marriage pre-1902 as \u2018early\u2019 in order to equalize the number of early versus late ban states. Re-sults in Table B.4 do not suggest major differences between these states, though the small number ofobservations means we have limited power to detect such differences.208Table B.4: Early versus late bans and state characteristicsVariable Early ban Late ban Diff(Pre-1902) (1902-onward) (2) - (1) N(1) (2)Cousin marriage rate (1800-1850) 0.05 0.05 -0.001 24(0.00) (0.00) (0.001)Year of Union 1851.12 1847.12 -4.00 32(9.39) (9.78) (13.564)Year of Compulsory Schooling 1887.31 1892.88 5.563 32(3.53) (3.35) (4.869)Share Foreign Born 0.08 0.13 0.051 19(0.02) (0.03) (0.043)Proportion urban 0.11 0.08 -0.034 18(0.03) (0.02) (0.037)Literacy Rate 0.86 0.89 0.026 18(0.03) (0.02) (0.038)Baptist churches per 10k ppl 3.98 3.46 -0.517 16(0.60) (0.88) (1.134)Methodist churches per 10k ppl 5.38 5.82 0.618 16(0.92) (0.96) (1.362)Presbyterian churches per 10k ppl 1.96 2.02 0.070 16(0.44) (0.31) (0.523)Roman Catholic churches per 10k ppl 0.63 0.73 0.097 16(0.13) (0.20) (0.256)Significance levels: * <10% ** <5% *** <1%. Standard errors in parentheses. \u201cYear of Union\"denotes the year in which the state became a part of the Union. \u201cYear of Compulsory School-ing\u201d denotes the year in which compulsory schooling laws were passed in the state. Cousinmarriage rates are calculated from marriage records as described in section 3.2.2. Proportionurban, share foreign born and literacy rates are measured from the 1850 Census. The num-ber of churches is measured from the 1870 Census. The number of churches are per 10,000inhabitants.Another potential threat to identification could be differential pre-trends in cousin marriage ratesbetween states that banned cousin marriage early versus those that banned it late. In other words, itmight be the case that states that banned cousin marriage early are the ones where it was decliningfaster anyway. To rule this out, Table B.5 uses a state-year panel of 1800-1858 isonymy rates to showthat changes over time in rates of cousin marriage are not correlated with the (future) timing of cousinmarriage bans. Specifically, we regress state-year rates of observed isonymy on the year (as a continuousvariable) interacted with the timing of a cousin marriage ban in that state. In absence of pre-trends we209should see a null effect on this interaction term, which is what we find.Table B.5: Pre-trends in isonymy rates(1)Observed isonymy ratesYears Banned by 1940 (Fraction) -0.00006\u00d7 Year (1800-1858) (0.0003)State F.E. YesYear F.E. YesN 1239Adj. R2 0.092* p<0.10, ** p<0.05, *** p<0.010. State-year level observations. A marriage is consideredto be isonymous if both individuals involved in the marriage share the same surname.Marriages are collapsed at the state-year level to obtain isonymy rates. Standard errorsclustered at the state level in parentheses.210B.1.6 Non-random isonymy censoringThroughout our analysis, we use log values of non-random isonymy as our measure of cousin marriage.Before taking the log, we replace values of non-random isonymy below \u03f5 with \u03f5. We do this for two rea-sons. The simplest is that non-random isonymy takes a negative value whenever isonymous marriagesare less frequent than predicted under random mating. Replacing these values with zero would still notallow us to convert them into logs, hence a positive value. The second reason is that most surname-statecells have rates of non-random isonymy near zero, and we cannot statistically distinguish these ratesfrom zero (or each other). Since small level changes near zero are large proportional changes, valuesof \u03f5 that are too small result in most of the variation in the log of non-random isonymy being drivenby measurement error. To attenuate this concern, we choose a value of \u03f5 sufficiently large that rates ofnon-random isonymy above this threshold are typically distinguishable from zero.We use a threshold of \u03f5 = 0.015 in our main analysis. In this section we justify our threshold choiceand show robustness to other values of \u03f5. First, we analyze how the total number of individuals witha surname (sample size) and its isonymy rate, in a marriage pool, affect the ability to reject zero non-random isonymy for that group. This motivates our threshold choice. To do this, we first test for eachsurname whether its rate of non-random isonymy in the