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Essays on British labour markets during the Second Industrial Revolution Milner, Benjamin 2020

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Essays on British Labour Markets During the SecondIndustrial RevolutionbyBenjamin MilnerB.A. (Honours), University of Saskatchewan, 2012M.A., Queen’s University, 2013A 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)November 2020c© Benjamin Milner, 2020The following individuals certify that they have read, and recommend to the Faculty ofGraduate and Postdoctoral Studies for acceptance, the dissertation titled:Essays on British Labour Markets During the Second Industrial Revolutionsubmitted by Benjamin Milner in partial fulfillment of the requirements for the degree ofDoctor of Philosophy in Economics.Examining Committee:Mauricio Drelichman, Associate Professor, Economics, UBCSupervisorFelipe Valencia Caicedo, Assistant Professor, Economics, UBCSupervisory Committee MemberThomas Lemieux, Professor, Economics, UBCUniversity ExaminerChristopher Kam, Associate Professor, Political Science, UBCUniversity ExaminerAdditional Supervisory Committee Members:Nicole Fortin, Professor, Economics, UBCSupervisory Committee MemberMarit Rehavi, Associate Professor, Economics, UBCSupervisory Committee MemberiiAbstractChapter 1 examines the importance of public education to occupational outcomes and inter-generational mobility. The UK’s 1870 Education Act, which introduced a public educationsystem in England and Wales, provides a unique historical context in which to explore this.Using newly digitized historical records and a regression kink design, I find that public schoolaccess improved a child’s chance of obtaining an occupation requiring literacy in adulthoodby as much as 13 pp. To study the reform’s effect on intergenerational mobility, I linkfather-son pairs across time using full-count historical censuses. I find that by targeting thelower classes, public school introduction significantly improved intergenerational mobility,decreasing the adult outcome gap between high- and low- class children by over 10%.Chapter 2 demonstrates how legislation can change the incentives for human capitalaccumulation in resource-dependant communities, and in doing so help insure against futureresource busts. I examine the UK’s 1860 Mining Act, which made literacy or schooling aprerequisite for children seeking to work in mines. Using a triple difference specification andfull-count census records linked across decades, I find that by decreasing the opportunity costand increasing the returns to schooling, the Act led to increased human capital acquisitionamong the children of coal miners. This improved their likelihood of holding human capital-intensive occupations in adulthood, particularly among children residing in parishes thatsubsequently experienced mining busts.Chapter 3 explores the effects conflict continues to have on labour and marriage mar-kets even after the shooting stops. Using variation in First World War death rates acrossiiiBritish communities, I find higher conflict death rates are associated with a fall in poverty,particularly among men, and an increase in employment, particularly among women. To-gether, these results suggest that while high death rates improved labour market conditionsfor those left behind, widowed women were likely forced into the labour market to avoidpoverty. Finally, I demonstrate that war-induced falls in the sex-ratio led to increases inout-of-wedlock births, confirming previous findings showing that men often utilize marriagemarket bargaining power to shirk childcare responsibility.ivLay SummaryThis thesis consists of three chapters, each set in the context of Britain’s Second IndustrialRevolution, which spanned from the mid-nineteenth century to the First World War. Chap-ter 1 examines the introduction of public schools in England and Wales in 1870, showingthat it significantly improved the quality of occupations children held in adulthood, andimproved equality of opportunity by targeting poorer children. Chapter 2 finds that, by re-quiring children working in mines to either prove literacy or attend school, the 1860 MiningAct increased education among the children of miners, and in so doing helped protect themagainst future downturns in the local mining industry. Chapter 3 explores the effects of con-flict, finding that communities with high First World War death rates experienced decreasedpoverty and increased employment after the war. However, these benefits disproportionatelywent to men over women.vPrefaceThis dissertation is original, unpublished, independent work by the author, Benjamin Milner.viTable of ContentsAbstract . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . iiiLay Summary . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . vPreface . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . viTable of Contents . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . viiList of Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xList of Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xiiAcknowledgements . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xiiiIntroduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 11 The Impact of State-Provided Education: Evidence from the 1870 Edu-cation Act . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 51.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 51.2 Literature Review . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 81.3 The Education Act of 1870 . . . . . . . . . . . . . . . . . . . . . . . . . . . . 121.4 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 171.5 Regression Kink Identification . . . . . . . . . . . . . . . . . . . . . . . . . . 211.5.1 Regression Kink Estimation and Results . . . . . . . . . . . . . . . . 241.6 Triple Difference . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 261.6.1 Model and Theory . . . . . . . . . . . . . . . . . . . . . . . . . . . . 261.6.2 Triple Difference Results . . . . . . . . . . . . . . . . . . . . . . . . . 301.7 Census Linkage and Mobility Estimation . . . . . . . . . . . . . . . . . . . . 341.7.1 Linkage Description . . . . . . . . . . . . . . . . . . . . . . . . . . . . 351.7.2 Mobility Regressions and Results . . . . . . . . . . . . . . . . . . . . 371.8 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 40vii2 Education as Insurance against Resource Busts: Evidence from the 19thCentury . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 642.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 642.2 Historical Background . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 672.2.1 Coal in 19th Century Britain . . . . . . . . . . . . . . . . . . . . . . 672.2.2 Child Labour in the Mines . . . . . . . . . . . . . . . . . . . . . . . . 682.2.3 Early Attempts to Regulate Child Labour . . . . . . . . . . . . . . . 712.2.4 1860 Mining Act . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 722.2.5 Enforcement of Mining Acts . . . . . . . . . . . . . . . . . . . . . . . 732.3 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 742.4 Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 752.4.1 Effect on the Extensive Margin of School Attendance . . . . . . . . . 762.4.2 Effect on Adult Occupation . . . . . . . . . . . . . . . . . . . . . . . 792.4.3 Booming vs. Busting Mines . . . . . . . . . . . . . . . . . . . . . . . 812.4.4 Effect of 1860 Act on those Compelled to Leave Mining . . . . . . . . 842.5 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 863 Post-Conflict Outcomes: Community-Level Effects of WWI Deaths inPost-War England and Wales . . . . . . . . . . . . . . . . . . . . . . . . . . . 1013.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1013.2 GBHGIS Data and Historical Context . . . . . . . . . . . . . . . . . . . . . 1063.2.1 Geography and Data Aggregation . . . . . . . . . . . . . . . . . . . . 1063.2.2 Census Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1073.2.3 Poor Law Union Pauperage Reports . . . . . . . . . . . . . . . . . . 1103.3 Soldier Data, Instruments, and Historical Context . . . . . . . . . . . . . . . 1113.4 Specifications . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1163.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1193.5.1 Poverty . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1193.5.2 Employment . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1203.5.3 Out-of-Wedlock Births . . . . . . . . . . . . . . . . . . . . . . . . . . 1213.6 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 122Bibliography . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 138A Appendix to Chapter 1 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 148A.1 Childhood vs Adult Parish of Residence . . . . . . . . . . . . . . . . . . . . 148A.2 Effect of Boards on School Supply and Attendance . . . . . . . . . . . . . . 150viiiA.3 Appendix: Reports to Parliament . . . . . . . . . . . . . . . . . . . . . . . . 154A.4 Appendix: Regression Kink Model . . . . . . . . . . . . . . . . . . . . . . . 157A.5 Appendix: Running Variable Density Tests . . . . . . . . . . . . . . . . . . . 159A.6 Appendix: Differences between RK and DDD estimates: Disproven Theories 160A.7 Appendix: Census Linking Procedure . . . . . . . . . . . . . . . . . . . . . . 164A.8 Appendix: Middle Initial Test for False Positives . . . . . . . . . . . . . . . . 165A.9 Appendix: More Conservative Matching Procedures . . . . . . . . . . . . . . 169A.10 Appendix: Alternative Mobility Measures . . . . . . . . . . . . . . . . . . . 172A.11 Appendix: Advantage of Higher Class Children . . . . . . . . . . . . . . . . 174B Appendix to Chapter 3 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 176B.1 Administrative Unit Descriptions . . . . . . . . . . . . . . . . . . . . . . . . 176B.2 Estimation of PLU 1921 Populations . . . . . . . . . . . . . . . . . . . . . . 178B.3 Possible Border Changes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 180B.4 Matching Administrative Geographies with Soldier Birthplaces . . . . . . . . 181B.5 Measurement error caused by migration and birthplace exclusion . . . . . . 183ixList of Tables1.1 Summary Statistics: Treated vs Untreated Parishes . . . . . . . . . . 421.2 Full 1881 Population vs Population Matched to School Data . . . . 431.3 Common Jobs by Literacy Requirement . . . . . . . . . . . . . . . . . 431.4 Years of Treatment Difference by Board Arrival Year and Age . . . 441.5 RK 2SLS Results at CCT Bandwidth . . . . . . . . . . . . . . . . . . . 451.6 Full Sample Triple Difference . . . . . . . . . . . . . . . . . . . . . . . . 451.7 1861 Placebo . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 461.8 Effect of Full Treatment, Dropping Partially Treated . . . . . . . . . 461.9 Full Sample Triple Difference, Tails Dropped . . . . . . . . . . . . . . 471.10 Only Treated . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 471.11 HISCLASS Categories . . . . . . . . . . . . . . . . . . . . . . . . . . . . 481.12 Full Sample Triple Difference. Dependent Variable: Class Dummy 481.13 Linkage Summary Statistics: Early Periods . . . . . . . . . . . . . . . 491.14 Linkage Summary Statistics: Late Periods . . . . . . . . . . . . . . . . 501.15 Comparison of Linkages . . . . . . . . . . . . . . . . . . . . . . . . . . . 511.16 Social Mobility Triple Difference . . . . . . . . . . . . . . . . . . . . . . 521.17 Triple Differences By Father’s Class . . . . . . . . . . . . . . . . . . . . 532.1 Low Skilled Occupation Earnings, England . . . . . . . . . . . . . . . 872.2 Summary Statistics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 872.3 1860 Act’s Effect on Likelihood of Attending School . . . . . . . . . 882.4 1860 Act’s Effect on Literate Occupations . . . . . . . . . . . . . . . . 882.5 Summary Statistics, Mining Parishes Only . . . . . . . . . . . . . . . 892.6 Triple Difference, Growing vs. Shrinking Mines . . . . . . . . . . . . 902.7 Mining Opportunities . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 902.8 Mining Opportunities Placebo: Children of Non-Mining Fathers . . 913.1 Original Data Aggregation Level . . . . . . . . . . . . . . . . . . . . . . 1243.2 Description of PLU Aggregation into City Level Units . . . . . . . . 124x3.3 Population Summary Statistics . . . . . . . . . . . . . . . . . . . . . . . 1253.4 Employment Rate Summary Statistics . . . . . . . . . . . . . . . . . . 1253.5 Poor Law Union Pauperage Rate Summary Statistics . . . . . . . . . 1263.6 Within Wedlock Birth Share by LGD . . . . . . . . . . . . . . . . . . . 1273.7 Death Records Summary Statistics . . . . . . . . . . . . . . . . . . . . 1273.8 Estimated Death Rate Summary Statistics . . . . . . . . . . . . . . . 1273.9 Change in Total Able-Bodied Pauperage Rate, 1911-1921 . . . . . . 1283.10 Difference in Growth of Outdoor Able-Bodied Pauperage Rates,Male Growth - Female Growth . . . . . . . . . . . . . . . . . . . . . . 1293.11 First Stage of Tables 3.9 and 3.10 . . . . . . . . . . . . . . . . . . . . . 1303.12 County Employment Rate Change, 1911-1921 . . . . . . . . . . . . . 1313.13 Difference in growth rates of Employment (Male Growth - FemaleGrowth) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1323.14 Within Wedlock Birth Rate, Using Gender Specific OccupationData . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1333.15 Within Wedlock Birth Rate, Using Total Occupation Data . . . . . 134A.1.1 Childhood vs. Current Parish of Residence . . . . . . . . . . . . . . . 149A.2.1 Merged vs Unmerged Schools . . . . . . . . . . . . . . . . . . . . . . . 152A.2.2 School Supply Per Capita Diff-in-Diff, 1871 and 1888 . . . . . . . . 153A.2.3 1888 School Attendance Rate . . . . . . . . . . . . . . . . . . . . . . . 153A.5.1 Smoothness tests of 1871 School Supply density at the cutoff . . . 160A.6.1 Triple Diff Within RK Bandwidth . . . . . . . . . . . . . . . . . . . . 163A.6.2 Difference-in-differences for those over 35 . . . . . . . . . . . . . . . . 163A.8.1 Overrepresented Combinations among Differing Middle Initials . . 167A.8.2 Estimated Linking Characteristics . . . . . . . . . . . . . . . . . . . . 168A.9.1 Social Mobility Triple Difference, Matches Unique Within 5-yearBand . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 171A.10.1 Social Mobility Triple Difference, Alternative Measures . . . . . . 173A.11.1 Advantage of Untreated High Class Children, 1901 . . . . . . . . . 175xiList of Figures1.1 School Board Formation by Year . . . . . . . . . . . . . . . . . . . . . . 541.2 Pre-Treatment School Supply . . . . . . . . . . . . . . . . . . . . . . . . 551.3 Parishes that Received School Boards . . . . . . . . . . . . . . . . . . . 561.4 First Stage Kink . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 571.5 Second Stage Kink . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 581.6 Second Stage Kink Placebo Test: Same Age, Untreated Year . . . . 591.7 Second Stage Kink Placebo Test: Same Year, Untreated Age . . . . 601.8 Running Variable Density . . . . . . . . . . . . . . . . . . . . . . . . . . 611.9 Varying Bandwidth . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 621.10 RK Donut Analysis (Exclusion around kink) . . . . . . . . . . . . . . 632.1 Use of Child Labour in Mines, 1861 . . . . . . . . . . . . . . . . . . . . 922.2 Use of Child Labour in Mines, 1861, Mining Parishes Only . . . . . 932.3 Coal Mining Parishes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 942.4 1881 Occupation Attainment by 1861 Age . . . . . . . . . . . . . . . . 952.5 1901 Occupation Attainment by 1881 Age . . . . . . . . . . . . . . . . 962.6 Mining Transmission from Fathers to Sons, 1861 . . . . . . . . . . . . 972.7 Coal Mining Parishes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 982.8 1861 Coal Mining Parishes . . . . . . . . . . . . . . . . . . . . . . . . . . 992.9 1881 Coal Mining Parishes . . . . . . . . . . . . . . . . . . . . . . . . . . 1003.1 Administrative Geographical Hierarchy . . . . . . . . . . . . . . . . . . 1353.2 Changing Sex Ratio . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1363.3 Poor Law Union Soldier Deaths to Population Ratio . . . . . . . . . 137A.3.1 1871 Survey Report . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 154A.3.2 1879 School Boards . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 155A.3.3 1888 Schools . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 156A.6.4 Population Weighted RK . . . . . . . . . . . . . . . . . . . . . . . . . . 162xiiAcknowledgementsThanking the many individuals who supported the construction of this thesis is a dauntingand humbling task. My first and greatest debt is to my supervisor, Mauricio Drelichman:without his sage advice, countless hours of editing, and general support and encouragementthroughout this process, I doubt this thesis would have ever seen the light of day. I am alsoindebted to Felipe Valencia Caicedo who, even prior to arriving at VSE, has been incrediblygenerous with his time, support, and wise council. Kevin Milligan, who gave me a chance asa research assistant early on in my studies and continued to mentor me throughout – I owehim much as well. I also need to thank Nicole Fortin and Marit Rehavi, whose insightfulcomments and suggestions throughout this process played an important role in shaping theoutcome. This barely scratches the surface of VSE faculty members who have helped mealong the way. In particular, Siwan Anderson, Patrick Francois, David Green, ThomasLemieux, Matt Lowe and Angela Redish have all provided extremely helpful guidance andsupport over the years.I am also truly thankful for my classmates at VSE. Nathan Canen, Thomas Cornwall,Matthew Courchene, Jeffrey Hicks, Bert Kramer, Aruni Mitra, Kim Nguyen, Juan FelipeRiano Rodriguez, Rogerio Santarrosa, Gaelle Simard-Duplain, Michael Wiebe – they werethe ones who helped keep me sane, who shared in the highs and lows, who understood thedifficulties faced because they had faced them as well.There are many to thank outside of VSE as well. My professors at Queen’s Universityand the University of Saskatchewan, especially Eric Howe, whose encouragement of a lowlyxiiiundergrad provided the confidence needed to pursue post-graduate studies. Those outsideof academia, too numerous to name, who provided me with friendship and emotional sup-port along the way. Finally, my parents, Barb and Cam, and my brothers, Sam and Jake:ceaselessly encouraging, always there when I needed you, words cannot express how gratefulI am for each of you.xivIntroductionLost to living memories, Britain’s Second Industrial Revolution - spanning from the mid-nineteenth century to the First World War - can seem irrelevant, part of a distant past. Yetmany of the issues faced then mirror those faced today. Society grappled with the issueof inequality, and struggled to ensure that one’s fate was not determined by that of theirparents. The role of the state in education provision was hotly contested. The fates ofresource-dependant communities rose and fell based on forces largely outside their control.And the slaughter of war emptied communities of many of their most able. Examining howthese issues were addressed then, and the resulting outcomes, can inform how they shouldbest be addressed today. This is the motivating force behind the three chapters of this thesis.In Chapter 1, I examine the impact of the 1870 Education Act. This reform created apublic school system in England and Wales, marking the first time the state stepped into therealm of school administration in these regions. It thus provides a unique window throughwhich one can study the impact of publicly provided schools. While many previous scholarshave examined the state’s role in school provision, few if any have studied it outside themodern context, where public schools are ubiquitous. The alternative of little to no directstate involvement has remained relatively unexplored. To fill this hole in the literature,I make use of newly digitized school records, as well as full-count individual-level censusrecords. Utilizing a kink in treatment probability created by a well-defined rule, I use aregression kink design to show that access to public schooling increased a child’s probabilityof obtaining an occupation requiring literacy in adulthood by as much as 13 pp. For children1further removed from the kink, I use a triple difference specification to verify the effect anddemonstrate that each additional year of public school access significantly improved a child’schance of obtaining a high social status occupation in adulthood.I also examine the 1870 Education Act’s effect on intergenerational mobility. Ensuringequality of opportunity is an oft-cited reason for public education expenditure, yet evidencedemonstrating that schooling evens the playing field has thus far been weak. While recentwork by Chetty et al. (2014) and Chetty & Hendren (2018) have found a positive cor-relation between a school quality and intergenerational income mobility, causality has notbeen demonstrated. Indeed, several studies, including Grawe (2010), Parman (2011), andRauscher (2016), have suggested that improvements to public school provision often worsenintergenerational mobility, due to affluent children capturing most of the associated gains.This suggests that targeted reform, aimed specifically at improving the outcomes of the dis-advantaged, might have more positive effects on mobility. By providing schools specificallyfor the working class, the 1870 Education Act provides an ideal opportunity to test thistheory. To that end, I conduct what is to my knowledge the largest linkage of full-counthistorical English censuses in the literature, following nearly 4 million individuals across thefull-count 1861, 1881, and 1901 censuses from childhood to adulthood. Using this sample, Iagain use a triple-difference specification to demonstrate that the 1870 Act’s targeting suc-cessfully improved intergenerational mobility, narrowing the gap in occupational attainmentbetween lower- and higher-class children in treated areas by over 10%.Chapter 2 examines another education reform: the 1860 Mining Act. Prior to it, boysas young as 10 were allowed to work in mines, regardless of education. Similar to today,resource extraction in 19th century Britain provided relatively well paying work to low skilledlabourers. As such, miners’ sons, being very likely to become miners themselves in adulthood,had little incentive to acquire human capital.This negative relationship between resource extraction and human capital acquisition hasbeen found in modern