pre-period can be distinguished from zero. Wesplit non-random isonymy values into a range of threshold choice bins and present the average rejectionprobability (rate) across all surnames in each bin, in Figure B.6a. Clearly, for low threshold values, oneneeds a very large sample size to reject zero non-random isonymy, whereby the rejection rate is low. Forbins with higher values, the rejection rate increases. A value of \u03f5 = 0.015 is the lower bound of the bin0.015-0.02. As can be observed in Figure B.6a, this gives a rejection rate around 80%.211Figure B.6: Surname Frequency and Zero NR Isonymy Rejection0.2.4.6.81Rejection Rate0- .005- .01- .015- .02- .025- .03- .035- .04- .045-Threshold Choice (Bins)(a) Threshold Choice and Rejection Rate0.2.4.6.81Rejection Rate0 500 1000 1500 2000300Surname Count0-0.005 0.005-0.010.01-0.015 0.015-0.020.02-0.025 0.025-0.03Threshold Choice (Bins)(b) Surname Count and Rejection RateNote: In Figure B.6a non-random isonymy values are split into a range of threshold choice bins and average rejection ratesacross all surnames in each bin is presented. In Figure B.6b, we show how rejection rates vary, given a threshold choice bin, asthe number of records for a surname increases. Each line represents a separate threshold bin.In Figure B.6b, we show how rejection rates vary, given a threshold choice bin, as the number ofrecords for a surname increases. With lower threshold values a larger number of records are requiredto reject zero isonymy. On average, around 300 records are required for surnames with non-randomisonymy in the range 0.015-0.02, to achieve a 80% rejection probability. The median surname count in212our data is 455. The choice of 0.015 as the threshold therefore leads to a rejection rate of greater than 80%for more than half of the surnames in our sample.We test robustness of our results to alternative choices of thresholds in Table B.8 in the Appendix.We re-run our analysis using various values of \u03f5. As expected, low values of \u03f5 attenuate the coefficients,consistent with our interpretation that small differences in non-random isonymy between surnameswith low rates of cousin marriage are mostly measurement error.213B.2 Supplementary tables and figuresTable B.6: Impact of bans on cousin marriage rates (Year Bins)(1)Log (CousinMarrpost )Treatment intensity (pre-1940 bans)Year banned (1-16) \u00d7 Log (CousinMarrpr e ) \u2013Year banned (17-33) \u00d7 Log (CousinMarrpr e ) -0.141(0.0907)Year banned (34-50) \u00d7 Log (CousinMarrpr e ) -0.212***(0.0820)Year banned (51-67) \u00d7 Log (CousinMarrpr e ) -0.245***(0.0782)Year banned (68-85) \u00d7 Log (CousinMarrpr e ) -0.287***(0.0773)N 1,207,523Adj. R2 0.450* p<0.10, ** p<0.05, *** p<0.010. Standard errors clustered at the origin state (father\u2019s birth state)-surname level in parentheses. All regressions include age effects, origin-state, residence state,and surname fixed effects. Log (CousinMarrpr e ) and Log (CousinMarrpr e ) are constructed as de-scribed in section 3.2.2. Cousin marriage rates are calculated at the state level in the pre-period andsurname-state level in the post period and linked at the surname-state (of father\u2019s birth) level withthe 1940 Census. Sample includes White males aged 18 to 50 in 1940 unless otherwise specified.214Table B.7: Cousin marriage rates in levels(1) (2) (3) (4)Log Occup. Income Highest Grade Weeks Worked Log UrbanizationFemalesYears Ban (Fraction) \u00d7 CousinMarrpr e 0.150* 0.839* 5.534** 1.004**(0.0890) (0.478) (2.718) (0.439)Mean Dep. Var. 2.87 10.17 14.95 8.28Surname F.E. . Yes Yes Yes YesState of Origin F.E. Yes Yes Yes YesState of Residence F.E. Yes Yes Yes YesN 976,414 1,187,725 942,605 1,207,523Adj. R2 0.122 0.120 0.055 0.132* p<0.10, ** p<0.05, *** p<0.010. Standard errors clustered at the surname-origin state (father\u2019s birth state) level in parentheses. Cousinmarriage rates are calculated (as described in section 3.2.2) at the surname-level in the pre-period and surname-state level in the postperiod and linked at the surname-origin state (of father\u2019s birth) level with the 1940 Census records. Years Ban (Fraction) refers to the numberof years each state had a ban on cousin marriage in place by the year 1940, divided by 82, which is the number of years that had passed sincethe first ban in Kansas in 1858. Sample includes White males aged 18 to 50 in 1940 unless otherwise specified.215Table B.8: Robustness to threshold choice\u03f5 = 0.005 \u03f5 = 0.010 \u03f5 = 0.015 \u03f5 = 0.020(1) (2) (3) (4)Log Occupational IncomeYears Ban (Fraction) \u00d7 Log(CousinMarrpr e ) 0.00788 0.0148* 0.0392*** 0.0522**(0.00533) (0.00875) (0.0140) (0.0218)Mean Dep. Var. 2.87 2.87 2.87 2.87N 976,414 976,414 976,414 976,414Adj. R2 0.122 0.122 0.122 0.122Log population size of locality of residence (Urbanization)Years Ban (Fraction) \u00d7 Log(CousinMarrpr e ) 0.0391 0.109*** 0.303*** 0.492***(0.0243) (0.0421) (0.0733) (0.122)Mean Dep. Var. 8.29 8.29 8.29 8.29N 1,207,523 1,207,523 1,207,523 1207523Adj. R2 0.132 0.132 0.132 0.132Surname F.E. Yes Yes Yes YesState of Origin F.E. Yes Yes Yes YesState of Residence F.E. Yes Yes Yes Yes* p<0.10, ** p<0.05, *** p<0.010. Standard errors clustered at the surname-origin state (father\u2019s birth state) levelin parentheses. Cousin marriage rates are calculated (as described in section 3.2.2) at the surname-level in thepre-period and surname-state level in the post period and linked at the surname-origin state (of father\u2019s birth)level with the 1940 Census records. Years Ban (Fraction) refers to the number of years each state had a ban oncousin marriage in place by the year 1940, divided by 82, which is the number of years that had passed since thefirst ban in Kansas in 1858. Sample includes White males aged 18 to 50 in 1940 unless otherwise specified.216Table B.9: Dropping top and bottom 5% of common surnamesLog Occupational Income (1940) Highest Grade Completed (1940) Weeks Worked Log (Urbanization)Females(1) (2) (3) (4) (5) (6) (7) (8)Years Ban (Fraction) \u00d7 Log (CousinMarrpr e ) 0.0354** 0.0301* 0.223*** 0.178** 1.005** 0.906* 0.298*** 0.231***(0.0142) (0.0157) (0.0776) (0.0905) (0.4377) (0.4777) (0.0730) (0.0774)Surname F.E. Yes Yes Yes Yes Yes Yes Yes YesState of Origin F.E. Yes Yes Yes Yes Yes Yes Yes YesState of Residence F.E. Yes Yes Yes Yes Yes Yes Yes YesSurname-state pre-treatment controls No Yes No Yes No Yes No YesMean Dep. Var. 2.88 2.88 10.17 10.10 14.98 15.04 8.29 8.30N 924,512 837,719 1,124,534 1,013,575 893,306 808,537 1,143,195 1,028,614Adj. R2 0.122 0.122 0.120 0.120 0.055 0.101 0.132 0.135* p<0.10, ** p<0.05, *** p<0.010. Standard errors clustered at the surname-origin state (father\u2019s birth state) level in parentheses. Cousin marriage ratesare calculated (as described in section 3.2.2) at the surname-level in the pre-period and surname-state level in the post period and linked at the surname-origin state (of father\u2019s birth) level with the 1940 Census records. Years Ban (Fraction) refers to the number of years each state had a ban on cousin marriagein place by the year 1940, divided by 82, which is the number of years that had passed since the first ban in Kansas in 1858. Surname-state pre-treatmentcontrols include occupational income (logged) and population of locality of residence (logged) measured at the surname-state level from the 1850 censusrecords. Sample includes White males aged 18 to 50 in 1940 unless otherwise specified.217Table B.10: Including all states (including states that never banned)Log Occupational Income (1940) Highest Grade Completed (1940) Weeks Worked Log (Urbanization)Females(1) (2) (3) (4) (5) (6) (7) (8)Years Ban (Fraction) \u00d7 Log (CousinMarrpr e ) 0.0270*** 0.0306*** 0.0465 0.0733 0.505* 0.625* 0.136** 0.163***(0.00930) (0.0116) (0.0494) (0.0656) (0.2907) (0.3462) (0.0565) (0.0624)Surname F.E. Yes Yes Yes Yes Yes Yes Yes YesState of Origin F.E. Yes Yes Yes Yes Yes Yes Yes YesState of Residence F.E. Yes Yes Yes Yes Yes Yes Yes YesSurname-state pre-treatment controls No Yes No Yes No Yes No YesMean Dep. Var. 2.88 2.87 9.97 9.85 15.47 14.84 8.34 8.18N 1,665,794 1,208,303 2,018,176 1,460,251 1,658,089 1,256,009 2,057,490 1,486,457Adj. R2 0.129 0.124 0.138 0.138 0.0629 0.0576 0.189 0.156* p<0.10, ** p<0.05, *** p<0.010. Standard errors clustered at the surname-origin state (father\u2019s birth state) level in parentheses. Cousin marriage ratesare calculated (as described in section 3.2.2) at the surname-level in the pre-period and surname-state level in the post period and linked at the surname-origin state (of father\u2019s birth) level with the 1940 Census records. Years Ban (Fraction) refers to the number of years each state had a ban on cousin marriagein place by the year 1940, divided by 82, which is the number of years that had passed since the first ban