settings as well, from Norway (Butikofer et al., 2018) to North Dakota2(Rickman et al., 2017). Indeed, it has often been described as a crucial part of the “NaturalResource Curse,” slowing economic growth in locations dependant on resource extraction.1Understanding if and how this relationship can be counteracted is thus an important policyquestion, to which the 1860 Act provides some answers. By requiring either literacy orschool attendance from boys under 12 working in mines, the Act improved the incentivesfaced by miners’ sons to acquire an education. Using a triple difference comparing miners’sons against those from other periods, older cohorts, and non-miners’ sons, I demonstratethat school attendance rates rose as a result of the reform. Further, using linked census data,I find that treated cohorts were nearly 17% more likely to obtain an occupation requiringliteracy in adulthood than would otherwise have been the case. Finally, I examine whetherthe increased human capital resulting from the Act served to shield the treated against futureresource shocks. Using local mine growth to instrument for mining employment opportunitiesand allowing the treatment effect to vary accordingly, I estimate that the Act increased bynearly 30 pp the likelihood that those who were forced out of the industry subsequentlyobtained a literate occupation.In Chapter 3, I study the effects of the event that brought an end to the Second IndustrialRevolution: the First World War. In particular, I examine the impact soldier deaths had onpoverty, employment, and marriage markets of their home communities post-war.Ex ante, the effects on employment and poverty are especially uncertain. On one hand,Malthusian arguments suggest that raising the death rate should improve the living standardsof survivors. On the other, the patriarchal nature of early 20th century Britain meant thatmany of the soldiers who died were previously their family’s sole breadwinner. The widowsand orphans created by the war may have been forced to seek alms. Using a difference-in-difference approach, I find that soldier deaths lowered post-war local poverty levels and mayhave risen employment rates among those left behind, lending support to the Malthusianhypothesis. However, the effects varied by gender - while women saw the greater gains in1See, for instance, Asea & Lehiri (1999) or Douglas & Walker (2017).3employment, it was men who experienced the greater fall in poverty rates, suggesting thatmany of the newly employed women were compelled to seek work so as to avoid pauperage.Concerning marriage markets, theory is more certain: a decrease in the male to femaleratio should give men more bargaining power. I document a negative relationship betweenthe sex-ratio and the rate of out-of-wedlock births, confirming previous findings that suggestmen use their increased bargaining power to shirk childrearing responsibilities.4Chapter 1The Impact of State-ProvidedEducation: Evidence from the 1870Education Act1.1 IntroductionDuring the 20th century large improvements in education provision coincided with rapidand inclusive economic growth. Goldin & Katz (2009) called this era the “Human CapitalCentury”.1 Today education accounts for over 10% of global public expenditures, totallingnearly $4 trillion annually, and many point to it as the key to upward social mobility.2 Yet,despite the faith and fortunes staked on education, important questions remain unanswered.The role of the state in education provision and the impact of public schooling continue tobe sources of debate in both political and academic spheres. While recent works by Chettyet al. (2014) and Chetty & Hendren (2018) find that places exhibiting high intergenerationalmobility also tend to have good schools, causal identification has yet to be cleanly established.I examine the impact of publicly provided schooling on occupational outcomes and in-1Claudia Goldin & Lawrence Katz, The Race between Education and Technology, 2009, ch. 12UNESCO Global Education Monitoring Report (2019), pg. 235-236.5tergenerational mobility, exploiting the introduction of public schools in England and Walesby the 1870 Education Act.3 This reform offers several advantages relative to modern-daysettings: the selection of treated areas followed a well-defined rule, yielding clean causalidentification; the previous system consisted exclusively of private schools; and the reformeffectively targeted the working classes. Armed with freshly digitized historical data on therollout of public schools, as well as full-count individual-level census records, I use a regres-sion kink design to show that access to public schooling increased a child’s probability ofobtaining an occupation requiring literacy in adulthood by as much as 13 pp. I then use atriple difference specification to show that the effect extended to children further removedfrom the kink, and that the quality of occupational outcomes increased with each additionalyear of schooling. Finally, to examine the effect of public schools on intergenerational mo-bility, I link nearly 4 million individuals across the full-count 1861, 1881, 1901 censuses.To my knowledge, this is the largest linkage of full-count historical English censuses in theliterature. Once again using a triple-difference framework, I show that by targeting childrenof the lower classes, public schools increased intergenerational mobility by narrowing the gapin occupational attainment between lower- and higher-class children in treated areas by over10%.As early as 1962, Milton Friedman argued that public schools were unnecessary and thatthe state should instead support choice between private providers of education.4 Debate con-cerning the state’s role has continued since, producing a massive body of academic work.5Yet throughout this literature the context studied is always one of public school dominance(Hanushek (2002)). Friedman’s counterfactual of little to no direct state involvement re-mains unexamined. To better understand the impact of state education provision, one must3Throughout this paper I refer to state-provided schools as “public” and all others as “private”. Otherworks use these terms differently. In the literature, “public” occasionally refers to any school that receivedgovernment subsidies, which included many church and charity school as well as state schools. In othercontexts, “public school” refers to the exclusive private schools attended primarily by the upper class.4Milton Friedman, Capitalism and Freedom, 1962, ch. 6.5Recent papers include Dronkers & Avram (2010), Bravo et al. (2010), Lefebvre et al. (2011), Elder &Jepsen (2014), Thapa (2015), Nghiem et al. (2015), and Feigenberg et al. (2017). For a review of earlierworks, see Hanushek (2002)6examine a scenario where private schools were the dominant force and public schools werein a fledgling state. Prior to 1870, all primary schooling in England and Wales was privatelyprovided, funded by charity, fees, and government subsidies. The Education Act introduceda public system for the first time, thus providing the ideal context to study the effect ofpublicly provided education.The Education Act also provides a unique opportunity to study the intergenerationalmobility effects of targeted education reform. Recent works by Chetty et al. (2014) andChetty & Hendren (2018) show that intergenerational income mobility varies greatly acrossthe US, and that highly mobile areas also tend to have higher quality schools. However, bothworks stress that the relationship they document between schools and mobility is purelydescriptive. Card et al. (2018) document a negative relationship between school quality andthe intergenerational persistence of years of schooling using 1940 US census data, but do notexamine adult outcomes. The few existing works that extend the analysis to adult outcomessuggest that improvements to public school provision and quality actually tend to decreaseintergenerational mobility. Parman (2011) shows that public school expansion in Iowa atthe turn of the 20th century worsened intergenerational income mobility. Similarly, Grawe(2010) uses US census data from 1940-2000 to demonstrate that state-cohorts with low pupil-to-teacher ratios experienced less intergenerational mobility; Rauscher (2016) finds that 19thcentury compulsory school attendance laws in US states initially reduced intergenerationalmobility, with it eventually returning to pre-reform levels. The reason typically given for thissurprising result is that affluent children are better able to take advantage of improvementsin public education, suggesting that improvements targeted at the disadvantaged might havebetter results.6 I show that this was precisely the case in the context of the 1870 reform, whichaffected and benefited almost exclusively working class children, improving intergenerationalmobility as a result.The remainder of the paper is structured as follows. Section 2 frames this paper’s contri-6Rauscher (2016), pg. 1698.7bution by providing a review of the related literature. Section 3 describes the 1870 EducationAct and its historical context in detail. Section 4 describes the data and its collection. InSection 5 I describe the regression kink framework and results. In Section 6 I turn to thetriple difference specification and results. Finally, in Section 7 I outline the census linkingprocedure, and use the linkage to demonstrate the impact public school introduction had onintergenerational mobility. I summarize the findings in Section 8 and discuss future avenuesof research.1.2 Literature ReviewIn addition to contributing to the discussions comparing public and private schooling andthe impact of public schools on social mobility, my work relates to several other strands ofliterature. In showing how education affected the job prospects of those who received it, ittouches on the well-trodden topic of individual returns to education. Since the late 1950s,when the importance of human capital was formalized in the works of Becker, Mincer, andothers, the topic has received considerable attention.7 It is safe to say few casual relationshipshave been more thoroughly established than the modern link between education and income.8If and how the relationship has changed across time is less clear. Clark (2005) suggests thatthe return to skill in England – measured by comparing the wages of carpenters vs generallabourers – varied widely over the period from 1200-2000. Long (2006) finds a positivecorrelation between education and occupation outcomes in 19th century England (more onthis below). I prove that this correlation was in fact causal: better education improved adultoccupation outcomes in the late 19th century.I also add to the literature examining the role of education during what is known as the7Becker (1962), Mincer (1958). Of course, the notion of human capital goes back much further: in 1776,Adam Smith wrote that “the improved dexterity of a workman may be considered in the same light as amachine or instrument of trade which facilitates and abridges labour, and which, though it costs a certainexpense, repays that expense with a profit.” (Smith 1963, pg. 214)8For surveys of early work, see Card (1999, 2001) or Psacharopoulos & Patrinos (2004). For more recentevidence see, for example, Gennaioli et al. (2012), Oreopoulos & Petronijevic (2013), or Hanushek et al.(2015).8Second Industrial Revolution (1870-1914). It is generally accepted that education playedat most a small role in the First Industrial Revolution (Mitch, 1999).9 Recent work hassuggested that this changed during the Second Industrial Revolution. Mokyr (1998) positsthat during this period the rate of innovation increased, with the spread of people and ideasfacilitated by the rapid expansion of railroad and communication networks. Maloney &Valencia (2017) show the important role engineers played in generating and applying newtechnologies during the Second Industrial Revolution, suggesting the importance of the uppertail of the education distribution during this time. Squicciarini (2017) demonstrates thatCatholicism – which she suggests depressed educational quality at the time – was negativelycorrelated with industrial employment in French regions after 1870, but not before. Similarly,Becker et al. (2011) find evidence that better educated regions in Prussia showed greaterindustrialization in both 1849 and 1882. I build upon this literature by examining theeffects of education during this time at the individual level, and measuring its impact onintergenerational mobility.Beyond what it can teach us about the effect of public schooling, the impact of theEngland’s first foray into public school provision is of great historical interest in and ofitself. Hamilton (1883), published only 13 years after the 1870 Act’s passage, suggeststhat the Act had a positive impact on national education, and subsequent historians havein general supported this view.10 However, Hamilton only had aggregate data, and fewsubsequent statistical analyses have been at a much finer level. This has left some room fordisagreement over the Act’s impact. In particular, West (1970, 1975) points out that schoolsupply was growing quickly by private means before the passage of the reform, and arguesthat public intervention crowded out private investment in schools and thus had at best aminimal impact on total school supply. My work is the first to gather and analyse pre- and9An important caveat to this statement is that the very upper tail of the education distribution likelyplayed a significant role. This idea is presented in Mokyr (2005), and Squicciarini & Voigtla¨nder (2015) haverecently provided empirical evidence supporting it, showing regions with a highly educated elite industrializedquicker. However, the reform studied here specifically targeted working class education, and thus likely hadlittle impact on the upper tail of the education distribution.10See, for instance, Hamilton (1883), Middleton (1970), Armytage (1970), or Mitch (1986, 1992, 1996).9post- reform parish level school figures, as well as the first to study the reform’s impact onindividuals into adulthood. The results show that not only did the reform have a positiveeffect on school supply and attendance, but that those positive effects spilled over into adultoutcomes.More broadly, my work studies the effects of major education reform. Close counterpartsin this regard are Duflo (2001, 2004), which also examine the impact of a large positiveshock to school supply and observe positive labour market effects. Goldin & Katz (2008)is another close relation, showing that compulsory schooling and child labour laws played asmall but significant role in the arrival of mass secondary schooling in early 20th century US.Indeed, my use of an education policy reform as a natural experiment mirrors the prolificliterature using compulsory schooling laws in the same way.11 Montalbo (2019) parallelspart of my approach in its use of a regression discontinuity to identify positive effects ofa historical education reform: France’s 1833 Guizot Law. However, without the benefit ofindividual level data, he is necessarily silent on the effect on intergenerational mobility. Bylinking fathers and sons across time I am able to push further than these previous works andanalyse how social class interacted with access to schooling.Blanc & Wacziarg (2020) also discuss, among many other things, the effects of theFrance’s Guizot Law. Aided by a linkage of nearly 1000 father-son pairs from a rural village,they observe little effect of reform induced school expansion on social mobility. However,their focus on a single village, while enabling incredibly detailed analysis, also limits the ex-ternal validity of the results, the ability to control for migration, the power of the estimatesand the ability to control for endogeneity issues. I am able to largely address these concernsby studying the effects of education expansion at the national level, utilizing full-count cen-sus records to link several million father-son pairs and making use of the idiosyncratic rollout of the reform to cleanly identify its effects.I also add to the growing list of studies that have utilized regression kink analysis. This11See, for instance, Angrist & Keueger (1991), Margo & Finegan (1996), Acemoglu & Angrist (2000), andOreopoulos et al. (2006).10identification technique, described in detail in Section 1.5, is conceptually similar to a regres-sion discontinuity, but relies on a discontinuity in the first derivative (a kink), as opposedto the level (a jump), of the treatment schedule. While its use has been growing in publicfinance, labour, and health, my paper is among the first, along with Miller et al. (2018),to apply the technique in the economic history literature. It is also one of the first papers,besides Dong (2018) and Sohn & Lee (2019), to utilize a kink in the probability of receivingtreatment, as opposed to in its magnitude.Long (2006) is the contribution closest to my paper. It also uses late 19th centuryEnglish census data to measure the impact of education on occupation outcomes. Usinga nationally representative sample of 5,337 men linked across the 1851 and 1881 censuses,Long finds that 1851 school attendance is related to higher 1881 occupation status, evenafter controlling for father’s occupation and other family characteristics. My results supportthis, showing, among other things, that those treated with improved primary education aremore likely to have higher 1901 occupation status. However, several important differencesexist between our works. I am able to address the endogeneity of the education choice, usingan external policy shock (the 1870 Act) that varies by location. I also show how policy canaffect intergenerational mobility. Long is limited in his study of mobility both by his lack ofa policy instrument and his small sample. As documented in detail in Section 1.7, my papermatches historical full-count censuses for England and Wales. The resulting linkage of nearly4 million men enables me to identify the policy’s mobility effects with precision, while stillaccounting for age and parish level differences. Finally, Long focuses on 1881 occupations,a generation earlier than 1901 results I examine. This is significant: the Second IndustrialRevolution was just beginning in 1881, while by 1901 it was well underway.111.3 The Education Act of 1870William Forster – the 1870 Education Act’s architect and leading advocate in parliament –stated that the Act’s main purpose was to extend and improve “the elementary educationchiefly of the working classes,” by increasing supply, attendance, and quality.12 Accordingto Middleton (1970), “it is not too extravagant to claim that [the 1870 Education Act]introduced a new type of society which radically altered the child’s place in the community.”13This is not an overstatement. In the ten years following the its passage, the Act caused over2,000 parishes to form school boards (Figure 1.1).14 These in turn created thousands ofpublic schools, known as “board schools”. This represented the first public sector foray intoschool administration in English history, and was massive in scale. By 1900 nearly 5,700board schools existed, attended by nearly 1,900,000 children.15There were separate, contemporary legislative acts that addressed middle and upper classeducation: the 1869 Endowed Schools Act for the middle class, and the 1868 Public SchoolsAct for the upper class. Both were far more limited in scope, however. The Public SchoolsAct only concerned the administration of the nine leading primary schools in the nation,while the Endowed Schools Act was concerned with the 1/7 of the population labelled asmiddle class by the Registrar General and mainly sought to ensure endowments at existingschools catering to this class were properly managed.16 In contrast, it was estimated inthe legislation of the 1870 Act that the lower classes it served represented over 85% of thepopulation.17Prior to 1870, pressure for large-scale education reform in England and Wales had beenbuilding up for decades. Scotland, Germany, and large parts of the US had all provided12McCann (1970), pg. 13413Middleton (1970), pg. 166.14The parish, also known as the civil parish, represented the smallest unit of local government in the UKat the time. Their borders were originally based on those of the Church of England’s ecclesiastic parishes,but had diverged prior to 1870. See Gregory and Southall (2000) for more details.15Lawson & Silver (2013), pg. 31416Middleton (1970), pg. 168-170.17“Report of the Committee of Council on Education (England and Wales); 1870-71,” UK parliamentarypaper, 1871, Vol. 22, paper C.406.12universal primary education since the early 19th century. Several failed attempts at similarreforms had taken place in the 1850s and 60s.18 By 1870, a large and diverse coalition ofliberals, non-conforming religious believers, industrialists, and trade unions had formed topush the Act through parliament. Their motivations varied. In 1867, the franchise had beenextended to nearly all working class men, and some thought it important to educate thesenew voters.19 Non-conforming religious believers disliked the Church of England’s role inschool provision, and preferred the state provide non-denominational education instead.20Finally, both industrialists and trade unionists viewed education as central to improving theproductivity of their workers and members, respectively.21 There was already concern thatEnglish industry was falling behind its American and German rivals, and many blamed theeducation, or lack thereof, of the English workforce. Forster expressed the sentiment of theindustrialists well when he stated that “upon the speedy provision of elementary educationdepends our industrial prosperity.”22Prior to the Act’s passage, schooling (where it existed at all) was provided through amixture of private and church-run schools, which in turn were funded through a combinationof charity, fees, and government subsidies.23 The Act sought to “fill in the gaps” where theseinstitutions fell short of providing sufficient school space. To that end, school space wasjudged by government inspectors, and those parishes deemed to have insufficient space forchildren ages 5-12 were forced to elect school boards. These boards, under supervision fromLondon, were to construct and run board schools, funded through a mixture of local landtaxes and government subsidies and loans.Gaps in school supply were very common prior to the reform. Figure 1.2 shows thegeographic distribution of school supply. The