in Kansas in 1858. Surname-state pre-treatmentcontrols include occupational income (logged) and population of locality of residence (logged) measured at the surname-state level from the 1850 censusrecords. Sample includes White males aged 18 to 50 in 1940 unless otherwise specified.218Table B.11: 1930 OutcomesLog Occupational Income Log (Urbanization)(1) (2) (3) (4)Years Ban (Fraction) \u00d7 Log (CousinMarrpr e ) 0.0230*** 0.0173** 0.0852** 0.0379(0.00732) (0.00781) (0.0463) (0.0481)Surname-state pre-treatment controlsLog Occupational Income (1850) 0.0541*** 0.259***(0.00766) (0.0444)Log Urbanization (1850) 0.0263*** 0.310***(0.00181) (0.0137)Mean Dep. Var. 3.03 3.02 8.59 8.59Surname F.E. Yes Yes Yes YesState of Origin F.E. Yes Yes Yes YesState of Residence F.E. Yes Yes Yes YesN 3,161,458 2,989,111 4,021,199 3,790,663Adj. R2 0.133 0.131 0.145 0.144* p<0.10, ** p<0.05, *** p<0.010. Standard errors clustered at the surname-origin state (father\u2019s birth state)level in parentheses. Cousin marriage rates are calculated (as described in section 3.2.2) at the surname-level in the pre-period and surname-state level in the post period and linked at the surname-origin state(of father\u2019s birth) level with the 1930 Census records. Years Ban (Fraction) refers to the number of yearseach state had a ban on cousin marriage in place by the year 1940, divided by 82, which is the number ofyears that had passed since the first ban in Kansas in 1858. Sample includes White males aged 18 to 50 in1930.219Table B.12: Robustness to years of compulsory schoolingLog Occupational Income (1940) Highest Grade Completed (1940) Weeks Worked Log (Urbanization)Females(1) (2) (3) (4) (5) (6) (7) (8)Years Ban (Fraction) \u00d7 Log(CousinMarrpr e ) 0.0466*** 0.0408*** 0.270*** 0.215** 0.904** 0.934* 0.307*** 0.249***(0.0144) (0.0156) (0.0832) (0.0942) (0.452) (0.494) (0.0717) (0.0764)Years Compulsory Schooling \u00d7 Log(CousinMarrpr e ) -0.000733* -0.00104** -0.00235 -0.00214 0.0127 0.00177 -0.000355 -0.00145(0.000377) (0.000410) (0.00186) (0.00213) (0.01123) (0.01262) (0.00191) (0.00221)Surname F.E. Yes Yes Yes Yes Yes Yes Yes YesState of Origin F.E. Yes Yes Yes Yes Yes Yes Yes YesState of Residence F.E. Yes Yes Yes Yes Yes Yes Yes YesSurname-state pre-treatment controls No Yes No Yes No Yes No YesMean Dep. Var. 2.87 2.88 10.17 10.10 14.95 14.95 8.28 8.29N 976,414 885,324 1,187,725 1,071,133 942,605 853,731 1,207,523 1,087,102Adj. R2 0.122 0.122 0.120 0.119 0.0549 0.0545 0.132 0.134* p<0.10, ** p<0.05, *** p<0.010. Standard errors clustered at the surname-origin state (father\u2019s birth state) level in parentheses. Cousin marriage rates arecalculated (as described in section 3.2.2) at the surname-level in the pre-period and surname-state level in the post period and linked at the surname-origin state(of father\u2019s birth) level with the 1940 Census records. Years Ban (Fraction) refers to the number of years each state had a ban on cousin marriage in place bythe year 1940, divided by 82, which is the number of years that had passed since the first ban in Kansas in 1858. Surname-state pre-treatment controls includeoccupational income (logged) and population of locality of residence (logged) measured at the surname-state level from the 1850 census records. Sample includesWhite males aged 18 to 50 in 1940 unless otherwise specified.220Table B.13: Robustness to years of statehoodLog Occupational Income (1940) Highest Grade Completed (1940) Weeks Worked Log (Urbanization)Females(1) (2) (3) (4) (5) (6) (7) (8)Years Ban (Fraction) \u00d7 Log(CousinMarrpr e ) 0.0402*** 0.0345** 0.241*** 0.189** 0.9762** 0.8516* 0.340*** 0.262***(0.0144) (0.0159) (0.0793) (0.0917) (0.4531) (0.5002) (0.0790) (0.0842)Years Statehood \u00d7 Log(CousinMarrpr e ) 0.0000776 0.0000532 -0.000346 -0.000792 -0.00598 -0.00742 0.00287** 0.00166(0.000175) (0.000223) (0.000856) (0.00113) (0.00537) (0.00709) (0.00119) (0.00124)Surname F.E. Yes Yes Yes Yes Yes Yes Yes YesState of Origin F.E. Yes Yes Yes Yes Yes Yes Yes YesState of Residence F.E. Yes Yes Yes Yes Yes Yes Yes YesSurname-state pre-treatment controls No Yes No Yes No Yes No YesMean Dep. Var. 2.87 2.88 10.17 10.10 14.95 14.95 8.28 8.29N 976,414 885,324 1,187,725 1,071,133 942,605 853,731 1,207,523 1,087,102Adj. R2 0.122 0.122 0.120 0.119 0.050 0.101 0.132 0.134* p<0.10, ** p<0.05, *** p<0.010. Standard errors clustered at the surname-origin state (father\u2019s birth state) level in parentheses. Cousin marriage ratesare calculated (as described in section 3.2.2) at the surname-level in the pre-period and surname-state level in the post period and linked at the surname-origin state (of father\u2019s birth) level with the 1940 Census records. Years Ban (Fraction) refers to the number of years each state had a ban on cousin marriagein place by the year 1940, divided by 82, which is the number of years that had passed since the first ban in Kansas in 1858. Surname-state pre-treatmentcontrols include occupational income (logged) and population of locality of residence (logged) measured at the surname-state level from the 1850 censusrecords. Sample includes White males aged 18 to 50 in 1940 unless otherwise specified.221Table B.14: Robustness to percent native populationLog Occupational Income (1940) Highest Grade Completed (1940) Weeks Worked Log (Urbanization)Females(1) (2) (3) (4) (5) (6) (7) (8)Years Ban (Fraction) \u00d7 Log(CousinMarrpr e ) 0.0415*** 0.0339** 0.247*** 0.200** 0.938** 0.946* 0.295*** 0.242***(0.0151) (0.0155) (0.0876) (0.0921) (0.4760) (0.4890) (0.0824) (0.0779)Percent Native Born (1850)\u00d7 Log(CousinMarrpr e ) 0.000659 0.000370 0.000721 -0.00164 0.00163 -0.01312 0.0108*** 0.00989***(0.000604) (0.000631) (0.00305) (0.00341) (0.00165) (0.01817) (0.00351) (0.00361)Surname F.E. Yes Yes Yes Yes Yes Yes Yes YesState of Origin F.E. Yes Yes Yes Yes Yes Yes Yes YesState of Residence F.E. Yes Yes Yes Yes Yes Yes Yes YesSurname-state pre-treatment controls No Yes No Yes No Yes No YesMean Dep. Var. 2.87 2.88 10.11 10.10 15.06 15.00 8.29 8.29N 914,220 885,324 1,106,857 1,071,133 882,015 853,731 1,123,479 1,087,102Adj. R2 0.123 0.122 0.119 0.119 0.099 0.101 0.132 0.134* p<0.10, ** p<0.05, *** p<0.010. Standard errors clustered at the surname-origin state (father\u2019s birth state) level in parentheses. Cousin marriage rates arecalculated (as described in section 3.2.2) at the surname-level in the pre-period and surname-state level in the post period and linked at the surname-originstate (of father\u2019s birth) level with the 1940 Census records. Years Ban (Fraction) refers to the number of years each state had a ban on cousin marriage in place bythe year 1940, divided by 82, which is the number of years that had passed since the first ban in Kansas in 1858. Surname-state pre-treatment controls includeoccupational income (logged) and population of locality of residence (logged) measured at the surname-state level from the 1850 census records. Sampleincludes White males aged 18 to 50 in 1940 unless otherwise specified.222Figure B.7: Enforcement of cousin marriage bans in the news(a) Arkansas 1884(b) Indiana 1887223Appendix CAppendix to Chapter 4C.1 Tables and figuresTable C.1: Election cycle and fatal mining accidents (State-Level) (OLS)(1) (2) (3)Log Cases Log Injuries Log DeathsFour Years -0.0495 0.236 0.234**(0.116) (0.156) (0.136)[0.671] [0.133] [0.04]Three Years 0.0231 0.206 0.173(0.177) (0.157) (0.137)[0.903] [0.207] [0.252]Two Years -0.0962 0.0155 0.0246(0.138) (0.0909) (0.0717)[0.478] [0.855] [0.711]One Year -0.247** -0.237* -0.181(0.111) (0.123) (0.115)[0.036] [0.058] [0.102]State F.E. Yes Yes YesYear Effects Yes Yes YesState Time Trends Yes Yes YesN 350 350 350R2 0.898 0.550 0.495Notes : * p<0.10, ** p<0.05, *** p<0.010. State-Year Level observations between 1998-2015. Depen-dent variables are the natural logarithm of the number of events in a year in a given state. StandardErrors clustered at the State Level in parenthesis. P-values from Wild cluster Bootstrap with 1000replications presented in square [] brackets. All regressions include state effects, year effects andstate time trends. Outcome variables are subject to a log (x+1) transformation.224Table C.2: Election cycle and mining fatalities (district-level)Any Bad Event Accidents Deaths(1) (2) (3) (4) (5)Election\u22121 -0.0899 -0.132* -0.0262 -0.167** -0.321*(0.0607) (0.0667) (0.0859) (0.0687) (0.169)Election -0.176*** -0.151*** 0.0467 -0.0814* -0.083(0.0610) (0.0523) (0.0502) (0.0448) (0.130)Election+1 0.0779 0.121*** 0.325*** 0.161*** 0.420***(0.0691) (0.0397) (0.0715) (0.0491) (0.149)District F.E. Yes Yes Yes Yes YesRegion-Year F.E. Yes Yes Yes Yes YesN 412 412 412 412 412R2\/Log \u2212Li kel i hood 0.409 0.857 -543 0.623 -382Estimation OLS OLS Poisson OLS PoissonNotes : * p<0.10, ** p<0.05, *** p<0.010. District-Year level observations