government judged parish primary schoolsupply to be sufficient if spots were provided for at least 1/6 of the total population. In its18Lawson & Silver (2013), pg. 30819Ibid, pg. 30820Richards (1970)21McCann (1970)22Middleton (1970), pg. 16723For a more detailed description of the providers of education prior to 1870, see Mitch (1992).13instructions to inspectors, the Board of Education stated that,“In ordinary cases . . . it may be assumed that accommodation in elementaryschool will be required for one sixth of the entire population. This has been therule hitherto followed . . . and it is probably sufficient for all practical purposes.”24This 1/6 rule, widely accepted throughout the second half of the 19th century, was basedon the calculation that approximately 6/7 of the population belonged to the working classfor whom parish schools were provided, and a little over 1/6 of the population was of schoolage (5-12).25 Examination of the 1871 survey of school space suggests only 30% of parishes,representing less than a quarter of the total population, met this requirement at the time.26The 1/6 rule was not hard and fast. Comparing Figure 1.2 with Figure 1.3, which showswhere boards were formed, one can see that some parishes above the 1/6 threshold receivedboards, while many below did not. The most important reason for this was that parisheswere given a grace period, during which they could attempt to fill any school insufficiencyprivately.Before a parish was compelled to form a school board, several steps had to be taken.First, the central Board of Education needed to determine that a parish lacked sufficientschool space and provide notice of the deficiency to the parish.27 This involved sending aninspector to the parish in person, and appears to have been a time consuming process giventhat some parishes did not receive notice until 1874.28 After notice was given, local schoolproprietors and land owners were allowed one month to dispute the deficiency and demand a24“Committee of Council on Education. Instructions to H.M.Inspectors of Schools, May 1871, relativeto Inquiries into School Supply of their Districts,” pg. 2. UK parliamentary paper, 1883, Vol. 53, paperC.3602.25“Report of the Committee of Council on Education (England and Wales); 1870-71,” UK parliamentarypaper, 1871, Vol. 22, paper C.40626“Return of Civil Parishes in England and Wales under Education Act, of Population, Rateable Value,Number of Schools and Scholars in Attendance.” UK parliamentary paper, 1871, Vol. 55, paper 201.27“The Elementary Education Act, 1870,” Section 8, reprinted in “Report of the Committee of Councilon Education; with appendix 1870-71” UK parliamentary paper, 1871, Vol. 22, paper C.40628“Report of the Committee of Council on Education (England and Wales); with appendix 1873-74.”, UKparliamentary paper, 1874, Vol. 18, paper C.101914public inquiry.29 If no inquiry was needed, or after it was held, a final notice of the deficiencywas to be provided to the parish. If a deficiency still existed six months after the posting ofthis final notice and was not in the process of being alleviated through the construction of aschool, the parish was to be compelled to form a school board.30Landowners and the established church were united in opposing “the dread intrusion of aSchool Board.”31 The opposition of the landowners is unsurprising, since school boards werepartially funded by local land taxes. Further, landowners typically did not belong to theclass that sent their children to board schools, and, unlike industrialists, they stood to gainlittle from a more educated workforce.32 Goni (2018) empirically verifies the opposition oflandowners to the Act, documenting a negative relationship between school board fundingand landowner power across parishes. At the same time, the Church of England viewed theAct as a “source of great danger,” both to its own influence and to the moral fabric of thenation.33This antipathy meant that, to avoid school boards, small school deficiencies were oftenfilled privately by local elites during the grace period. However, the greater a parish’s pre-reform school supply deficit was, the more likely it was to form a board, presumably due tothe increasing cost the local elite faced to fill it privately. Parishes with sufficient pre-reformschool supply were allowed to voluntarily form school boards, but this option was rarelyexercised. The result is that a kink in treatment probability existed at the 1/6 cutoff, ascan be seen in Figure 1.4, which compares the empirical frequency of eventually receiving aschool board with pre-reform school supply. Section 1.5 describes how I exploit this kink toidentify the treatment effect of the reform.Table 1.1 compares the summary statistics of parishes that received school boards withthose that did not. Unsurprisingly, school supply in 1871 was lower among parishes that29“The Elementary Education Act, 1870,” section 930Ibid, Section 10.31Thompson (1963), pg. 20832Galor & Moav (2006); Galor, Moav & Vollrath (2009)33Platten (1975)15eventually received school boards. These parishes were on average more urban, with largerpopulations and a higher proportion of non-agricultural workers. While school boards clearlywere not randomly distributed, for the identification strategies used here they do not have tobe. Both the regression kink design and the triple difference-in-differences solve the selectionproblem based on minimal and flexible assumptions, as described in Sections 1.5 and 1.6.Prior to the passing of the Act, Forster noted that“there are vast numbers of children utterly untaught, or very badly taught,because there are too few schools, because many schools are bad schools, andbecause many parents either cannot, or will not, send their children to school.”34As already established, school boards addressed the issue of “too few schools”. They alsosought to address the problems of “bad schools” and parents who “cannot, or will not, sendtheir children to school.” While board schools did charge fees to those able to pay, thesewere typically lower than those charged by private schools,35 and were remitted for familiesdeemed unable to pay.36 Additionally, board officers were given the right to fine parents ofabsentee children aged 10 and under, and the discretion to pass bylaws requiring attendanceup to age 13. Outside the boards, schools were unable to mandate attendance until after1880, and even then only for children up to age 10.37 Further, there is anecdotal evidence ofhigher teacher quality in board schools relative to private schools. An 1861 parliamentaryreport on education noted that “The teachers of them [for-profit schools] have often no specialfitness, ... but have taken up the occupation in default or after the failure of other trades.”38Others have suggested that the operators of these schools were often themselves illiterate.3934Middleton (1970), pg. 17035Platten (1975)36“The Elementary Education Act, 1870,” section 1737The effectiveness of compulsory schooling laws in the era is a matter of debate. Middleton (1970)suggests that “the early [school board] bye-laws usually contained the loophole of ‘reasonable excuse’ fornon-attendance” (pg. 175). Landes & Solomon (1972) find little evidence of compulsory schooling lawsincreasing enrolment in the US from 1880-1910. However, Margo & Finegan (1996) do find significantattendance effects in the US using the 1900 census38J. Fraser, “Report of the Commissioners appointed to inquire into the State of Popular Education inEngland” (Newcastle Report), pg. 38. UK parliamentary paper, 1861, Vol. 21, paper 2794.39Gardner (1984), 118; Hurt (1971), pg. 625-629.16In contrast, teachers at board schools were generally drawn from teacher training colleges.40Further, classes were examined annually by government inspectors to ensure standards ofefficiency were met.41Through multiple channels, including increased supply, lowered fees, better enforced at-tendance, and better quality of instruction, school boards brought improvements in educationto the working classes. This motivates their use throughout this work as a source of a pos-itive shock to education provision. Nonetheless, in Appendix A.2 I verify this ‘stage zero’effect, proving that school boards dramatically increased school supply and attendance.1.4 DataThis project draws upon several primary sources never before used in empirical work. Pre-treatment school supply and population figures are gathered from a national survey adminis-tered immediately following the passage of the reform. Local parish officials were instructedto fill out returns requesting total local school capacity, defined as a tenth of school squarefootage. The results were published in an 1871 report to parliament.42 Using optical char-acter recognition software I digitized the records of all 14,094 parishes surveyed.43This represents the universe of parishes laying outside of municipal boroughs. Parisheswithin municipal boroughs were not administered the survey and thus are not includedin the data.44 Thus, parishes in the cores of many major cities, including London, areexcluded from the analysis. Nonetheless, it would be wrong to view the remaining parishesas exclusively rural. Many cities, such as West Bromwich and Wolverhampton, did not haveborough status, while many densely populated suburbs, such as Croydon and West Ham,lay outside of boroughs. As shown in Table 1.2, where I compare the general population to40West (1970), pg. 166-16941“The Elementary Education Act”, section 71.42“Return of Civil Parishes in England and Wales under Education Act, of Population, Rateable Value,Number of Schools and Scholars in Attendance”, UK parliamentary paper, 1871, Vol. 55, 201. A sample ofthe report, showing 54 parish records spread across two pages, is shown in Appendix Figure A.3.1.43Characters classified as uncertain in the OCR output were verified by hand.44There were 221 municipal boroughs at the time, and each often contained many parishes.17those residing in included parishes, over 24% of those included resided in parishes with apopulation density greater than 4 people per acre (or 2560 per square mile). Further, thelinked sample used in Section 1.7 includes adults residing in municipal boroughs, so long asdata from their childhood parish of residence is available.Pre-treatment school supply is mapped in Figure 1.2. Few parishes at the time met the1/6th rule for school supply, and many had no school space whatsoever.To determine which parishes ended up receiving school boards, I use the Board of Edu-cation’s 1878-79 Annual Report to Parliament, which records all 2,398 parishes that formedschool boards, along with formation date for each.45 I digitized this information by hand,and matched it to the 1871 survey data. As can be seen in Figure 1.3, while boards weremore common in some areas - in particular the Southwest and Wales - they were formedacross the country, with more than one in every English and Welsh county. Comparing Fig-ures 1.2 and 1.3 one can see that, as expected, boards were more likely to form in parisheslacking school supply prior to the reform. Table 1.1, which compares parishes that formedboards with those that did not, verifies this fact.To observe the effect board formation had on school supply and attendance, I hand-collected these variables at the parish level from the Board of Education’s 1888-89 AnnualReport to Parliament, published nearly ten years after the last boards were formed.46Several control variables were added from other sources. Local religiosity is controlled forusing denominational church attendance from the 1851 Religious Census.47 Parish distancefrom London was constructed using GIS software, after matching parishes to shape files oftheir historical boundaries.48The parish data is merged with individual data from the 1861, 1881, and 1901 censuses.45“Report of the Committee of Council on Education (England and Wales); with appendix. 1878-79”,UK parliamentary paper, 1878-79, Vol. 23, paper C.2342. Appendix Figure A.3.2 shows a sample page.46“Report of the Committee of Council on Education (England and Wales); with appendix 1888-89.” UKparliamentary paper, 1889. Vol. 29, paper C.5804. Appendix Figure A.3.3 shows a sample page.47Southall & Ell (2004) Great Britain Historical Database : Census Data : Religion Statistics, 1851. [datacollection]. UK Data Service. SN: 4562, http://doi.org/10.5255/UKDA-SN-4562-1.48“Great Britain Historical GIS Project” (2011), University of Portsmouth.18This includes information on age, occupation, gender, family, and place of birth. The censusdata was made available by the Integrated Census Microdata (ICeM) project, part of theUK Data Archive at the University of Essex.49,50 In Sections 1.5 and 1.6, my sample is theuniverse of males ages 16-50 in each census, while for reasons described in Section 1.7 Inarrow my focus to those ages 25-45 for the census linked analysis. Females are not includedin the analysis because the practise of changing surname at marriage severely limits theability to link women across censuses. Additionally, the occupation reported for women atthe time was suspect, with many reporting their husband’s occupation as their own.51I wish to identify which parish an individual spent their childhood in, so as to observewhether or not they were treated. However, for Sections 1.5 and 1.6, when I am using thecomplete, unlinked censuses, I only observe with certainty current parish of residence andcounty of birth. Those no longer residing in their birth county are obviously less likely tohave grown up in their current parish of residence, hence they are dropped. In Section 1.7,however, I keep these movers, as using the linked sample I directly observe childhood parishof residence. While the linked sample is mainly used to address questions of social mobility,in Appendix A.1 I use it to demonstrate that excluding movers in the previous sectionsdid not bias results, and that it was indeed childhood place of residence that matters fortreatment.Income was not recorded in the censuses of the period. Occupation, however, was, andI use it as a proxy for social status and return to human capital. The censuses reportover 7 million unique occupation strings. Following each census, officials in the GeneralRegister Offices categorized each string into one of nearly 800 occupation groups that werebroadly consistent across the censuses used. Using job adverts published in 19th centuryEnglish periodicals, as well as other contemporaneous descriptions of occupations, Mitch49Schurer & Higgs (2014), Integrated Census Microdata (I-CeM), 1851-1911. [data collection]. UK DataService. SN: 7481, http://doi.org/10.5255/UKDA-SN-7481-1.50Schurer (2019), Integrated Census Microdata (I-CeM) Names and Addresses, 1851-1911: Special LicenceAccess. [data collection]. UK Data Service. SN: 7856, http://doi.org/10.5255/UKDA-SN-7856-1. Note thataccess to this data set is restricted, and thus I am unable to share it publicly.51Higgs (1996), pg. 98.19(1992) estimates each occupation group’s use of literacy, specifying four categories of jobs:“literacy required”; “literacy likely to be useful”; “possible (or ambiguous) use of literacy”;and “unlikely to use literacy”. It is this categorization of occupations that I use as thedependent variable for most of the analysis, although to ease interpretation I group the firsttwo and the last two together to create a binary variable. In Table 1.3 I show the 12 mostcommon jobs by literacy requirement.To be clear, I do not rely on this categorization to determine how public education affectedthe spread of literacy. By many measures literacy was already widespread at the time of theAct; by 1870 around 80% of men were able to write their own name.52 Instead, occupationsthat required literacy should be viewed as a proxy for those in which the returns to humancapital were high. While basic levels of literacy were common, there was still large variationin the degree of literacy. For instance, at the time many could read but were unable towrite anything beyond their name.53 Jobs that required literacy were typically those whereproductivity increased with literacy ability. While literacy alone may have sufficed, thosewith greater mastery of it were more sought after.54 Further, reading and writing were oftengrouped together with the third of the three “R’s”: arithmetic. As Mitch points out, highlevels of literacy at the time was seen as a signal of general intelligence.55Thus, the literate occupation variable used throughout this paper should be viewed asa proxy for occupations where the returns to general human capital were high. Such oc-cupations were also typically better compensated, and held in higher esteem.56 However,to more precisely proxy for positive outcomes, I also verify the results using HISCLASS, abreak down of 19th occupations by social class which I describe in detail in Section (1978)53Mitch (1992), pg. xvii54Ibid, pg. 1755Ibid, pg. 1356Ibid, pg. 22-36201.5 Regression Kink IdentificationOne of the goals of the 1870 Education Act was to “fill in the gaps”: to target parisheswith insufficient school supply. As previously described, each parish was expected to provideenough school space to educate 1/6 of its entire population, with each pupil expected torequire ten square feet of school space. Thus, parishes with less than 0.167 school spots –equivalently 1.67 square feet of school space – per capita, were deemed to have insufficientschool supply, and were to be compelled to form school boards to address the shortfall.However, they were given a grace period to address the shortfall privately if they so wished.If this was accomplished, board formation was not compelled.The outcome of this assignment rule can be seen in Figure 1.4. The larger the pre-reform supply shortfall, the more likely a parish was to receive a school board. This waslikely because larger shortfalls were more costly to fill privately, making expansion of privatesupply less attractive relative to board formation. Crucially, though, past the cutoff of 0.167school spots per capita, pre-reform school supply had little bearing on whether or not aparish received a school board. These sufficiently-supplied parishes were still allowed toform school boards voluntarily, but did so rarely. The result is a kink in the relationshipbetween treatment probability and pre-reform school supply at the cutoff.If school boards improved human capital among the treated, then the kink in treatmentprobability at the cutoff should induce a second stage kink in human capital at the cutoffas well. As discussed above, the use of literacy in an occupation serves as a good proxy forthe return to human capital in said occupation. Therefore, I use the 1901 proportion of jobswithin a parish among 19-30 year olds that make use of literacy as a proxy for human capitalaccumulation. The 19-30 age range is the largest range that ensures all individuals includedfrom treated parishes received at least four out of a possible eight years of treatment, whilein the comparative age range in 1881 no individual received four years or more.57 Figure 1.5demonstrates that there is indeed a “kink” in this variable present at the cutoff. I exploit57See Table 1.421these first and second stage kinks to identify the effect of public school introduction.Identification using a Regression Kink (RK) design rests on four assumptions, describedformally in Appendix A.4. The first is simply that a kink in treatment probability exists.Of course, the existence of such a kink at the cutoff of 0.167 pre-reform school spots percapita is strongly supported both by the institutional setting and by the data displayed inFigure 1.4.58 A second assumption rules out other kinks in treatment probability near thecutoff, and also rules out a jump in treatment probability at the cutoff. Again, Figure 1.4supports this.The final assumptions ensure no kink exists in the dependent variable near the cutoffgiven treatment status. Let Y represent the proportion of jobs within a parish that makeuse of literacy, and Y1 and Y0 its potential values given treatment or not, respectively. Thethird assumption asserts that the relationship between Y0 or Y1 and pre-treatment schoolsupply itself is not kinked at the cutoff, while the fourth assumption is that there is no kinkin the distribution of unobservables at the cutoff. This means the kink in Y must be inducedby the kink in treatment probability. These final assumptions may be viewed as analogousto an exclusion restriction, as they imply that the instrument (the kink) is only correlatedwith Y through its association with the endogenous variable (treatment status).The threats to these assumptions are a kink in the relationship between Y0 or Y1 and pre-treatment school supply itself at the cutoff, or a kink in the distribution of unobservablesat the cutoff which in turn induces a kink in Y0 or Y1. The first concern seems unlikely:school space and human capital accumulation are likely related, but there is no reason toexpect a kink, let alone one specifically at 1.667 square feet per capita. The same applies forunobservables - with the exception of sorting (which I address below), there is no economicor historical reason why there should be a kink in Y at the cutoff except because of the kinkin treatment probability. Nevertheless, I test this assumption by examining two similar,but untreated, samples. As pointed out by Landais (2015), if Y is kinked at the cutoff for58Note that while the setting suggests the treatment kink is induced by a kink in the cost of supplying aschool shortfall at the cutoff, identification does not depend on this being the cause.22a reason other than the kink in treatment probability, such a kink should also appear insamples without a kink in treatment probability, assuming they are similar enough in allother ways. If the kink in Y only appears in the sample experiencing the first stage kink,this suggests assumptions 3 and 4 hold. In Figure 1.6 I examine the relationship between Yand pre-treatment school supply among the same age group (19-30 year olds) as Figure 1.5but from twenty years prior (1881 as opposed to 1901); in Figure 1.7 I do the same for thosefrom the same year as Figure 1.5 but older (35-50). These men were too old to be treated bythe reform, thus a kink at the cutoff in either sample would suggest an assumption violation.However, neither graph suggests a kink. While this result does not rule out a violation ofassumptions, it does imply that such a violation likely did not exist in 1881, nor in 1901among older