covering 104 districts across 15 states between 2010-2015. Standard errors clustered at the state-year level reported in parenthesis. Standard deviations for outcome means arereported in parenthesis. \u201cAny Bad Event\" is a dummy variable coded 1 if there was at least one serious or fatal accident in amining field. \u201cAccidents\" refer to the sum of both fatal and serious accident and \u201cDeaths\" refer to the total number of peopledkilled in mining fields in a district in a given year. Election\u22121, Election and Election+1 are dummies for the year immediatelybefore, the year of and the year immediately after a scheduled election respectively. All regressions include district and region-year effects. Outcomes Deaths and Accidents for OLS regressions are subject to a log (x+1) transformation.225Figure C.1: Election cycle and mining intensity (state-level coefficient plots)-.2-.10.1Log (Total mining leases)-4 -3 -2 -1 0Years to scheduled electionElection cycle and mineral licensing (state-level)-.10.1.2.3Log (Mining output per-capita)-4 -3 -2 -1 0Years to scheduled electionElection cycle and mining output (state-level)-.50.51Accidents in Mines-4 -1 -2 -1 0Years to scheduled electionElection cycle and mining accidents (state-level) -- poisson regressionNote: This figure presents coefficient plots from results in Tables 4.2, 4.3 and 4.4. The first plot (licensing) is based on Column(1) of Table 4.2, the second (output) is based on Column (1) of Table 4.3 and the third (fatal accidents) is based on Column(2) ofTable 4.4.226Figure C.2: Scheduled vs unscheduled elections and mining output \u2013 placebo test-.2-.10.1.2.3Impact on Log Mining Output (State Level)Unscheduled Election Scheduled ElectionImpact of Scheduled and Unscheduled Elections on Mining OutputNote: This figure shows the impact of scheduled and unscheduled elections on mining output from the state-level analysis. The y-axis plotscoefficient values from a regression of log mining output on a election dummy and an interaction between the election dummy and a dummydenoting whether the election was scheduled or not. Unscheduled elections are therefore all elections that occurred before the end of the 5 yearpolitical term.This figure plots coefficient estimates from the following regression,Yst =\u03b1s +\u03b21Elect i onst +\u03b22El ect i onst \u00d7Schedul edst +\u03b4t +\u03f5st (C.1)where Yst is log mining output in state s at year t , \u03b1s is a state fixed effect and \u03b4t is a year fixed effect andScheduledst denotes whether the election in state \u2018s\u2019 is scheduled or not. The effect of an unscheduledelection is therefore given by \u03b21 and that of a scheduled election by \u03b21 + \u03b22. Unscheduled electionsinclude all elections that took place before the end of a 5 year political term. The coefficient estimatesare relative to the average of all non-election years.227Table C.3: Mining cycles, literacy rates and Scheduled Tribe populationLog Accidents Log Casualties(1) (2) (3) (4) (5) (6)Election -0.176*** -0.126** -0.588** -0.174*** -0.120 -0.767***(0.0499) (0.0624) (0.234) (0.059) (0.074) (0.233)Election \u00d7 Proportion ST -0.370 -0.500(0.340) (0.490)Election \u00d7 Proportion Literate 0.720* 1.00***(0.380) (0.370)District F.E. Yes Yes Yes Yes Yes YesRegion-Year F.E. Yes Yes Yes Yes Yes YesN 605 605 605 605 605 605R2 0.878 0.878 0.879 0.696 0.697 0.698* p<0.10, ** p<0.05, *** p<0.010. District-Year Level observations covering 104 districts between 2010-2015.Each column represents a separate regression. Standard errors clustered at the state-year level reported inparenthesis. All regressions include District Fixed Effects and Region-Year Fixed Effects. Log Accidents referto the natural logarithm of all mining accidents in a district in a given year. Log Casualties refer to the naturallogarithm of the sum of deaths and injuries in mining fields in a district in a given year. Percentage of Sched-uled Tribe in each district have been obtained from the 2011 Census of India. Outcomes Log Accidents andLog Casualties are subject to a log (x+1) transformation.Table C.4: Correlates of mining fatalities and Naxalite conflictOnset Log Rebel Deaths Log Security Forces Deaths(1) (2) (3) (4) (5) (6)Log Accidents 0.0790*** 0.0217 0.121*** -0.0113 0.033 -0.0575(0.0288) (0.0393) (0.0446) (0.0710) (0.0344) (0.0593)Log Accidents \u00d7 Proportion ST 0.280* 0.622** 