cohorts.One possible cause of a violation is a kink in the distribution of unobservables, perhapscaused by sorting at the cutoff. In Figure 1.8, I bin the parishes according to pre-treatmentschool supply R and plot the number of parishes in each bin. The density of R, fR(r),appears smooth around the cutoff r0 = 0.167, suggesting sorting is not an issue. Nonetheless,in Appendix A.5 I formally assess this smoothness using two tests. The first, the McCrarytest, fails to reject its null that fR(r) is continuous at r0. In a normal RD, this would besufficient, as continuity of the distribution of unobservables is all that is assumed. However,in RK, differentiability is also required. Thus, I conduct a second test, suggested by Card etal. (2012), the null of which is that fR(r) is differentiable at r0. This test also fails to rejectits null, providing further evidence against sorting.Thus, all evidence suggests that the four RK assumptions hold. This enables identifi-cation of a local average treatment effect of public schools. Let G(r) = E[Y |R = r], andtreatment T = 1{P (R)−U≥0}, where U is normalized such that U ∼ Unif(0, 1), so P (R) is theprobability of treatment given pre-treatment school supply. The treatment effect is equal to23the size of the second stage kink, divided by the size of the first stage kink:59G′+ −G′−P ′+ − P ′−= E[Y1 − Y0|U = P (r0), R = r0] = τ (1.1)See Appendix A.4 for proof.It is important to make clear what this measures: the average treatment effect at r0among those of type U = P (r0). These are the compliers: the parishes that would not betreated to the right of the kink but would be treated to the left. Thus, τ identifies the effectof public schools on the marginal parish, the one just on the edge of being treated or not.1.5.1 Regression Kink Estimation and ResultsTo identify G′+, G′−, P′+, and P′−, local linear regression is used. On either side of thecutoff, observations within a distance of h are used to estimate parameters for the followingequations using OLS:T = α0 + α1R + α2[1[R≥r0] ∗ (R− r0)] +  (1.2)Y = γ0 + γ1R + γ2[1[R≥r0] ∗ (R− r0)] + v (1.3)Then the treatment effect described above can be estimated asτˆ =Gˆ′+ − Gˆ′−Pˆ ′+ − Pˆ ′−=γˆ2αˆ2(1.4)Note that Equation 1.3 is simply the reduced form of the following:Y = β0 + β1R + τ˜T + µ (1.5)59F ′+ = limr↓r0∂F (r)∂r and F′− = limr↑r0∂F (r)∂r .24The treatment effect τ˜ is estimated using 2SLS on an optimal bandwidth h = 0.0796609.60,61Table 1.5 shows the results. The first stage is very strong, as was suggested by Figure 1.4.The second stage estimate suggests that parishes near the kink treated with a school boardexperience a nearly 13 pp increase in the proportion of jobs requiring literacy in the treatedage range. To put this effect in perspective, in 1901 around 45% of the total population wereemployed in jobs requiring literacy.These estimates are not sensitive to bandwidth selection. Figure 1.9 plots the secondstage estimates and confidence intervals for alternative bandwidths.62 While the confidenceinterval grows as the bandwidth (and thus sample size) decreases, the size of the coefficientis quite constant. This also suggests that asymptotic bias, which should decrease as thebandwidth shrinks, is small.As a final robustness test, a “donut” regression kink is examined. First proposed inBarreca et al. (2011), this test addresses concerns that observations at or very near thecutoff may violate one of the identifying assumptions. For instance, while the smoothnessof Figure 1.8 around the cutoff argues against any endogenous sorting, if it did occur itwould likely be among those closest to the kink. To ensure that the result is not beingdriven by some strange subsample very near the kink, only observations laying within anouter bandwidth but outside of an inner bandwidth are used in the estimation, with theinner bandwidth creating a “donut hole” of unused observations around the kink. In Figure1.10 I show the results of a series of such estimations, keeping the outer bandwidth constantat 0.0796609 but varying the size of the inner bandwidth.63 By construction, the estimatedtreatment effect and confidence interval are identical to the original estimation at the optimalouter bandwidth when the inner bandwidth is 0. As expected, the confidence interval grows60Given the system of equations 1.2 and 1.5 is exactly identified, using 2SLS to estimate τ˜ yields anestimate identical to τˆ . The instrument is α2, measuring the first stage kink. Lemma A.2 of Calonico etal. (2014) demonstrates that, under certain regularity conditions and when h → 0 as N → ∞, (τˆ − τ) isasymptotically normal, justifying the use of standard 2SLS errors.61The optimal bandwidth was selected using the method of Calonico et al. (2014)62I tested all bandwidths h = 0.0796609 + c ∗ (0.006), where c ∈ {−5,−4, ..., 4, 5}63I tested all inner bandwidths h = 0 + c ∗ (0.005), where c ∈ {0, 1, 2, 3, 4, 5, 6, 7}25with the size of the inner bandwidth (as sample size shrinks), but the size of the estimatedeffect is quite stable, ranging from 0.095 to 0.212.In sum, public schools increased the proportion of people holding jobs requiring literacyby nearly 13 pp among treated ages in parishes near the cutoff. This result is robust to awide range of bandwidths, as well as to a “donut” design, and demonstrates that attendingpublic schools increased human capital and improved adult outcomes.1.6 Triple DifferenceWhile using a regression kink design offers the benefit of allowing for considerable endogene-ity, it is also restrictive, only identifying the treatment effect on compliers near the kink.This is not an issue when treatment effects are relatively stable across the population, butthis is difficult to assess when viewing an RK in isolation.The nature of the reform allows for another identification technique: a difference-in-difference-in-differences, or Triple Difference (DDD). Using this method, I estimate an aver-age treatment effect on the treated (ATT) across the entire sample (Section 1.6.2), which Ithen compare with the RK LATE (Section 1.6.2). This method also provides more flexibility,allowing me to test the effects of partial treatment, as described below. Finally, by mak-ing use of all the data, it provides much tighter estimates, which are necessary to identifyintergenerational mobility effects in Section Model and TheoryThe three dimensions used in the DDD framework are time, place, and age. The timedimension compares 1881, when the reform was in its infancy and few had been affectedby it, with 1901. Assume that no one was treated in 1881 (this assumption will be relaxedshortly). The place dimension compares parishes that received school boards with those thatdid not. The age dimension compares those of the correct age to have been schooled within26parishes with school boards with those not. For now, assume that the treated age rangedoes not vary by parish (this will also be relaxed shortly). At its most basic, the model canbe written as:Yitpa = δ+γ1t+γ2Sp+γ3Aa+γ4(Sp∗t)+γ5(Sp∗Aa)+γ6(t∗Aa)+γ7(Sp∗Aa∗t)+uitpa (1.6)where t is a year dummy (1 if 1901, 0 if 1881), Sp is a school board dummy (1 if parish preceived a school board, 0 otherwise), and Aa is an age dummy (1 if a is a treated age, 0otherwise). For the moment I will remain agnostic concerning what the dependent variableY represents. Some simple arithmetic reveals that γ7 is equal to the following:γ7 = [(Y¯1BS − Y¯2BS)− (Y¯1NS − Y¯2NS)]− [(Y¯1BU − Y¯2BU)− (Y¯1NU − Y¯2NU)] (1.7)where B represents parishes with boards and N represents parishes without, 1 represents1881 and 2 represents 1901, S represents those of the correct age to be schooled withinboards and U those not. Thus the treatment effect, γ7, represents the difference betweentwo DIDs, one on those of the correct age to be treated and another on those not.The ATT over the entire population is identified by γ7 if two assumptions hold. Both aremodified versions of the traditional DID assumptions: parallel trends, and no spillovers. Theparallel trends assumption in a DDD is much more relaxed than the one found in a DID, as itallows for a difference in trends between treated and untreated parishes in the absence of thereform, as long as the difference in trends was common across the two age groups. To be clear,this does not imply the two age groups needed common trends in the absence of the reform.Put another way, to violate the assumption, not only must treated and untreated parisheshave experienced different growth rates in the absence of the reform, but this difference ingrowth rates between treated and untreated parishes would itself also have to differ by agegroup. Even without this added flexibility, differences in parish level trends can partially beaccounted for by adding a vector Zp of pre-treatment parish controls (population, measures27of religiosity, distance from London, school supply per capital), interacted with time.The second assumption is that there are no spillover effects into untreated parishes orages. Spillovers across parishes would be a concern in large cities, where multiple parishesexist within the same labour market. However, as described in Section 1.4, parishes insidemunicipal boroughs - which most large cities were - are excluded. For most remainingparishes it is reasonable to view each as separate labour markets. That being said, with thelinked sample in Section 1.7 I observe both childhood and adult residence, and use this tomore closely examine the effect of inter-parish migration. As for spillovers across ages, thisis unlikely if one assumes the old and young are separate labour markets. For the sake ofrobustness, in Appendix A.6 I use a simple DID to test for spillover effects among the oldand find no evidence of any.Two issues stand in the way of implementing the model described in Equation 1.6. First,due to the reform’s staggered roll out (see Figure 1.1), treated ages vary by parish. In 1901 a35-year-old residing in a parish that formed a board in 1870 would have been 4 at that time,enabling them to spend a full 8 years in a board school from age 5-12. However, someonefrom the same birth cohort but residing in a parish that formed a board in 1879 would havebeen too old to receive any treatment. And while the correct age range can be inferred forparishes that ended up receiving the reform, it is unclear what age range they should becompared against in parishes that never did.I address this difficulty by adding more flexibility to the model, replacing the single schoolboard dummy with a set of fixed effects, one for each possible reform arrival year (from 1870to 1879, inclusive) as well as one for untreated parishes. Additionally, instead of a singleage dummy, fixed effects for each year of age are included. As before, these place and agedummies are interacted with each other and with the time dummy. The result is as follows:Yitpa = µra + λrt + αat + γ7(Aart) + (Zp)Ψ + (Zp ∗ t)Ω + uitpa (1.8)28where r represents the arrival year group parish p belongs to, µra are the age-arrival yearfixed effects, λrt are the arrival year trend effects, αat are the age trend effects, and Aart is adummy equal to 1 if the individual is from the 1901 census of the age to be treated in parishof type r. The old model is nested in this new model, as the new model simply divides theage and board dummies into finer categories.64A second issue is treatment intensity: some receive the full 8 years of instruction in aboard school, while children already of school age when the board arrives are only partiallytreated. To further complicate matters, in the base year of 1881 some individuals had alreadybeen partially treated. For instance, in 1881 a 16-year-old residing in a parish that formed aschool board in 1870 would have been 5 at the time. If we allow a year for the board to builda school, they had the opportunity to attend a board school from ages 6-12, or 7 years. In1901, a 16-year-old residing in the same parish had the opportunity to attend a board schoolfor all 8 primary years, 5-12. Thus, the latter cohort received only one additional year oftreatment. To address this, I use the difference in years of possible board school attendanceTYtra as the treatment variable in place of the treatment dummy Aapt. Assuming that boardsalways took one year after formation to institute board schools, I calculate the number ofyears each year-parish-age cohort could have attended board schools, and subtract from thatthe number of years the equivalent parish-age cohort in 1881 could have attended. In thisway, the treatment variable is always 0 if the year is 1881, and is the difference between 1881treatment and 1901 treatment by parish-age group if the year is 1901. Table 1.4 shows howthe value of this treatment variable in 1901 varied by age and year of school board formation.The final model is:Yitpa = µra + λrt + αat + γ7(TYtra) + (Zp)Ψ + (Zp ∗ t)Ω + uitpa (1.9)64Goodman-Bacon (2019) describes how to interpret a similar model - where multiple groups receivetreatment at different times, necessitating the inclusion of fixed effects - in a DD setting. The estimatedtreatment effect can be viewed as a weighted average of all possible estimators that compare one treatmentyear group with another.29Additional flexibility can be added by including parish fixed effects ηp in the place of thevector of constant parish controls:Yitpa = µra + λrt + αat + γ7(TYtra) + ηp + (Zp ∗ t)Ω + uitpa (1.10)1.6.2 Triple Difference ResultsTable 1.6 presents the main results of the full sample triple difference. I again use theprobability of obtaining an occupation that requires literacy as my main dependent variable.Unlike the RK, however, the unit of observation is the individual instead of the parish,enabling me to control for age and partial treatment. The results suggest that each additionalyear of access to public school increased the probability of obtaining a literate occupation byaround 0.13 pp. Given that primary schooling lasted 8 years (from ages 5 to 12 inclusive),this implies that full treatment improved chances by around 1 pp. The exclusion of parishfixed effects has very little effect on the size of the estimated treatment effect, although itdoes result in a large increase in standard errors. I also include a number of parish levelcontrols interacted with time to ensure parish level differences in growth rates are not drivingresults; the estimated treatment effect coefficient is relatively unaffected by their inclusion.65RobustnessA placebo test of the identifying assumption - that the difference in trends between those intreated vs untreated parishes would not have varied systematically across ages in the absenceof the reform - can be conducted using 1861 census data. Suppose we mistakenly thought theEducation Act was passed 20 years earlier, in 1850, and that all parishes that received boardsformed them 20 years prior to their actual formation date. If the identifying assumption istrue, we should not see any significant results when running the same regressions as in Table65Controls included (all interacted with a 1901 dummy): 1871 parish population; 1871 parish populationsquared; distance from London; distance from London squared; 1871 school supply per capita; 1851 Churchof England attendees per capita 1851 Catholic attendees per capita; 1851 other religious service attendeesper capita.301.6 but using 1881 data in the place of 1901 data and 1861 data in the place of 1881 data.Table 1.7 shows the results of these regressions. As expected, all estimates are insignificant.Indeed, the estimated treatment effect is very close to zero when parish fixed effects areincluded.Note that using TYtra relies on the assumption that each additional year residing in aparish with a board school between the ages of 5-12 had on average the same effect. In truth,there is reason to doubt this. For one, at the older end of the 5-12 age range attendancewas less frequent due to labour market opportunities, and thus having a board school couldhave made less of a difference at these ages. Further, even if attendance were steady acrossages, it is plausible that education showed either diminishing or increasing returns. To testif this assumption biases my results, I replace years of treatment TYtra with a full treatmentdummy by dropping all those partially treated, for whom TYtra /∈ {0, 8}.66. This allows meto use the specification described in Equation 1.8, the results of which are reported in Table1.8. Note that the treatment coefficient now represents the effect of a full 8 years of publicschooling. As before, full treatment improves the chance of obtaining a literate occupationby around 1 pp.To ensure outlying parishes are not driving the results, I drop individuals residing in thetop and bottom ventile in terms of 1871 school supply per capita and rerun the regressionsof Table 1.7. I then do the same for 1871 population. The results are shown in Table 1.9and demonstrate that dropping the tails has little impact on the estimated treatment effect.Comparison with RK resultsWhile the baseline DDD treatment effects may seem small, bear in mind that only 45% ofthe population held literate occupations. Further, this effect is a population average, butthe reform was directed at the lower classes. As I will show using linked census data below,the effect was much larger among the poor. Nonetheless, the ATT measured by the triple66This drops all individuals whose parish-age groups were only partially treated in either 1881 or 1901,meaning they had access to public schools for some of the years from 5 to 12 but not all of them31difference is much smaller than the LATE given by the regression kink.Of course, there is no reason why these two estimates should be equal. They estimatedifferent things: the RK LATE, the effect of public schools in parishes at the kink just onthe edge of receiving treatment; the DDD ATT, the average effect of public schools acrossall treated individuals. Yet the sources of their difference can help us better understand howthe effect of public schools varied across the population.In Appendix A.6, I rule several possible sources of the difference: that treatment effectsare on average larger near the kink; that it is the result of using different levels of observation(parish vs individual); that the DDD result is biased due to spillovers across ages.Perhaps the most likely explanation for the difference is that the effects of public schoolswere on average larger in the parishes on the margin of receiving them. Remember that theRK estimates the effect on compliers near the kink - the parishes that would not have beentreated were they to the right of the kink, but would have been treated were they on theleft. This excludes the parishes near the kink that would have received treatment whetherthey were on the left or the right. Were the treatment effect on the compliers larger thanthat on the always takers, the RK estimate would be larger than the DDD estimate, evenover the same sample.This scenario implies that the parishes with the most to gain from public schools werealso the most reluctant to receive them. This is more plausible than it may seem, giventhat the local elites who influenced the treatment decision were unlikely to benefit from itgiven that the reform was aimed at the children of the lower classes. Unfortunately, sinceone cannot differentiate between compliers and always takers in the data, this theory isimpossible to test.It is also possible that the DDD is underestimating the effect due to a violation inits parallel trends assumption. If, in the absence of the reform, the young would haveshown more gains in literate occupations relative to the old in untreated parishes than intreated ones, the DDD would be biased downward. To test this, I rerun the regressions of32Table 1.8 but using only those parishes that received boards.67 The results are shown inTable 1.10. The treatment effect (0.225-0.278 pp per additional year of public schooling,or 1.8-2.224 pp from the full 8 years) is larger then the baseline estimates (0.126-0.136 ppper additional year), but the differences between the two estimation strategies are neversignificant. The results nonetheless suggest that, if anything, the baseline DDD results arean underestimation.Class ResultsI have thus far examined the effect public schooling had on the probability of obtaining aliterate job, a good proxy for occupations with a high return to human capital. Literate jobswere also typically better compensated, and viewed in higher esteem.68To make the link between public schooling and positive adult outcomes even clearer, I testthe impact public schooling had on the probability of obtaining a job viewed as high class. Iuse HISCLASS, a ranking of occupations by social class developed by Maas & Van Leeuwen(2016) using 19th century occupation data from Canada and Western Europe.69 It dividesoccupations into seven ordered social classes, shown in Table 1.11. For comparability with myliterate occupation variable, I create a binary class variable by grouping classes 1-3 and classes4-7. The resulting class dummy is equal to 1 for high class occupations and 0 otherwise.Just over 45% of the male population in 1901 was employed in a high class occupation,very similar to the proportion employed in literate occupations. The Pearson correlationcoefficient between my occupation class and literacy dummies is 0.5772, suggesting thatwhile closely related, the two variables are indeed measuring different things.I run the baseline DDD regressions using the class dummy as the dependent variable.67This is possible due to the staggered roll out of the reform over the course of a decade, which createdvariation in the treated age range across treated parishes, allowing me to separate age-trend effects from thetreatment effect.68See Mitch (1992), pg. 22-3669Note that HISCLASS and Mitch’s literacy ranking are derived from two separate occupation classifica-tions (HISCO (Van Leeuwen et al., 2002) and Armstrong (1972), respectively), and thus any correlation isnot the result of shared sources.33The results, shown in Table 1.12, suggest that an additional year of access to public schoolingincreased the odds of obtaining a high class occupation by 0.15-0.3 pp, and thus exposureto public schooling for the full 8 years of primary school increased the odds by 1.2-2.4 pp.Note that, when parish fixed effects are included, the treatment effects are very similar insize to literate occupation results.Thus, it is clear that the introduction of public school education improved access to jobsthat were not only more human capital intensive, but also higher class.1.7 Census Linkage and Mobility EstimationIn modern minds, Victorian England and Wales may conjure images of extreme class rigidity.Reading Hardy or Dickens, one is led to believe that ambition among the lower classes wasconstantly thwarted (Jude the Obscure, 1895), and that social mobility was only possiblevia large inheritances (Great Expectations, 1861). But as Long (2013) and Long & Ferrie(2013) have shown, there was a surprising amount of mobility during the period. Further,Long (2013) shows that social mobility increased significantly between his two comparisonperiods (1851-1881 and 1881-1901). Was this increase in mobility driven by the introductionof public schooling in 1870?The analysis thus far has estimated the average effect of public school introduction byage-parish-year groups. But there is good reason to believe heterogeneous treatment effectsexisted within such groups across social classes. The lower, middle, and upper classes alllargely attended different schools. The 1870 Education Act was aimed at improving edu-cation among the working classes, estimated to represent about 85% of the population.70Even within that 85% there was considerable variation, as this included everyone from farmday labourers to skilled tradesmen. If, in the absence of public schools, those near the topof the distribution were better able to endow their children with human capital than those70“Report of the Committee of Council on Education (England and Wales); 1870-71,” UK parliamentarypaper, 1871, Vol. 22, paper C.406.34at the bottom, then the arrival of public schools may have served to level the playing field,improving social mobility. To test this I need to observe both adult outcomes and childhoodclass, something that can only be done by linking individuals across censuses.1.7.1 Linkage DescriptionI link young people (ages 5-25) in the full 1881 census to their adult selves (ages 25-45) in thefull 1901 census, and find 2,357,948 unique matches. For a pre-treatment comparison group, Ialso link those aged 5-25 in the full 1861 census to their 1881 selves and find 1,522,047 uniquematches. To construct these links, I use a modified version of the Abramitzky, Boustan, andEriksson (2012, 2014, 2019a) method, described in detail in Appendix A.7, using first andlast name, birth year, and birth place (county and parish). Summary statistics of the linkagesare provided in Tables 1.13 and 1.14.I only link ages 25-45 – as opposed to recreating the 16-50 age range used in Sections 1.5and 1.6 – for several reasons. Individuals aged 16-19 in the later census were not born 20years prior, and thus do not appear in the earlier census. Since I am interested in where anindividual attended primary school, which began at age 5, beginning the early census agerange at 5 was appropriate. Finally, father’s class is only observed when he lived in the samehousehold in the earlier census, and thus would only be observable for 50 year olds if theyresided with their father when they were 30. For this reason I limit the top age to 45.As far as I am aware, full-count versions of the English and Welsh censuses have neverbeen previously linked in the literature.71 Even outside of the UK, linkages using historicalfull-count censuses are relatively rare. Table 1.15 compares notable linkages in the historicalliterature with those constructed here. As can be seen, my match rates are very good. Whilematch rates of 15-30% are common in the literature, here 37.1% of men age 0-25 in 1861 arematched to 1881, while 42.2% of men age 0-25 in 1881 are matched to 1901. The reason forthe high match rate is that, unlike historical US censuses where birthplace was only listed at71Long (2005), which used a 2% sample of the 1851 census and the full 1881 census to link 28,000 men,might come closest.35the state level, the censuses of England and Wales included birth parish. Matching on thismuch finer level of geography greatly increases the probability that a match will be unique.72To test the frequency of false positives, I make use of middle initials. Given that middleinitial was not used in the matching process (as they are only available for a subset ofindividuals), a middle initial shared by both sides of a match is a strong indicator thatthe match is correct. In Appendix A.8 I describe the test in detail. The results suggestthat after factoring in the probability of two individuals incorrectly matched sharing thesame middle initial, as well as adjusting for likely transcription errors, the PPVs (PositivePredictiction Value, as the ratio of true matches to total matches is known in the machinelearning literature) of the 1861-1881 and 1881-1901 linkages are approximately 87.2% and93.5%, respectively. The literature suggests that these are very good: Bailey et al. (2019)state that common match procedures lead to PPVs between 66% and 90%, while Abramitzkyet al. (2019b) are slightly more optimistic, arguing that modern procedures lead to PPVsbetween 70% and 95%.73The high PPVs found here (or equivalently, low rates of false positives) are likely drivenby the use of full-count censuses. As pointed out in Bailey et al. (2019), a match thatappears unique when linking a subsample may not be when linking the full population.Such a match, which has a high probability of being a false positive, would be included inthe subsample linkage but excluded when linking full-count samples, leading to lower falsepositive rates in full-count linkages.Both the 1861-1881 and 1881-1901 baseline linked samples are representative of the totalpopulation, judging by the first two columns of Table 1.14. As noted previously, school72Long (2005) and Long & Ferrie (2013) also match English and Welsh census data using birth parish,while not achieving as high a match rate. This is likely because (a) they link across a longer period (30 vs20 years), over which more individuals would have died or emigrated, and (b) they did not have access tothe standardized birth parish variable recently constructed by I-CeM researchers, which addresses the issueof parishes with multiple and changing names.73I also construct two other, more conservative linkages of the 1861-1881 and 1881-1901 censuses, describedin detail in Appendix A.9. These reduce the linkage rate, but lead to even fewer false positives. If falsepositives significantly affect analysis, one would expect results obtained using the more conservative linkagesto be closer to the truth than those obtained using the baseline method. Table A.9.1 demonstrates that, ifanything, the mobility effects described below actually get larger when using the more conservative methods.36data, indicating whether or not a parish received a school board, was only available forparishes laying outside of municipal boroughs. Columns 2 and 3 of Table 1.13 comparethe subset of the population matched to school data with the corresponding linked sample.Linked individuals tend to be slightly younger, and from slightly smaller parishes. Thisis unsurprising, as younger men are less likely to die between censuses, and smaller birthparishes make unique matches more likely. Finally, column 4 of Tables 1.13 and 1.14 showssummary statistics of the subset of linked individuals who resided with their father in theearlier census, enabling measurement of childhood class (using father’s occupation).74 Theseindividuals are about a year and a half younger than the general population, as one wouldexpect given younger children are more likely to reside with their fathers. Concerning class,however, these individuals seem representative of the overall population.1.7.2 Mobility Regressions and ResultsI next test the effect of the introduction of public schools on intergenerational mobility, usingthe triple difference framework described in Section 1.6. As before, I estimate the effect anadditional year of access to public schools had on the probability of obtaining a literateoccupation in adulthood.75 However, using the linked sample, I now observe the occupationan individual’s father held 20 years prior, which I use as a proxy for the individual’s childhoodsocial class (using the class dummy described in Section 1.6.2). By interacting childhoodsocial class with the triple difference, I can compare the effects of public schools on high andlow class children. The resulting triple difference equation is as follows:74Note that individual’s are only linked to their fathers in the census if they reside in the same house-hold. This provides an extra impetus for linking to childhood, as co-residence with one’s father was rare inadulthood.75In Appendix A.10 I estimate effects using other measures of occupation quality, including OCCSCORE- a commonly used measure based on the median income of occupation practitioners in the US in 1950 - anda ranking of occupations based on the likelihood of practitioners’ children obtaining prestigious occupations.The results described below hold in each case.37Yitpac = µrac + λrtc + αatc + γ(TYtra) + ζ(TYtra ∗ FCi)+ηpc + (Zp ∗ t)Ω + (Zp ∗ t ∗ FCi)Π + uitpac(1.11)Observe that, in addition to the treatment years variable TYtra, all lower level termshave been interacted with father’s class (FCi) as well, so as to avoid biasing the interactionof interest. In the place of Equation 1.10’s age-arrival year and parish fixed effects (µraand ηp), and arrival year and age trend effects (λrt and αat), Equation 1.11 has age-arrivalyear-class and parish-class fixed effects (µrac and ηpc), and arrival year-class and age-classtrend effects (λrtc and αatc). Parish trend controls have also been interacted with FCi. Theeffect on lower class children of an additional treatment year is estimated by γ, while ζ isthe difference between this effect and that on higher class children.Baseline Mobility ResultsThe first two columns of Table 1.16 report the results of regression on Equation 1.11 withand without parish trend controls. Children of fathers with lower class occupations saw theirprobability of obtaining a literate job in adulthood increase by approximately 0.2 pp witheach additional year of access to public school. Thus, those treated for a full eight years sawtheir chance at a literate job increase by around 1.6 pp. In contrast, children of fathers withhigher class occupations saw zero or perhaps even slightly negative effects from treatment.Again, this fits with the 1870 Education Act’s stated purpose of improving the education ofworking class children, and with the historical reality that upper and middle class childrenlargely attended separate private schools unaffected by the reform.The gains made by lower class children allowed them to partially close the gap betweenthem and high class children. Consider that among untreated children in 1901, those withhigh class fathers were 20.0 pp more likely than their low class counterparts to obtain literateoccupations in adulthood.76 Each additional year of access to public schools decreased this76Controlling of age and parish of birth. For derivation, see Appendix A.1138gap by 0.29-0.31 pp. Thus, having access to public schools from age 5 to 12 reduced theoutcome gap by over 10%, to 17.5-17.7 pp.Comparison of BrothersThe linked sample enables another method of identification: comparing the outcomes ofbrothers. Many brothers residing in the same household experienced differing levels of treat-ment based on age. By including brother fixed effects, one can therefore control for geneticand household effects while still identifying the treatment effect. Of course, age must stillbe controlled for along with its interactions, but all parish, time, and class fixed effects andcontrols are subsumed by the brother fixed effects. The resulting equation is shown below,with κb representing the brother fixed effect:Yitpacb = µrac + αatc + κb + γ(TYtra) + ζ(TYtra ∗ FCb) + uitpacb (1.12)Brothers are only identified in the census if they resided in the same household, whichtypically only occurred in childhood. Thus, this method is only possible using the linkedsample, in which childhood household is observable. The results are shown in the thirdcolumn of Table 1.16. While the significance of the interaction term disappears - likelydue to the much smaller sample size - the effect sizes are even larger than those previouslyestimated, implying that full treatment would have reduced the occupational outcome gapbetween high and low class children by over 15%.Using Finer Categories of ClassI have so far defined class as a binary variable. Of course, in reality Victorian class structurewas more complex than this. To better understand how access to public school differentiallyeffected various parts of the social hierarchy, I make use of the original seven ranked classesof the HISCLASS variable, listed in Table 1.11. I divide my sample into seven groups,each containing all the children of fathers belonging to one of the ranked classes. For each39group I then regress on the probability of obtaining a literate occupation in adulthood usingEquation 1.8. The treatment years coefficients of each regression are reported in Table 1.17.The smaller sample sizes of each regression - the result of dividing into seven differentclasses - lead to larger standard errors. The trend across regressions nonetheless confirmsthat, in general, the impact of public schools increased the further down the social ladderone began.1.8 ConclusionThe creation of England and Wales’ public school system in 1870 provides a unique opportu-nity to observe how instituting a public school system on top of a previously existing privatesystem affected outcomes, and how an education reform specifically aimed at the poor canimprove social mobility across generations. I find that the introduction of public schoolsresulted in a large positive shock to education provision, increasing school supply and atten-dance. More importantly, children lucky enough to have access to public schooling were morelikely to obtain good occupations in adulthood. In the parish just on the margin of receivingtreatment, public schools increased the probability of obtaining a human capital-intensiveoccupation by 13 pp. Each additional year of public school access significantly improved achild’s chance of obtaining a high social status occupation in adulthood. Further, by target-ing children of the lower classes, public schools decreased the gap in occupational attainmentbetween lower- and higher-class children by over 10%.Further work remains to be done to disentangle how public school provision improvededucational outcomes. Whether public schools improved private schools by providing com-petition in the education marketplace, for example, is an open question. As well, while thispaper focused entirely on males due to data restrictions, the effects of public school provisionon females, who were also provided for by the 1870 Education Act, is obviously of interest.This paper moves the literature forward on multiple fronts. In particular, it contributes40to comparisons of public and private schools by demonstrating that a private only systemwill not always be optimal. And perhaps more significantly from a policy standpoint, theresult that public school provision increased social mobility goes against previous findings ofthe opposite, justifying the hope that education policy properly targeted at disadvantagedchildren will increase equality of opportunity.41Tables & FiguresTable 1.1: Summary Statistics: Treated vs Untreated Parishes1871 1881 1901VARIABLES Board No Board Board No Board Board No BoardPopulation of parish 1,604 718.0 1,838 837.2 2,008 930.4School Supply per capita 0.0921 0.131Distance to London 208.81 194.921851 Religious Attendance Per CapitaChurch of England 0.332 0.373Roman Catholic 0.0080 0.0117Other Religious Services 0.378 0.307Percent Occupied Within SectorAgriculture 0.178 0.289 0.136 0.215Secondary 0.520 0.395 0.536 0.442Tertiary 0.229 0.246 0.290 0.303Occupation Requires Literacy 0.311 0.310 0.367 0.363Parishes 2399 10711 2399 10711 2399 1071142Table 1.2: Full 1881 Population vs Population Matched to School Data(1) (2)VARIABLES Full Matched to School DataAge 30.38 30.35Population Density > 4/acres 0.560 0.245Percent Occupied Within SectorAgriculture 0.147 0.252Secondary Sector 0.466 0.437Tertiary Sector 0.315 0.240Literacy Required 0.386 0.311N 6,072,649 3,018,783Table 1.3: Common Jobs by Literacy RequirementLiteracy Required or Likely to be Useful Unlikely to Use LiteracyCommercial or Business Clerks Coal MinerCarpenter General LabourerFarm Owner/Steward Agricultural LabourerGrocer Carman/Carrier/CarterBlacksmith PainterPolice Cotton processorRailway official Bricklayer/MasonCommercial traveler Engine StokerSchoolmaster/teacher GardenerInnkeeper BakerInsurance agent CoachmanPostman Brick / tile / terra-cotta maker43Table 1.4: Years of Treatment Difference by Board Arrival Year and AgeAge in 1901 1870 1871 1872 1873 1874 1875 1876 1877 1878 187916 1 2 3 4 5 6 7 8 8 817 2 3 4 5 6 7 8 8 8 818 3 4 5 6 7 8 8 8 8 819 4 5 6 7 8 8 8 8 8 820 5 6 7 8 8 8 8 8 8 821 6 7 8 8 8 8 8 8 8 822 7 8 8 8 8 8 8 8 8 823 8 8 8 8 8 8 8 8 8 824 8 8 8 8 8 8 8 8 8 825 8 8 8 8 8 8 8 8 8 826 8 8 8 8 8 8 8 8 8 827 8 8 8 8 8 8 8 8 8 728 8 8 8 8 8 8 8 8 7 629 8 8 8 8 8 8 8 7 6 530 8 8 8 8 8 8 7 6 5 431 8 8 8 8 8 7 6 5 4 332 8 8 8 8 7 6 5 4 3 233 8 8 8 7 6 5 4 3 2 134 8 8 7 6 5 4 3 2 1 035 8 7 6 5 4 3 2 1 0 036 7 6 5 4 3 2 1 0 0 037 6 5 4 3 2 1 0 0 0 038 5 4 3 2 1 0 0 0 0 039 4 3 2 1 0 0 0 0 0 040 3 2 1 0 0 0 0 0 0 041 2 1 0 0 0 0 0 0 0 042 1 0 0 0 0 0 0 0 0 043 0 0 0 0 0 0 0 0 0 044 0 0 0 0 0 0 0 0 0 045 0 0 0 0 0 0 0 0 0 046 0 0 0 0 0 0 0 0 0 047 0 0 0 0 0 0 0 0 0 048 0 0 0 0 0 0 0 0 0 049 0 0 0 0 0 0 0 0 0 050 0 0 0 0 0 0 0 0 0 044Table 1.5: RK 2SLS Results at CCT BandwidthFirst Stage: School Board1871 School Supply/Pop -3.23027***(0.20747)D*(1871 School Supply/Pop - 0.1667) 2.86375***(0.42977)Constant 0.62631***(0.02772)Second Stage: Proportion of jobsrequiring literacy, ages 19-30School Board 0.12845**(0.06102)1871 School Supply/Pop 0.14156(0.13380)Constant 0.18102***(0.03026)Parishes 6314Bandwidth 0.07966Instrument F-Stat 44.40D = 1[1871 School Supply/Pop≥0.1667]. Robust standard errors in parentheses. *** p<0.01, ** p<0.05, * p<0.1Table 1.6: Full Sample Triple Difference(1) (2) (3)Literacy Required Literacy Required Literacy RequiredYears of Treatment 0.00136 0.00130*** 0.00126***(0.00108) (0.000439) (0.000446)Observations 3,896,991 3,896,985 3,864,784Controls NO NO YESParish Fixed Effects NO YES YESArrival-Age Fixed Effects YES YES YESAge Trend Effects YES YES YESArrival Trend Effects YES YES YESRobust standard errors in parentheses, clustered at the parish level. Controls (all interacted with a 1901 dummy):1871 parish population; 1871 parish population squared; distance from London; distance from London squared; 1871school supply per capita; 1851 Church of England attendees per capita 1851 Catholic attendees per capita; 1851other religious service attendees per capita. *** p<0.01, ** p<0.05, * p<0.145Table 1.7: 1861 Placebo(1) (2) (3)Literacy Required Literacy Required Literacy RequiredYears of Treatment 0.000788 -0.000045 -0.000037(0.00142) (0.000466) (0.000474)Observations 3,229,655 3,229,650 3,202,470Controls NO NO YESParish Fixed Effects NO YES YESArrival-Age Fixed Effects YES YES YESAge Trend Effects YES YES YESArrival Trend Effects YES YES YESRobust standard errors in parentheses, clustered at the parish level. Controls (all interacted with a 1901 dummy):1871 parish population; 1871 parish population squared; distance from London; distance from London squared; 1871school supply per capita; 1851 Church of England attendees per capita 1851 Catholic attendees per capita; 1851other religious service attendees per capita. *** p<0.01, ** p<0.05, * p<0.1Table 1.8: Effect of Full Treatment, Dropping Partially Treated(1) (2) (3)VARIABLES Literacy Required Literacy Required Literacy RequiredTreatment 0.0124 0.0108*** 0.0104***(0.00782) (0.00369) (0.00374)Observations 3,509,820 3,509,814 3,479,798Controls NO NO YESParish Fixed Effects NO YES YESArrival-Age Fixed Effects YES YES YESAge Trend Effects YES YES YESArrival Trend Effects YES YES YESRobust standard errors in parentheses, clustered at the parish level. Controls (all interacted with a 1901 dummy):1871 parish population; 1871 parish population squared; distance from London; distance from London squared; 1871school supply per capita; 1851 Church of England attendees per capita 1851 Catholic attendees per capita; 1851other religious service attendees per capita. *** p<0.01, ** p<0.05, * p<0.146Table 1.9: Full Sample Triple Difference, Tails DroppedVARIABLES School Tails Dropped Pop Tails DroppedYears of Treatment 0.00110** 0.00109** 0.00128** 0.00105**(0.000458) (0.000465) (0.000538) (0.000537)Observations 3,464,070 3,440,137 2,127,948 2,116,353Controls NO YES NO YESParish Fixed Effects YES YES YES YESArrival-Age Fixed Effects YES YES YES YESAge Trend Effects YES YES YES YESArrival Trend Effects YES YES YES YESRobust standard errors in parentheses, clustered at the parish level. Controls (all interacted with a 1901dummy): 1871 parish population; 1871 parish population squared; distance from London; distance fromLondon squared; 1871 school supply per capita; 1851 Church of England attendees per capita 1851 Catholicattendees per capita; 1851 other religious service attendees per capita. *** p<0.01, ** p<0.05, * p<0.1Table 1.10: Only Treated(1) (2) (3)Literacy Required Literacy Required Literacy RequiredYears of Treatment 0.00278* 0.00225* 0.00240**(0.00163) (0.00118) (0.00119)Observations 928,995 928,979 923,479Controls NO NO YESParish Fixed Effects NO YES YESArrival-Age Fixed Effects YES YES YESAge Trend Effects YES YES YESArrival Trend Effects YES YES YESRobust standard errors in parentheses, clustered at the parish level. Controls (all interacted with a 1901 dummy):1871 parish population; 1871 parish population squared; distance from London; distance from London squared; 1871school supply per capita; 1851 Church of England attendees per capita 1851 Catholic attendees per capita; 1851other religious service attendees per capita. *** p<0.01, ** p<0.05, * p<0.147Table 1.11: HISCLASS CategoriesClass Labels RankHigher managers/professionals 1Lower managers/professionals, clerical and sales positions 2Foremen and skilled workers 3Farmers and fishermen 4Lower skilled workers 5Unskilled workers 6Lower and Unskilled farm labourers 7Table 1.12: Full Sample Triple Difference. Dependent Variable: Class Dummy(1) (2) (3)VARIABLES Class Dummy Class Dummy Class DummyYears of Treatment 0.00296*** 0.00158*** 0.00156***(0.000741) (0.000422) (0.000426)Observations 4,030,970 4,030,964 3,998,038Controls NO NO YESParish Fixed Effects NO YES YESArrival-Age Fixed Effects YES YES YESAge Trend Effects YES YES YESArrival Trend Effects YES YES YESRobust standard errors in parentheses, clustered at the parish level. Controls (all interacted with a1901 dummy): 1871 parish population; 1871 parish population squared; distance from London;distance from London squared; 1871 school supply per capita; 1851 Church of England attendees percapita 1851 Catholic attendees per capita; 1851 other religious service attendees per capita.