0.430*(0.151) (0.309) (0.260)Log Accidents \u00d7 Proportion ST \u00d7 Election -0.231** -0.221** -0.143**(0.095) (0.095) (0.065)District F.E. Yes Yes Yes Yes Yes YesRegion-Year F.E. Yes Yes Yes Yes Yes YesN 684 684 684 684 684 684R2 0.624 0.632 0.475 0.489 0.475 0.682* p<0.10, ** p<0.05, *** p<0.010. District-Year Level observations between 2010-2015 covering 114 districts. Stan-dard errors clustered at the state-year level reported in parenthesis. All regressions include District Fixed Effectsand Region-Year Fixed Effects. Log Accidents refer to the natural logarithm of all mining accidents in a district ina given year. Percentage of Scheduled Tribe in each district have been obtained from the 2011 Census of India.\u201cOnset\" is a dummy variable coded 1 if at least one death occurred from a clash between state forces and rebels.Outcomes Log Rebel and Log Security forces deaths are subject to a log (x+1) transformation.228Figure C.3: Red Corridor in Andhra Pradesh and Orissa(a) Andhra Pradesh (before split)(b) OrissaNote: This figure marks all districts in the states of Andhra Pradesh and Orissa that form a part of the sample for mining fatalitiesdata. Within each state Naxal affected districts as classified by the Union Ministry of Home Affairs in 2008 have been marked inred and the rest in green. This figure illustrates that when studying mining cycles, within-state variation can be used to identifythe overall effect of being in the Red Corridor on mining intensity.229Figure C.4: Fatality cycles and Red Corridor (state fixed effects)Note: This figure plots log predicted accidents over the electoral cycle comparing districts in the Red Corridor (red) and thosenot in the Red Corridor (blue) with state-fixed Effects . I use pre-sample classification of districts into the Red Corridor wherebyit is a fixed district characteristic. Since there is variation within states with respect to districts that are classified as part of theRed Corridor and those that are not, the main effect of being in the Red Corridor is captured here. This figure is based on resultsfrom Column (2) of Table 4.7. Dotted lines show 95% confidence intervals.Figure C.5: Fatality cycles and Red Corridor (state fixed effects)Note: This figure plots log predicted casualties over the electoral cycle comparing districts in the Red Corridor (red) and thosenot in the Red Corridor (blue) with state-fixed Effects. I use pre-sample classification of districts into the Red Corridor wherebyit is a fixed district characteristic. Since there is variation within states with respect to districts that are classified as part of theRed Corridor and those that are not, the main effect of being in the Red Corridor is captured here. This figure is based on resultsfrom Column (5) of Table 4.7. Dotted lines show 95% confidence intervals.230Figure C.6: Naxal rebel deaths over the election cycleNote: This diagram plots log predicted naxal rebel deaths from clashes between naxal rebels and security forces over the elec-toral cycle in mining and non-mining districts. The value in the election year is normalized to 0 in each case. It is based onspecifications of the form in Table 4.8 Columns (3), (6) and (9) but from a OLS model with log rebel deaths as the outcomevariable. The dotted lines represent 95% confidence intervals.Figure C.7: Security forces deaths over the election cycleNote: This diagram plots log predicted security forces deaths from clashes between naxal rebels and security forces over theelectoral cycle in mining and non-mining districts. The value in the election year is normalized to 0 in each case. It is basedon specifications of the form in Table 4.8 Columns (3), (6) and (9) but from a OLS model with log security forces deaths as theoutcome variable. The dotted lines represent 95% confidence intervals.231Figure C.8: Accident cycles and electoral competitionNote: This diagram plots log predicted accidents in mines over the next electoral cycle for notional districts with 0% and 90%close elections in the previous elections respectively. It is based on Column (3) of Table 4.5. Note that the value in election yearis 0 by construction for a district with no close elections. Dotted lines represent 95% confidence intervals.Figure C.9: Fatality cycles and electoral competitionNote: This diagram plots log predicted casualties in mines over the next electoral cycle for notional districts with 0% and 90%close elections