*** p<0.01, ** p<0.05, * p<0.148Table 1.13: Linkage Summary Statistics: Early Periods1861-1881 Linkage Summary Statistics: 1861(1) (2) (3) (4)Linked &Linked & Resides with FatherMatched to Matched to & Matched toVARIABLES Full School Data School Data School DataLive in treated (in future) parish 0.298 0.284 0.284Age 14.25 13.99 13.61 12.02Population of parish 12,107 4,868 4,282 4,306Resides with Father 0.594 0.612 0.664Father Class Dummy 0.356 0.279 0.284Linked to 1881 0.371 0.409Matched to School Data 0.510Observations 4,102,162 2,093,087 855,591 568,1071881-1901 Linkage Summary Statistics: 1881(1) (2) (3) (4)Linked &Linked & Resides with FatherMatched to Matched to & Matched toVARIABLES Full School Data School Data School DataLive in treated parish 0.334 0.318 0.320Age 14.19 13.99 13.83 12.32Population of parish 21,665 9,789 8,552 8,485Resides with Father 0.643 0.661 0.707Father Class Dummy 0.396 0.312 0.312Linked to 1901 0.422 0.468Matched to School Data 0.521Observations 5,591,747 2,915,615 1,365,184 964,760Note: The top panel describes the summary statistics of males aged 5-25 in the 1861 census. The bottom panel describesmales aged 5-25 in the 1881 census.49Table 1.14: Linkage Summary Statistics: Late Periods1861-1881 Linkage Summary Statistics: 1881(1) (2) (3) (4)Linked &Linked & Resided with FatherMatched to & Matched toVARIABLES Full Linked School Data School DataLinked to 1861 0.382Age 33.54 33.60 33.48 31.89Class Dummy 0.415 0.421 0.366 0.367Resided with Father 0.655 0.664Matched to School Data 0.562Observations 4,043,487 1,522,047 855,591 568,1071881-1901 Linkage Summary Statistics: 1901(1) (2) (3) (4)Linked &Linked & Resided with FatherMatched to & Matched toVARIABLES Full Linked School Data School DataLinked to 1881 0.531Age 34.06 33.87 33.74 32.24Class Dummy 0.436 0.438 0.385 0.383Resided with Father 0.692 0.707Matched to School Data 0.579Observations 4,444,271 2,357,948 1,365,184 964,760Note: The top panel describes the summary statistics of males aged 25-45 in the 1881 census. The bottom paneldescribes males aged 25-45 in the 1901 census.50Table 1.15: Comparison of LinkagesPaper Sources Match Rate Number Linked1861 England & Wales CensusMilner (2019) (Full, Men 5-25) to 1881 England 37.1% 1,522,047& Wales Census (Full, Men 25-45)1881 England & Wales CensusMilner (2019) (Full, Men 5-25) to 1901 England 42.2% 2,357,948& Wales Census (Full, Men 25-45)1851 England & Wales CensusLong (2005) (2% Sample, Men) to 1881 England 15.2% 28,474& Wales Census (Full, Men)1881 England & Wales CensusLong & Ferrie (2013) (2% Sample, Men 0-25) to 1881 20.3% 14,191England & Wales Census (Full, Men)1881 England & Wales CensusLong & Ferrie (2018) (Sons of Men Linked in Long (2005)) to 32.9% 6,6721911 England & Wales Census (Full, Men)1915 Iowa CensusFeigenbaum (2015) (Golden & Katz (2000, 2008) Sample, Men 3-17) 57.4% 4,349to 1940 US Census (Full, Men)1865 Norwegian Census (Full, Men 3-15)Abramitzky et al. (2012) to 1900 Norwegian Census (Full, Men) or 7.3% 20,4461900 Roster of NorwegiansImmigrants in US (Full, Men)1900 US Census (Subsample ofAbramitzky et al. (2014) white native & European born men 18-35) Native Born: 16.5% 1,650to 1910 US Census (Full, Men) Immigrant: 8.2% 20,218and 1920 US Census (Full, Men)1940 US Census (Full, Men born in South 23-58)Baker et al. (2018) to 1900, 1910, or 1920 White: 27.5% 432,235US Census (in each case Full, Men 3-18) Black: 18.6% 170,92351Table 1.16: Social Mobility Triple Difference(1) (2) (3)VARIABLES Literacy Required Literacy Required Literacy RequiredYears of Treatment 0.00210*** 0.00198*** 0.00237*(0.000719) (0.000719) (0.00127)(Years of Treatment)*(Father Class Dummy) -0.00309** -0.00290** -0.00324(0.00136) (0.00137) (0.00245)Observations 1,379,666 1,365,910 716,101Controls Included NO YES N.A.Birth Parish-Class Fixed Effects Included YES YES N.A.Arrival-Age-Class Fixed Effects Included YES YES YESAge-Class Trend Effects Included YES YES YESArrival-Class Trend Effects Included YES YES N.A.Brother Fixed Effects Included NO NO YESRobust standard errors in parentheses, clustered at parish level. Controls (all interacted with a 1901 dummy, and including interactions withfather’s class dummy): 1871 parish population; 1871 parish population squared; distance from London; distance from London squared; 1871 schoolsupply per capita; 1851 Church of England attendees per capita 1851 Catholic attendees per capita; 1851 other religious service attendees percapita. *** p<0.01, ** p<0.05, * p<0.152Table 1.17: Triple Differences By Father’s ClassFather’s Class Years of Treatment ObservationsHigher Professionals -0.00469 35,560(0.00387)Lower Professionals -0.00106 116,467(0.00239)Skilled Workers 0.00027 249,216(0.00145)Farmers 0.00286 145,305(0.00191)Semi-Skilled Workers 0.00089 348,709(0.00122)Unskilled Workers 0.00387* 114,540(0.00217)Unskilled Farm Labourers 0.00226* 347,875(0.00117)Robust standard errors in parentheses, clustered at the parish level. Controls (all interactedwith a 1901 dummy): 1871 parish population; 1871 parish population squared; distance fromLondon; distance from London squared; 1871 school supply per capita; 1851 Church ofEngland attendees per capita 1851 Catholic attendees per capita; 1851 other religious serviceattendees per capita. *** p<0.01, ** p<0.05, * p<0.153Figure 1.1: School Board Formation by YearNote: Figure 1.1 plots the take up of public school boards following the passage of the 1870 Education Act.54Figure 1.2: Pre-Treatment School SupplyNote: Figure 1.2 maps the 1871 school supply to population ratio at the parish level. Parishes were considered sufficientlysupplied if their ratio was above 1/6, or 0.167. Data are unavailable for parishes within municipal boroughs.55Figure 1.3: Parishes that Received School BoardsNote: Figure 1.3 maps which parishes received school boards between 1870 and 1879. Data are unavailable for parishes withinmunicipal boroughs.56Figure 1.4: First Stage KinkNote: Parishes are binned by 1871 school supply to population ratio using a bin width of 0.07. Figure 1.4 plots the 1871 parishschool supply to population ratio against the fraction of parishes within each bin that received school boards between 1870 and1879. The red line denotes the 0.167 cutoff.57Figure 1.5: Second Stage KinkNote: Parishes are binned by 1871 school supply to population ratio using a bin width of 0.07. Figure 1.5 plots the 1871 parishschool supply to population ratio against the average proportion of men aged 19-30 employed in occupations requiring literacyin 1901 within each bin. These men were of the correct age to have been treated by public schools. The red line denotes the0.167 cutoff.58Figure 1.6: Second Stage Kink Placebo Test: Same Age, Untreated YearNote: Parishes are binned by 1871 school supply to population ratio using a bin width of 0.07. Figure 1.6 plots the 1871 parishschool supply to population ratio against the average proportion of men aged 19-30 employed in occupations requiring literacyin 1881 within each bin. These men were too old to have been treated by public schools. The red line denotes the 0.167 cutoff.59Figure 1.7: Second Stage Kink Placebo Test: Same Year, Untreated AgeNote: Parishes are binned by 1871 school supply to population ratio using a bin width of 0.07. Figure 1.7 plots the 1871 parishschool supply to population ratio against the average proportion of men aged 35-50 employed in occupations requiring literacyin 1901 within each bin. These men were too old to have been treated by public schools. The red line denotes the 0.167 cutoff.60Figure 1.8: Running Variable DensityNote: Parishes are binned by 1871 school supply to population ratio using a bin width of 0.07. Figure 1.8 plots the 1871 parishschool supply to population ratio against the number of parishes within each bin. The red line denotes the 0.167 cutoff.61Figure 1.9: Varying BandwidthNote: Figure 1.9 plots for varying bandwidths the second stage estimates from the regression kink analysis, representing thetreatment effect of school boards on the proportion of men aged 19-30 employed in occupations requiring literacy. Estimatesusing the following bandwidths are plotted: h = 0.0796609 + c ∗ (0.006), where c ∈ {−5,−4, ..., 4, 5}. The optimal bandwidthh = 0.0796609 was selected using the method of Calonico et al. (2014).62Figure 1.10: RK Donut Analysis (Exclusion around kink)Note: Figure 1.10 plots for varying inner bandwidths the second stage estimates from the regression kink donut analysis. Onlyobservations laying within an outer bandwidth but outside an inner bandwidth around the cutoff are used in the estimation. Inall cases, the optimal bandwidth h = 0.0796609 is used as the outer bandwidth. Estimates using the following inner bandwidthsare plotted: h = 0 + c ∗ (0.005), where c ∈ {0, 1, 2, 3, 4, 5, 6, 7}.63Chapter 2Education as Insurance againstResource Busts: Evidence from the19th Century2.1 IntroductionNatural resource booms are famously double-edged swords, with immediate growth oftenfollowed by equally swift decline. This boom and bust pattern has been documented ineconomies rich and poor, local and national, and in a diverse set of industries, including oil,gas, precious metals, and coal.1 While far from the only mechanism at play, human capitalaccumulation has been identified as an important part of the so-called “Natural ResourceCurse.” As documented in Asea & Lahiri (1999), Cascio & Narayan (2015), Douglas &Walker (2017), Abramson & Esposito (2019), and many others, resource booms raise thereturns to unskilled labour, thus increasing the opportunity cost, lowering the relative returnsto education, and, through this channel, reducing future growth. Understanding if and howpolicy can address this effect is thus of first order importance.1van der Ploeg (2011), Frankel (2012), and Marchand & Weber (2018) provide surveys of the literature.64I examine a policy intervention that powerfully altered the incentives to acquire an ed-ucation among those most likely to enter the resource sector: the UK’s 1860 Mining Act.During this period, coal mining was one of the most important industries in the country.The particular features of the Act, combined with the ability to estimate treatment effectsover the course of decades thanks to census-linking, make it an ideal setting to study howgovernment can effectively encourage education in response to a resource boom, and whethersuch education in turn can help insure against future resource busts. Using a triple differ-ence design, I find that the 1860 Act succeeded at increasing human capital accumulationamong those most likely to enter the resource sector. This had long lasting effects on thetreated, improving their likelihood of holding a literate occupation in adulthood. Perhapsmost importantly, treatment is shown to have greatly improved the job prospects of workersforced out of the sector due to local resource busts, thus highlighting an insurance-like effectof education.The Act itself was somewhat unique: unlike the roughly contemporaneous Factory Acts,it did not raise the minimum working age in its targeted industry, nor did it raise theschool leaving age like compulsory school reforms. Instead, it specifically targeted incentives,making mine work contingent on education. Similar to resource extraction today, coal miningin 19th century Britain provided well-paying, low-skilled jobs, and from a young age workingin the mines was a lucrative alternative to attending school. Prior to 1860, boys could begintheir collier careers at age 10, regardless of education level. The 1860 Mining Act changedthis, allowing boys between the ages of 10 and 12 the chance to mine only if they wereconcurrently attending school or could prove they could read and write. This raised thereturn to education among those wishing to work in mines at a young age, as literacybecame the gateway to full time work at the earliest opportunity. Further, among thoseaged 10 and 11 who were not yet literate, it lowered the opportunity cost of attending schoolby disallowing children the opportunity to work otherwise.Using a triple difference design and the full-count 1851 and 1861 censuses, I verify that the651860 Act improved human capital acquisition, increasing the proportion of treated childrenrecorded as “Scholars” in the census by 13%. Linking individuals across the 1861, 1881, and1901 censuses so as to observe them as both children and adults, I also find that treatedchildren were about 17% more likely to obtain occupations that made use of literacy inadulthood. Finally, I test whether their improved education shielded the sons of colliersagainst future resource busts. Instrumenting mining employment opportunities on localmine growth and allowing the treatment effect to vary accordingly, I estimate that, amongthose forced out of the mining industry, treatment by the 1860 Act improved the likelihoodof obtaining a literate occupation by nearly 30 pp.The negative relationship between education and resource dependence is well established.Cascio & Narayan (2015), for instance, find that by increasing the demand for low-skilledlabour, the US shale boom reduced high-school graduation rates in affected areas. Rickmanet al. (2017) observe the same effect, as well as a decrease in post-secondary attendance,while Marchand & Weber (2020) find that the boom led to lower test scores and schoolattendance in affected Texas counties. Douglas & Walker (2017) use differential exposure tocoal mining in Appalachian communities to show that the lower levels of education causedby resource booms left those affected more exposed to future downturns and resulted inlower growth. Abramson & Esposito (2019) suggest that in regions of Europe exposed tocoal mining in the 19th and early 20th centuries, continual demand for low-skilled workerscreated cultural attitudes that devalue education and persist to this day. Yet geography neednot be destiny. I demonstrate in this paper that properly implemented policy can at leastpartially counteract the “Resource Curse” by encouraging education and providing insuranceagainst future shocks.Examination of the 1860 Education Act also provides a new perspective on compulsoryschooling legislation. The demonstrated efficacy of the 1860 Act stands in sharp contrast tothe relative inefficacy of compulsory schooling legislation from the period found elsewhere.For instance, Landes & Solomon (1972) find little evidence of compulsory schooling laws66increasing enrolment in US primary schools from 1880-1910, while Goldin & Katz suggestthat such laws played at most a very small role in High School Movement from 1910-1940.One possible explanation for the difference is the 1860 Act’s focus on incentives as opposedto coercion - it did not mandate school attendance, but rather made it more economicallyattractive. Indeed, in this approach, the 1860 Act may have more in common with moderncash-for-attendance programs of demonstrated efficacy, such as Progresa in Mexico (Schultz2004).Finally, this paper breaks new ground by tracing the effects of historical child labourreform from childhood through to adulthood. While many previous works have examinedthe immediate efficacy of 19th century child labour laws,2 without linked data they have beennecessarily silent on how they affected the adult outcomes of treated children. Using whatis to my knowledge the first linkage of full-count English and Welsh censuses, I demonstratethat the 1860 Act positively impacted the treated well into their adult lives.2.2 Historical Background2.2.1 Coal in 19th Century BritainTo understand the impact of the 1860 Mining Act, it is necessary first to understand thecontext it acted upon. Roy Church, in his history of the British coal industry, notes that “itis difficult to exaggerate the importance of coal to the British economy between 1830 and1913.”3 Coal-fired engines powered factories, trains, and ships across the country, drivingthe production and transportation networks in the world’s industrial leader. It was crucialin the production of steel, and heated the homes of the high and low alike.To satisfy industrial Britain’s thirst for fuel, coal mining became one of the largest in-dustries in the nation. Between 1850-1854 Britain was already producing 58 million tonnes2See, for example, Sanderson (1974), Nardinelli (1980), Kirby (1995), Kirby (2003). For a review of theliterature examining modern child labour laws, see Edmonds (2007).3Church (1986), pg. 75867of coal per year, the equivalent of nearly 3 tonnes per person.4 Yet mining only grew fromthere. According to the 1861 census, 4.5% of men aged 16-50 were employed in the miningof coal; by the 1881 census, 6.1% were; in 1901, 7.7%.5 In contrast, mining, quarrying, andoil and gas extraction together employed fewer than 0.5% of the US workforce in 2019.6It was dangerous work - in the 1850s, on average nearly 0.4% of coal workers died eachyear due to mining accidents.7 Due to this, and perhaps also strong coal unions and lack offoreign competition due to the expense of transporting such a bulky good, coal miners werepaid well.8 As can be seen in Table 2.1, throughout the second half of the 19th century coalmining offered a wage premium relative to other low skill occupations.2.2.2 Child Labour in the MinesPerhaps in part due to the occupation’s wage premium, the sons of miners were very likelyto go on to become miners themselves. As Table 2.2 shows, among men linked across the1861 and 1881 censuses, 59.1% of those aged 11-14 in 1861 whose fathers mined coal werethemselves coal miners in 1881. In contrast, only 3.1% of non-miners’s sons the same agewere. This disparity is of course related to geography: the children of coal miners typicallygrew up near coal mines, and thus often had ready access to mining jobs themselves inadulthood. Indeed, in parishes where at least 10% of men were employed in mining, theproportion of boys aged 11-14 in 1861 who followed in their fathers’ footsteps to become coalminers in 1881 increases to 64.7%. Even in these parishes, though, only 17.5% of non-miners’sons entered the profession, implying that coal mining was very much a family affair. Indeed,boys often followed their fathers into the mines at a very young age. Prior to 1842, it wascommon to see boys and girls aged 8 or 9 working in the mines, and children as young as 54Wrigley (2013), pg. 9.5Own calculations.6US Bureau of Labour Statistics, “Industries at a Glance: Mining, Quarrying, and Oil and Gas Extrac-tion,” 2020.7Hair (1968), pg. 18Williamson (1982), pg. 4268were not unheard of.9There are several reasons why child labour was common in the mines prior to the passageof legislation restricting it. The first is that coal mining was accessible for children. Whileother low skilled occupations were often too physically strenuous for children to perform,there were many positions in the mines that required little strength.10 The youngest childrentypically began their mining careers as “trappers”, manning ventilation doors.11 This jobmerely required them to wait for coal carters to appear, pull on a string to open a door whenthey did, and ensure the door closed behind them.12 Kirby (1995) suggests that “childrenwere brought into the pits to do it at an age when they could have performed no othertask.”13There were certain jobs in the mines that required children. In places where the coalseam was thin, only children were small enough to transport coal through it. Testifyingbefore Parliament in 1866, the president of the North England Institute of Mining Engineersstated that “the men could not do the boys’ work, at least I should not like to see them atit; they would get killed by the work.”14 Indeed, even when children under the age of 12were nominally banned from mines in 1872, the employment of younger children continuedto be allowed in places where “by reason of the thinness of the seams ... such employmentis necessary.”15In addition to demand from mines, there was a plentiful supply of miners willing to sendtheir children to work. One mine inspector wrote in his 1847 report to Parliament that“in very numerous instances the collier, in order to swell the amount of his usually highearnings, will endeavour to take his child down the pit with him at the earliest possible age,9Kirby (1995), pg. 79-10310ibid, pg. 185.11Tuttle (1999), pg. 156.12Kirby (1995), pg. 186.13ibid, pg. 186.14“Select Committee to inquire into Regulation and Inspection of Mines” (1866), p. 338, quoted in Kirby(1995).15“Act to consolidate and amend the Acts relating to the Regulation of Coal Mines and certain otherMines,” 35 & 36 Vict., C.76 (1872).69in preference to sending him to school.”16 As a result, any education the children might havereceived was often cut short.This was not for want of schools. The same mining inspector wrote that “after havinggone through the ... most important mining districts of the kingdom, I venture to assertthat the localities where a child of a collier ... would have to go much more than a mile to aschool are very rare.”17 In another inspector’s 1850 report, the following is written regardingthe children of miners:“The clergy and schoolmasters find with regret that notwithstanding theirexertions to establish good schools at the very low rate of [1 or 2 pence] perweek, the children attend very irregularly, and are generally taken away as soonas they can earn a shilling or two a week, before they have learnt anything welland soundly.”18The result was as one might expect. An 1840 parliamentary report produced by the Com-mittee of Council on Education noted the following:“Boys are taken into the coal or iron mine at eight or nine years old, oftenearlier ... Their occupation consists in opening and shutting air-doors, in throw-ing small pieces of coal or ironstone into the trams, or in handing implementsto the men at work. A boy thus learns early to become a good miner. It is notimprobable, however, that not much skill in that respect would be lost by hisbeginning somewhat later; and it is certain, that from the time he enters themine, he learns nothing else. A mother stated that her husband wanted to takeone of her boys, then only seven years old, into the mine. She said, ‘that herothers had gone there young enough at eight; and after they once went there,they turned stupid and blind-like, and would not learn any thing.’”1916“Inquiry into the Operation of Mines Act, State of Population in Mining Districts, 1847,” pg. 4.17ibid, pg. 5.18“Inquiry into the Operation of Mines Act, State of Population in Mining Districts, 1847,” pg. 31.19“Committee of Council on Education: Minutes, Part II” (1840), p. 212, quoted in Kirby (1995).70Miners’ willingness to send their children below ground may have stemmed in part fromexperience: testifying before parliament in 1842, one miner and father, comparing the workof children and men in mines, stated that “you may sooner bend a twig than a tree.”20 Butincentives presumably played the most important role. As already described, mining was arelatively well paying occupation which required little to no education. If a miner assumedhis son would follow in his footsteps and grow up to be a miner himself, as was commonlythe case, then the return to schooling would no doubt have been low in their minds. At thesame time, the above quotation makes clear the salience of the opportunity cost: it was “assoon as they [could] earn a shilling or two a week” that children were taken out of school.2.2.3 Early Attempts to Regulate Child LabourWhile miners themselves may have been receptive to sending their children to work, publicopinion and legislation gradually turned against child labour in the 19th century. Followingthe passage of Althorp’s 1833 Factory Act limiting the employment of children in textilemills, a commission was formed in 1840 to investigate the use of child labour in mines. Theresulting 1842 Mines Act banned all boys under the age of 10 from working in mines, andfemales of any age.21Mine operators caught employing individuals in violation of the Act were to be fined aminimum of £5 per person, while a parent misrepresenting the age of their child could befined £2 - not insignificant amounts, given that young children typically earned less thantwo shillings (£0.1) per week working in the mines.20“Royal Com. on Children’s Employment in Mines and Manufactories. First Report (Mines and Col-lieries), Appendix, Part II” (1842), p. 304. quoted in Kirby (1995).21“Act to prohibit the employment of women and girls in mines and collieries, to regulate the employmentof boys, and to make other provisions relating to persons working therein,” 5 & 6 Vict., C.99 (1842).712.2.4 1860 Mining ActWhile the 1842 Act increased the minimum age to work in mines, it was silent concerningschooling. This was in marked contrast to the parallel legislation governing factories. Start-ing in 1833 with the passage of Althorp’s Factory Act, work in factories for children aged9-13 was contingent on their attending school at least two hours a day, six days a week.22In their reports to parliament, the government’s coal inspectorate pushed for similar legis-lation to govern coal mining. In his 1847 report, for example, one coal inspector wrote thefollowing:“Persons of intelligence in all parts of the mining districts have expressed tome their regret that the [the 1842 Act] had not thought proper, when excludingboys under 10 years of age from working in the mines, to place their parents undersome kind of compulsion to send them to school for a limited period before theyshould be permitted to work ... Children of miners and colliers require protectionagainst the cupidity or short-sightedness of their parents, or against the demandsof capital, as much, if not more, than children employed in factories; and I believethe testimony ... as to the advantages that have arisen to the factory childrenfrom the ... application of the principle of compulsory education to their case.”23However, it was not until after the Cymer Colliery explosion in 1856, in which 22 childrenunder the age of 12 perished, that public opinion was moved to further regulate the employ-ment of children in mines.24 The resulting legislation was the Mines Regulation Act of 1860,otherwise known as the 1860 Mining Act. The Act nominally banned boys under the ageof 12 from working in mines: “it shall not be lawful ... to employ any male person underthe age of twelve years within a mine or colliery.” However, two important exceptions weremade. First, boys aged 10 and 11 who “were at or before the passing of this Act [August 28,22“Act to regulate the Labour of Children and young Persons in the Mills and Factories of the UnitedKingdom,” 3 & 4 Will. 4, C.103 (1833).23“Inquiry into the Operation of Mines Act, State of Population in Mining Districts, 1847,” pg. 6.24Lewis (1976), pg. 159.721861] employed within the same or some other mine or colliery” were wholly exempted fromthe Act. Second, going forward boys aged 10 and 11 would be allowed to work in mines,provided they satisfied one of two requirements:(a) “Obtain a certificate under the hand of a competent schoolmaster that such boy is ableto read and write,”(b) “In the second and every subsequent lunar month during which such boy is employed... the owner shall obtain a certificate under the hand of a competent schoolmasterthat such boy has attended school for not less than three hours a day for two days ineach week during the lunar month immediately preceding, exclusive of any attendanceon Sundays.”Thus, for children born prior to August 28, 1851, the 1860 Act made coal mining betweenthe ages of 10 and 11 contingent on either attending school or being able to read and write.Concerning enforcement, the Act carried forward much of the 1842 regulation, although itadded a clause stating that schoolmasters found to be providing false certificates of literacyor school attendance would be fined a minimum of £5 for each offence.2.2.5 Enforcement of Mining ActsPrior to the passage of the 1842 Act, no governmental body existed to enforce regulationsin coal mines. To ensure compliance, the 1842 Act allowed the Home Secretary to appointinspectors who were entitled “to visit and inspect any Mine or Colliery ... at all times orseasons, by day or night,” while mine owners were “required to furnish the means necessaryfor such Person or Persons so appointed to visit and inspect such Mines.”25In the early years following the passage of the 1842 Act, however, implementation appearsto have been shoddy. Initially, only a single inspector was employed to enforce the Act, ano doubt Sisyphean task given the over 550 mines across the country he needed to police.2625ibid, pg. 836.26Kirby (1995), pg. 20173Over time, though, the mining inspectorate grew. By 1850 there were 4 inspectors; by1854, 7. By the time the 1860 Mining Act was passed, there were a dozen inspectors taskedwith enforcing coal mining regulations.27 Between the years of 1856-1858, they collectivelyconducted nearly 6000 separate mine inspections in England and Wales.28 Given that in1856 there were 1704 coal mines in operation in those countries, each mine could reasonablyexpect a visit from an inspector each year.29In their attempts to enforce child labour regulations in coal mines, the inspectors wereaided by intra-mine jealously. In an 1846 report to parliament, a mine operator notes“parents of others complain, if we by accident admit any boy under age;”30 in the samereport, another operator states that “the parents all know the ages of each other’s children,and if one were admitted under the legal age, all the rest would want to be. They come andtell us, if a boy gets in before 10 years old.”31Evidence from the 1861 census supports the notion that child labour regulations werewell enforced in mines by that time. As can be seen in Figure 2.1, it was very rare for boysunder the age of 10 to be reported as working in coal mines, even among those whose fatherswere coal miners. Admittedly, the census responses should be taken with a grain of salt,given that parents of working children were often embarrassed or afraid to admit this toenumerators.32 Nonetheless, all evidence suggests that by the time the 1860 Act was passed,child labour laws in mining were effectively enforced.2.3 DataThe primary data sources used in the following analyses are the 1861-1881 and 1881-1901census linkages, described in detail in Chapter 1 of this thesis. These allow me to observe27“Return of Number of Inspectors of Coal Mines for England, Wales and Scotland; Number of CoalMines and of Visits of Inspectors,” (1859).28ibid.29Tuttle (1999), pg. 141.30“Inquiry into the Operation of Mines Act, State of Population in Mining Districts, 1847,” pg. 63.31ibid, pg. 15.32Higgs (2005), pg. 73.74the same individuals both at childhood, when treatment is occurs, and at adulthood, whenoccupation is used to assess outcomes. I make use of Mitch‘s (1992) classification of occu-pations based on their use of literacy. As outlined in Chapter 1, jobs where literacy wasrequired were typically well compensated and viewed in high esteem, and serve as a goodproxy for occupations where the return to general human capital was high.While the 1861-1881 linkage contains the treated cohorts, the 1881-1901 linkage is usedas well, functioning as a control group (see Section 2.4.2 for details). As shown in Chapter1, these linkages both have very high linkage and accuracy rates, and are representative ofthe population. Nonetheless, I make use of the full censuses whenever observation of bothadulthood and childhood is not necessary. In particular, to examine the 1860 Act’s effect onschool attendance, I examine the universe of children in both the 1851 and 1861 censuses.2.4 AnalysisAs described in detail above, the 1860 Act laid out in clear terms which children were eligibleto work in coal mines. Whereas by the 1842 Act any boy 10 and older was eligible to workin the mines, the 1860 Act raised this condition-less eligibility age to 12. Those aged 10 to11 and already working in a mine at the time of the Act’s passing (August 28, 1860) wereallowed to continue to do so. Going forward, boys aged 10 to 11 were only able to work inthe mines if they were concurrently attending school at least two days a week (excludingSunday Schools) or could prove they could read and write.As a result of these rules, boys under the age of 10 at the time of the Act’s passingexperienced not only a barrier to their ability to work in coal mines, but presumably also achange to their incentives to receive an education. While previously serving little purpose forthose bound for the mines, and a costly option after age 10 given forgone wages, educationnow provided a route to earlier employment eligibility. Indeed, one can in theory decomposethe likely effect of the Act on education into several parts, based on age and motivation. For75illiterate boys aged 10 and 11, attending school allowed them to concurrently work part-timein the mines. It also presumably brought them closer to being able to read and write, atwhich point they could devote themselves full time to mining. This second motivation alsoapplied for younger boys: if they could become literate before the age of 10, they couldwork full time in the mines at the earliest possible date. Indeed, for boys under 10, it seemsplausible that the Act affected not only the extensive margin of whether to attend school ornot, but also the intensive margin of how seriously students (and their parents) took theirstudies. In essence, the 1860 Act completely turned on their head the incentives to acquirehuman capital among the children of coal miners young enough to be effected.In contrast, those aged 10 and above at the time of the Act’s passing were presumablylittle affected, due to its grandfather clause. The reform also likely had little effect on boyswhose fathers did not work in the mines. As can been seen in Figure 2.1, while it was verycommon for the sons of miners to work in mines at a young age, it was almost unheard ofamong the sons of non-miners. This was even the case in parishes where coal mining was amajor industry (see Figure 2.2). Given these non-miner sons did not work in mines even priorto the reform, there is little reason to believe the reform changed either their opportunitycost or returns to getting an education.Using these two control groups – those too old to be affected by the reform and thoseunaffected due to their father’s occupation – one can estimate the reform’s effects on thetreated using a difference-in-difference identification strategy.2.4.1 Effect on the Extensive Margin of School AttendanceThe primary focus of this paper concerns how those treated by the 1860 Act experiencedimproved adult outcomes and insurance against negative shocks as a result of their increasedincentives to acquire education,. However, it is first necessary to validate that the 1860 Actreally did increase education acquisition.To that end, I use information from the 1861 Census regarding school attendance, ex-76amining the likelihood that a child’s primary occupation is recorded as “Scholar,” implyingthat they attended school regularly at the time. One would expect that, due to the increasedreturns to becoming literate, miners’ sons born prior to August 28, 1850, and thus youngenough to be treated by the reform, should in 1861 see a jump in school attendance relativeto those older than them. The second panel in Figure 2.3 suggests this is indeed the case -the drop off in school attendance between the ages of 9 and 11 is far steeper among the sonsof miners than it is among other boys.33There is a caveat, however. Even prior to the 1860 Act, boys under the age of 10 weredisallowed from working in mines. The jump observed may reflect this and not any changein incentives due to the 1860 Act. To test this, the 1851 Census is examined as well. If theeffect observed in 1861 were driven by the 1842 Act’s age 10 cutoff instead of the 1860 Act’schange in school incentives, one would expect it to appear in 1851 as well. Comparison of thefirst and second panels in Figure 2.3 suggest that the 1860 Act did play a role: a large gapin attendance rates between miners’ and non-miners’ sons under 10 existed in 1851 but hadnearly disappeared by 1861, while the gap among older ages remained largely unchanged.The effect can be measured more precisely using a triple difference regression framework.This is essentially the difference between two difference-in-differences (DIDs): the first com-paring the 1861 difference in the likelihood of being a “Scholar” between miners’ sons aged6-9 and 11-14 with the difference between non-miners’ sons aged 6-9 and 11-14, and thesecond comparing the same difference but in 1851.34 This can be done using the followingequation:33Given that the 1861 Census was taken in April that year, the age 10 cohort would have straddled thetreatment cutoff.34I exclude children aged 10 from the analysis for two reasons. First, given that only age, not birthdate, isavailable in the census, it is impossible to tell who among those aged 10 at the time of the 1861 census (takenin April) were born prior to August 28, 1850, and thus were unaffected by the reform, and ho were bornafter. Second, age rounding was a well known phenomenon at this time, where individuals would report theirages to the nearest multiple of 5 or 10. As a result, it is assumed likely that a large number of individualsreporting to be age 10 are actually several years older or younger.77Yi,t,p,a,j = δ + γ1Jj + γ2Aa + γ3Tt + γ4(Aa ∗ Jj) + γ5(Aa ∗ Tt)+γ6(Tt ∗ Jj) + α(Aa ∗ Jj ∗ Tt) + ui,t,p,a,j(2.1)where Jj is a occupation dummy equal to 1 if i’s father’s occupation j is coal mining and 0otherwise, Aa is an age dummy equal to 1 if i’s age a is 6 ≤ age ≤ 9 and 0 if 11 ≤ age ≤ 14,Tt is a time dummy equal to 1 if i is from the 1861 Census and 0 if from 1851, and prepresents i’s parish of residence. α identifies the difference in difference-in-differences, orthe treatment effect.The results are reported in Table 2.3. The first two columns report the results of a simpleDID on age and father’s occupation, using only the 1861 Census. While these suggest thatthe treatment improved the likelihood of miners’ sons being “Scholars” during the ages of6-9 by nearly 20 pp, these results should be viewed as the cumulative effect of the 1842and 1860 Acts. The isolated effect of the 1860 Act is estimated using the triple difference,with results shown in the final two columns. They suggest that the incentive among miners’children to become literate by age 10 created by the 1860 Act improved the likelihood ofbeing a “Scholar” by nearly 8 pp. Given that around 68% of miners’ sons aged 6-9 in 1861were recorded as “Scholar”, this implies and increase of around 13%.It is worth pointing out that this likely does not represent the full effect that the 1860Act had on human capital acquisition. Whether or not a child was recorded as a “Scholar”in the census likely only picks up the extensive margin of school attendance. The intensivemargin of school attendance varied widely at the time, with many students only attendinga day or two per week. Given that, even absent the reform, around 60% of treated childrenwould have attended some school, it seems plausible that much of the impact of the reformwould have been on how actively these children pursued their studies. Further, one wouldexpect the 1860 Act to also significantly increase schooling at ages 10 and 11, at least amongthose not already literate by age 10. However, since at the time of the 1861 Census theoldest fully treated cohort were only age 9, it is impossible to measure this effect. Thus,78the schooling effect measured above should be viewed merely as a demonstration that the1860 Act did affect education incentives, motivating the analysis conducted below concerningadult outcomes.2.4.2 Effect on Adult OccupationIf the 1860 Act increased the stock of human capital, one would expect the treated to bemore likely to hold human capital-intensive occupations in adulthood. To test this, I makeuse of the linkage of the 1861 and 1881 censuses, described above, allowing me to observeindividuals both as children and adults. In particular, I wish to test whether those treatedby the reform as children were more likely as adults to hold an occupation that made use ofliteracy.To this end, I use a difference-in-differences framework similar to that used above toanalysis schooling, comparing the difference in the likelihood of holding a literate occupationin 1881 between miners’ sons aged 6-9 and 11-14 in 1861 with the difference between non-miners’ sons aged 6-9 and 11-14 in 1861. The results are reported in the first two columns ofTable 2.4. They suggest that the 1860 Act improved by between 1.7 and 2.1 pp (or 10-14%)the likelihood a miner’s son aged 6-9 in 1861 held a literate occupation in 1881.Note that while in the preceding section this DID was contaminated by the 1842 Act’sban on children under the age of 10 mining, this should not be the case here. Once over theage of 10, all those in the sample had been equally treated by the 1842 Act, and thus anydifferences in adult outcomes cannot be caused by it.While the 1842 Act is unlikely to be driving results, it is still the case that the results areonly valid if, in the absence of the reform, the difference between the likelihood of a 6-9 yearold miners’ son vs. a 11-14 year old miners’ son holding a literate occupation 20 years laterwould have been the same as the equivalent difference among the sons of non-miners. This isessentially the parallel trends assumption common to DIDs, although compared across ages,rather than across time as is more typical. If true, one would expect the relationship between791861 age and likelihood of an 1881 literate occupation to exhibit similar trends across otherages for both miners’ and non-miners’ sons. Figure 2.4 demonstrates that this is indeed thecase.35If one remains unconvinced of the parallel trends assumption, comparison with children ofsimilar age and background, but born a generation later, provides further evidence. Unlike in1861, there is little reason to suspect a break at the age of 10 in adult occupation outcomesexists among the sons of coal miners in 1881.36 If something other than the 1860 Actimproved the outcomes of miners’ sons aged 6-9 relative to those aged 11-14, one mightassume this would show up in 1881 as well. However, as Figure 2.5 demonstrates, this wasnot the case. Indeed, the likelihood of holding a literate occupation in 1901 was slightlylower among those aged 6-9 relative to those aged 11-14 in 1881 among miners’ sons thanamong non-miners’ sons.Another way of demonstrating the robustness of the 1861 results is to directly incorporatethe 1881 control group into the regressions, using a triple difference. To that end, I reuseEquation 2.1, redefining Tt such that it is equal to 1 if i is from the 1861-1881 linkage and 0if from the 1881-1901 linkage.The results are reported in the final two columns of Table 2.4. Reflecting the fact that,as already discerned from Figure 2.5, the 1881 DID is slightly negative, the triple differenceestimates are larger than those obtained using the 1861 DID alone. The reform is estimatedto have improved the likelihood of the treated holding a literate job in adulthood by around2.5 pp, or 17%.As previously implied, the results of the triple difference can be viewed as a placebo35Note that to construct Figure 2.4, as well as Figures 2.5 and 2.6, the 1861-1881 and 1881-1901 censuslinkages described in Chapter 1 were extended to include those aged 0-4 in the early census (1861 or 1881)and aged 20-24 in the late census (1881 or 1901).36Both above and below the age dummy cutoff, mining children would have been subject to the 1872Mining Act, which essentially banned all children under 12 from mining. The arrival of public schools inthe decade following the 1870 Education Act may have resulted in a slightly more educated younger cohortamong working class children. However, the vast majority of these schools were running by 1875, meaningthere would have been little variation in treatment among the ages examined here. If anything, by increasingthe human capital of younger mining children in 1881 relative to other children, this should, when comparedwith 1861 children, lead to an underestimation of the 1860 Act’s effect.80test, confirming that the effect found in 1861 using the original difference-in-differences doesnot also exist in 1881. Alternatively, one can view it as a loosening of the parallel trendsassumption. Under the triple difference, the trend across ages in the absence