in the previous elections respectively. It is based on Column (6) of Table 4.5. Note that the value in election yearis 0 by construction for a district with no close elections. Dotted lines represent 95% confidence intervals.232C.2 Data appendixTable C.5: Primary data sourcesData SourceMining Output (State -Level) EOPP Indian States Data andPlanning Commission of IndiaMineral Licensing (State Level) Indian Bureau of MinesMining Fatalities (State and District Level) Directorate General of Mines Safety,Ministry of Labour and EmploymentNaxalite Conflict (District Level) Uppsala Conflict Data Program (UCDP) andSouth Asia Terrorism Portal (SATP)State Level Election Outcomes Election Commission of IndiaFigure C.10: Electoral cycle and accident probability (raw data).4.5.6.7.8Any Bad Event-4 -3 -2 -1 0Years to Scheduled ElectionAny Bad Event lb\/ubElection Cycle and Accident ProbabilityNote: This figure presents district-level averages of the probability of a casualty (\u201cAny Bad Event\") over the electoral cycle. Thevariable \u201cAny Bad Event\" is a dummy coded 1 if at least one person was either seriously injured or killed in a mining accident ina district in a given year. Data from a total of 104 districts across 15 Indian states have been used to generate this graph. The 95% confidence intervals are shown.233This figure plots district-level averages of the probability of a mining field accident in each year of theelectoral cycle. There are no fixed effects included in this analysis.Figure C.11: Electoral cycle, close elections and mining accidents (local polynomial)Note: This figure presents a kernel weighted local polynomial fit of mining accidents against close election proportions condi-tional on elections being four years away, and in the election year respectively. Each polynomial in a different colour representsa different year in the electoral cycle. There are no fixed effects included in this analysis.Figure C.8 presents plots from kernel-weighted local polynomial regressions of mining casualties onthe proportion of close elections across all districts, in the year immediately after the election and inthe next scheduled election year respectively. There are no fixed effects included in generating thesegraphs. The disproportionately large drop in fatalities in politically competitive districts during electionyears is evident in the raw data itself as presented above. Notice that the polynomial in red ( i.e. the plotin the election year) has a steeper downward slope and has a extended flatter portion compared to thepolynomial in blue (the plot four years from a scheduled election year). This implies that the differencebetween accidents in competitive and noncompetitive districts increase leading up to elections.234","type":"literal","lang":"en"}],"http:\/\/www.europeana.eu\/schemas\/edm\/hasType":[{"value":"Thesis\/Dissertation","type":"literal","lang":"en"}],"http:\/\/vivoweb.org\/ontology\/core#dateIssued":[{"value":"2022-11","type":"literal","lang":"en"}],"http:\/\/www.europeana.eu\/schemas\/edm\/isShownAt":[{"value":"10.14288\/1.0416484","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/language":[{"value":"eng","type":"literal","lang":"en"}],"https:\/\/open.library.ubc.ca\/terms#degreeDiscipline":[{"value":"Economics","type":"literal","lang":"en"}],"http:\/\/www.europeana.eu\/schemas\/edm\/provider":[{"value":"Vancouver : University of British Columbia Library","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/publisher":[{"value":"University of British Columbia","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/rights":[{"value":"Attribution-NonCommercial-NoDerivatives 4.0 International","type":"literal","lang":"*"}],"https:\/\/open.library.ubc.ca\/terms#rightsURI":[{"value":"http:\/\/creativecommons.org\/licenses\/by-nc-nd\/4.0\/","type":"literal","lang":"*"}],"https:\/\/open.library.ubc.ca\/terms#scholarLevel":[{"value":"Graduate","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/contributor":[{"value":"Anderson, Siwan","type":"literal","lang":"en"},{"value":"Squires, Munir","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/title":[{"value":"Essays in development economics","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/type":[{"value":"Text","type":"literal","lang":"en"}],"https:\/\/open.library.ubc.ca\/terms#identifierURI":[{"value":"http:\/\/hdl.handle.net\/2429\/82217","type":"literal","lang":"en"}]}}