of the reform nolonger needs to be the same for both miners’ and non-miners’ sons, as long as the differencein trends would not have changed between 1861 and 1881 in the absence of the reform.2.4.3 Booming vs. Busting MinesI have shown that the 1860 Act increased the likelihood of obtaining a literate occupation inadulthood. Yet even among treated children, a very large proportion of miners’ sons grewup to became coal miners themselves. As can be seen in Figure 2.6, nearly 60% of thosewhose father’s were miners in 1861 were themselves miners in 1881, regardless of age. Thisis consistent with the previously discussed wage premium paid to miners relative to otherlow-skilled occupations. Even with the ability to read and write, mining was still often themost lucrative career available to the children of miners. But it was not always available. Asmines aged and deepened, they became less and less profitable, eventually shutting down.This was typically a gradual affair - mines usually consisted of several pits, which would beabandoned one by one over time.37 The result was that industry growth varied hugely acrosscoal producing parishes. In the communities where the mine shrank, miners’ children wereoften forced out of the industry. When this occurred, the effects of the 1860 Act appear evenstronger.To demonstrate this, one must first define which parishes are “coal producing”. For eachof the 1861 and 1881 censuses, I classify a parish as a coal mining community if at least 10%of men aged 16-50 were employed in any occupation related to coal (including coal merchant,coal carter, colliery fitter, etc.) and at least 5% of men aged 16-50 were specifically employedas “Coal Miners – Hewers, workers on the coal face”. To be included in the following analysis,I also require that the parish contains at least 50 individuals between the ages of 0-20 in the371859 Mining Commissioner’s Report, pg. 9811861 (1881) census that I successfully link to 1881 (1901) census.38Figures 2.8 and 2.9 display where these coal communities were located in the country in1861 and 1881, respectively. As can be seen, coal mining was concentrated a few regions- Southern Wales, the West Midlands, and the North. These maps also show which minesgrew over the following 20 years. Encouragingly for identification, mine growth does notappear to be concentrated in any particular region, suggesting that it primarily dependedon local mine conditions and not, for example, on regional demand.I then divide these parishes in quintiles based on the growth of their mining workforce inthe 20 years following the base census year (either 1861 or 1881). The first panel of Figure2.7 clearly demonstrates the large variation in growth. While parishes in the bottom quintileoften saw their mining workforce shrink by over 50%, parishes in the top quintile experienceda doubling or more of theirs. The consequences for the employment prospects of miners’ sonsin the control group (those aged 11-14) in the base year can be seen in the second panel. Inparishes belonging to the top three quintiles, where the mining workforce grew, the likelihoodof miners’ sons themselves becoming miners is fairly steady at around 70%.39 In parisheswhere the workforce was shrinking, however, the likelihood drops considerably. Only 60.1%of 1861 miners’ sons growing up in a parishes belonging to the quintile second from thebottom become miners themselves, and only 55.6% in the bottom quintile, implying that inparishes with shrinking mines many sons of miners were compelled to seek other work.If, due to their changed incentives, children young enough to be affected by the 1860 Actbecame better educated, they may have been better able to obtain a good occupation whenforced out of mining than those slightly older. I test this hypothesis in a number of ways.First, I redo the triple difference regressions, but exclude from the sample all miners’ childrenwho reside in parishes with shrinking mines or non-mining parishes. Thus, I am left with allchildren of non-miners, and miners’ children who reside in parishes with growing mines. I38All the results reported below are robust to changing my definition of coal mining community.39The reason the proportion of miners’ sons becoming miners themselves in adulthood is much higher inFigure 2.7 than in Figure 2.6 is because Figure 2.7 excludes miners’ residing outside of mining parishes.82then repeat the exercise, but including miners’ children from parishes with shrinking minesand excluding those from parishes with growing mines and non-mining parishes.The results are shown in Table 2.6. The first two columns demonstrate the reform’seffect on the likelihood of miners’ sons aged 6-9 from parishes with growing mines obtainingliterate adult occupations, suggesting it increased by around 1.9 pp as a result. Unsurprising,this estimated effect is smaller than previously estimated, implying that where mining jobswere plentiful, treated children made little use of improved human capital. The converse canbe seen in the final two columns, which show the effect on miners’ sons aged 6-9 broughtup in parishes with shrinking mines. There, the reform is estimated to have improved thelikelihood of these treated boys obtaining literate adult occupations by 5.3-5.6 pp. Giventhat 17.8% of them ended up in such occupations, this represents an increase of over 40%from what would otherwise have been the case.Table 2.5 compares the summary statistics of growing and shrinking mining parishes.The two groups appear to have been very similar to begin with; while shrinking parisheswere on average slightly more populated at first, both the proportion of men employed inmines and the proportion employed in literate occupations started out very similar betweenthe two groups. The difference in treatment effect sizes presumably then is not driven byany pre-period differences.The evidence thus strongly suggests that the improved human capital among the childrenof miners treated by the 1860 Act acted as a form of insurance, protecting miners’ sons fromindustry busts by improving their employment prospects outside of mining. When localmines continued to offer ready employment, these children made little use of their education.But in locations where mining employment became more difficult to obtain, children youngenough to be affected by the 1860 Act performed much better on the job market.832.4.4 Effect of 1860 Act on those Compelled to Leave MiningIt is possible to be more precise concerning how effectively education insured against miningbusts. If one knew precisely which miners’ children, in the absence of the reform, wouldhave desired to work in the mines but were unable to due to industry conditions, one couldestimate how effectively the 1860 Act insured such children using the difference-in-differenceson time and age:Yi,t,a,p,j=M,f=F = δ + γ1Tt + γ2Aa + α3(Aa ∗ Tt) + ui,t,p,a,j=M,f=F (2.2)where j = M implies that only the sons of miners are included, and f = F implies allwere forced to seek employment outside of mining. Provided the usual assumptions hold,α3 would identify how much more likely a child forced out of mining would be to obtain aliterate occupation in adulthood as a result of the 1860 Act.It is impossible to know precisely which children were forced out of mining and whichwould have left regardless. However, if one knew the likelihood that an individual in parishp was forced out of the industry (Fp), the following regression could be run:Yi,t,p,a,j=M,f = δ + γ1Tt + γ2Aa + γ3Fp + γ4(Aa ∗ Tt) + γ5(Aa ∗ Fp)+γ6(Tt ∗ Fp) + α4(Aa ∗ Fp ∗ Tt) + ui,t,p,a,j=M,f(2.3)Assuming that the effect of the 1860 Act on the likelihood of holding a literate occupationamong miners’ sons who would have left the mines voluntarily is unrelated to the proportionof those forced to leave, then α3 = α4.To estimate Fp, I instrument the likelihood that a miner’s son from the age 11-14 controlgroup is employed outside of mining in adulthood with the growth rate of their local min-ing workforce. Given the non-linear relationship between mining growth and employmentprospects suggested by Figure 2.7, I divide mining parishes into quintiles based on growth(as shown in Figure 2.7) and instrument on quintile dummies. Thus the first stage looks as84follows:Ni,t,p,11≤a≤14,j=M = β0 + β1Tt + ζ1Q1,p + ζ2Q2,p + ...+ ζ5Q5,p + ui,t,p,11≤a≤14,j=M (2.4)where Ni is a dummy equal to 1 if i is not a miner in adulthood, and Qx,p is a dummy equalto 1 if parish p belongs to growth quintile x. I then use the predicted values from the firststage in the place of Fp in Equation 2.3 to find α4.The second-stage results are shown in Table 2.7. They imply that among miners’ childrenwho, if given the opportunity, would grow up to become miners themselves but were forcedout of the industry due to depression of the local mining industry, the 1860 Act improvedtheir likelihood of obtaining a literate occupation in adulthood by nearly 30 pp.This identification rests on several assumptions. The first is essentially a revised paralleltrends assumption: in the absence of treatment from the 1860 Act, any differences in howminers’ sons aged 6-9 would have been affected by the growth rate of the local miningworkforce relative to those aged 11-14 would have been the same in 1861 and in 1881. Thesecond assumption is the exclusion restriction for the instrument, which requires that anyeffect that is unique to the treatment group that the local mining workforce growth rate hadon the likelihood of holding a literate occupation in adulthood must have come through itseffect on the likelihood of these children becoming miners in adulthood. This allows for themining growth rate to affect the likelihood of holding a literate occupation in other ways,provided these effects are common to at least one of the control groups, either those too oldto be treated or those the same age but found in the 1881 census.One way to test these assumptions is to conduct a placebo test using non-miners’ children.Given non-miners’ sons rarely worked in the mines during childhood and were thus essentiallyunaffected by the 1860 Act, the revised parallel trends assumption implies there should beno effect among them. Table 2.8 shows the results of this placebo test. As expected, theestimated effect is close to zero.852.5 ConclusionThe 1860 Mining Act is difficult to categorize. It neither raised the minimum workingage among miners, nor made education universally compulsory. Instead, by tying work andeducation together, it effectively changed the incentives to acquire human capital. Previouslya waste of time among children expected to become miners, education suddenly became atool for them to begin work sooner.This paper shows that, as a result, mining children became significantly more likelyto attend school. Further, their improved human capital often played an important rolein determining their adult outcomes, increasing the odds of holding a literate occupationin adulthood by around 17%. Most importantly, it effectively insured them against localmining downturns, increasing the odds that those forced to leave the industry ended up inliterate occupations by nearly 30 pp.This paper advances the literature on several fronts. First, by making use of newly linkedcensus data, it provides the first historical evidence that child labour legislation can effectoutcomes well into adulthood. Second, in contrast with previous findings suggesting thathistorical laws compelling school were relatively ineffective, the 1860 Act’s incentive basedapproach is shown to perform quite well, perhaps lending some support to modern market-based approaches. Finally, the results produce a clear policy takeaway, demonstrating thatthrough effective education incentives, governments can help insure their citizens in resource-dependant regions against future downturns.86Tables & FiguresTable 2.1: Low Skilled Occupation Earnings, EnglandOccupation 1861 1881 1901Agricultural Labourers 36.04 41.52 46.12Non-agricultural Labourers 44.18 55.88 68.90Police, Guards, Watchmen 53.94 76.73 68.69Coal Miners 62.89 59.58 89.37Source: Williamson (1982)Table 2.2: Summary StatisticsMiners’ Son Non-miners’ SonAge in 1861 6-9 11-14 6-9 11-14Parish Population, 1861 7,257 6,994 9,359 9,257Parish Population, 1881 9,715 9,318 12,367 12,306% with Job in Mining, 1881 58.5 59.1 3.3 3.1% with Literate Job, 1881 17.2 17.2 40.4 42.1Observations 11,345 8,255 253,645 190,892Miners’ Son Non-miners’ SonAge in 1881 6-9 11-14 6-9 11-14Parish Population, 1881 9,684 9,850 12,425 12,197Parish Population, 1901 19,408 19,408 31,883 30,528% with Job in Mining, 1881 63.7 62.7 3.8 3.6% with Literate Job, 1881 17.0 18.3 46.3 46.9Observations 30,855 22,216 418,317 325,497Note: The top panel describes the summary statistics of men linked between the 1861 and1881 censuses. The bottom panel describes men linked between the 1881 and 1901 censuses.87Table 2.3: 1860 Act’s Effect on Likelihood of Attending SchoolDiff-in-Diff Triple Difference(1) (2) (3) (4)Scholar Scholar Scholar ScholarTreatment Effect 0.1977*** 0.1976*** 0.0799*** 0.0784***(0.0081) (0.0081) (0.0119) (0.0118)Observations 1,590,627 1,590,627 2,955,140 2,954,680Parish-Year Fixed Effects NO YES NO YESAge-Year Fixed Effects NO NO NO YESNote: All standard errors are clustered at the parish level.*** p<0.01, ** p<0.05, * p<0.1Table 2.4: 1860 Act’s Effect on Literate OccupationsDiff-in-Diff Triple Difference(1) (2) (3) (4)Literate Job Literate Job Literate Job Literate JobTreatment Effect 0.0168*** 0.0205*** 0.0246*** 0.0251***(0.0056) (0.0056) (0.0067) (0.0067)Observations 463,625 462,763 1,222,534 1,221,045Parish-Year Fixed Effects NO YES NO YESAge-Year Fixed Effects NO NO NO YESNote: Columns 1 and 2 report the difference-in-differences results using the age and father’s occupationdimensions, restricting the sample to children from 1861. Columns 3 and 4 report the triple difference results,including 1881 children. All standard errors are clustered at the parish level.*** p<0.01, ** p<0.05, * p<0.188Table 2.5: Summary Statistics, Mining Parishes Only1881 1901VARIABLES Mine Shrinking Mine Not Shrinking Mine Shrinking Mine Not ShrinkingPopulation, t-20 3022 2560 4439 3319Population 3289 4359 15,718 16,300% of Jobs in Mining, t-20 31.1 34.7 37.0 40.9% of Jobs in Mining 22.1 44.0 30.0 50.3% of Jobs Requiring Literacy, t-20 20.5 19.9 22.5 22.0% of Jobs Requiring Literacy 26.5 21.5 28.1 21.6Parishes 195 475 233 528Note: Summary Statistics of Mining Parishes, defined as those that satisfy all of the following: at least 10% of men aged 16-50 are employed in anyoccupation related to coal (including coal merchant, coal carter, colliery fitter, etc.); at least 5% of men aged 16-50 are specifically employed as “CoalMiners – Hewers, workers on the coal face”; at least 50 individuals between the ages of 0-20 in the 1861 (1881) census are successfully linked to 1881(1901) census. “Mine Shrinking” includes those parishes that saw their mining workforce shrink from 1861 (1881) to 1881 (1901); “Mine NotShrinking” includes all other mining parishes.*** p<0.01, ** p<0.05, * p<0.189Table 2.6: Triple Difference, Growing vs. Shrinking MinesShrinking Mines Excluded Growing Mines Excluded(1) (2) (3) (4)Literate Job Literate Job Literate Job Literate JobTreatment Effect 0.0185** 0.0188** 0.0526*** 0.0563***(0.0083) (0.0083) (0.0159) (0.0163)Observations 1,159,646 1,105,321 1,158,147 1,103,821Parish-Year Fixed Effects NO YES NO YESAge-Year Fixed Effects NO YES NO YESNote: Columns 1 and 2 exclude children from coal mining parishes whose mining workforce grew, while Columns3 and 4 exclude children from coal mining parishes whose mining workforce shrunk. All standard errors areclustered at the parish level.*** p<0.01, ** p<0.05, * p<0.1Table 2.7: Mining Opportunities(1) (2)Literate Job Literate Job(Age Dummy)x(Year Dummy)x 0.2600* 0.2868*(Likelihood of Mining Employment) (0.1533) (0.1605)Observations 56,411 56,411Parish-Year Fixed Effects NO YESAge-Year Fixed Effects NO YESFirst Stage Cragg-Donald Statistic 273.50 535.46Note: “Likelihood of Mining Employment” is the proportion of boys aged 11-14 in thesample who were employed as coal miners 20 years later, instrumented using the growthrate of the parish’s mining workforce.*** p<0.01, ** p<0.05, * p<0.190Table 2.8: Mining Opportunities Placebo: Children of Non-Mining Fathers(1) (2)Literate Job Literate Job(Age Dummy)x(Year Dummy)x 0.0837 0.0328(Likelihood of Mining Employment) (0.1099) (0.1073)Observations 96,189 96,189Parish-Year Fixed Effects NO YESAge-Year Fixed Effects NO YESFirst Stage Cragg-Donald Statistic 386.97 803.72Note: “Likelihood of Mining Employment” is the proportion of boys aged 11-14 in thesample who were employed as coal miners 20 years later, instrumented using the growthrate of the parish’s mining workforce.*** p<0.01, ** p<0.05, * p<0.191Figure 2.1: Use of Child Labour in Mines, 1861Note: Figure 2.1 displays the percentage of boys employed in mines by age in 1861, both among those whose father’s are minersand among all other children.92Figure 2.2: Use of Child Labour in Mines, 1861, Mining Parishes OnlyNote: Figure 2.2 displays the percentage of boys employed in mines by age in 1861, given they reside in a coal mining parish.93Figure 2.3: Coal Mining ParishesNote: Figure 2.3 displays the percent of boys whose primary occupation is recorded in the census as “Scholar,” both in 1861 and 1851, as well as among the sons of minersand among all other boys.94Figure 2.4: 1881 Occupation Attainment by 1861 AgeNote: Figure 2.4 displays the relationship between age and having an occupation that makes use of literacy in 1881, for boththe children of miners and other children. Likelihood of holding a literate occupation is demeaned for each group.95Figure 2.5: 1901 Occupation Attainment by 1881 AgeNote: Figure 2.5 displays the relationship between age and having an occupation that makes use of literacy in 1901, for boththe children of miners and other children. Likelihood of holding a literate occupation is demeaned for each group.96Figure 2.6: Mining Transmission from Fathers to Sons, 1861Note: Figure 2.6 displays the percentage of coal miners’ sons linked from 1861 to 1881 who, by 1881, were themselves employedas coal miners.97Figure 2.7: Coal Mining ParishesNote: I divide coal mining parishes into quintiles based on the growth of their mining workforce, shown in the first panel of Figure 2.7. The second panel displays for eachquintile the likelihood the child of a miner will themselves become a miner in adulthood.98Figure 2.8: 1861 Coal Mining ParishesNote: Figure 2.8 displays coal mining communities in 1861, as well as whether or not their mining workforce grew in thesubsequent 20 years. Parishes are considered as coal mining communities if at least 10% of men aged 16-50 were employed inany occupation related to coal (including coal merchant, coal carter, colliery fitter, etc.), at least 5% of men aged 16-50 werespecifically employed as “Coal Miners – Hewers, workers on the coal face”, and at least 50 men are linked from the 1861 to1881 censuses.99Figure 2.9: 1881 Coal Mining ParishesNote: Figure 2.9 displays coal mining communities in 1881, as well as whether or not their mining workforce grew in thesubsequent 20 years. Parishes are considered as coal mining communities if at least 10% of men aged 16-50 were employed inany occupation related to coal (including coal merchant, coal carter, colliery fitter, etc.), at least 5% of men aged 16-50 werespecifically employed as “Coal Miners – Hewers, workers on the coal face”, and at least 50 men are linked from the 1881 to1901 censuses.100Chapter 3Post-Conflict Outcomes:Community-Level Effects of WWIDeaths in Post-War England andWales3.1 Introduction“War is hell”—General William Sherman, 1879War may indeed be hell, but what comes after is uncertain. Numerous papers have begunquantifying what was long supposed: the effects of war continue long after the shooting stops.For example, Ghobarah et al. (2003) and Li & Ming (2005) both find national mortalityrates tend to increase post-conflict to such an extent that the resulting loss of life is typicallysimilar to that directly caused by the conflict itself. Ichino & Winter-Ebmer (2004) findthat WWII caused a sharp drop in child educational achievement in participating Europeannations, the results of which were felt well into the 1980s. Unfortunately, many of these101papers suffer from similar data limitations, and few have examined economic variables suchas employment and poverty. This paper seeks to fill this gap in the literature by directlyexamining the effect of soldier mortality on changes in poverty and employment outcomesin local English and Welsh communities.In their seminal survey on the economic literature of civil wars, Blattman & Miguel(2010) document many papers examining the causes of conflict, but stress the need forfurther work on its economic consequences. In particular, they point out the lack of researchusing sub-national data. One issue with past examinations of post-conflict effects stemsfrom the common use of nation level panel data. In such models, identification rests on theassumption that it is conflict itself that is driving the results and not some correlated butunobserved variable. However, this assumption appears strong. One suspects that forcesstrong enough to lead a state into conflict could very well have an impact on health andeconomic outcomes with or without conflict occurring. Even when country level fixed effectsare employed only time-invariant omitted variables are captured, yet it seems likely that thecauses of conflict will often vary across time. Thus the case for omitted variable bias in suchmodels is strong. Acemoglu & Lyle (2004) avoid such difficulties by relying not on whether anation was involved in conflict, but rather on local variation in conflict participation withina nation. Specifically, they use variation of US state WWII recruitment levels to examinepost-war effects on female labour supply. Riano & Valencia (2020) use local variation toexamine the long-run impact of the bombing of Laos during the Vietnam war. Abramitzkyet al. (2011) also rely on local variation, but in soldier mortality rates. They use soldierdeath rates from each of WWI France’s 22 War Regions to examine the effect war inducedgender imbalances have on post-conflict marriage markets. Boehnke & Gay (2020), perhapsthe closest complement to my work, also use variation in WWI French soldier mortalityrates, but at a finer level - examining Departments, of which there were 87. They find thathigh soldier death rates increased post-war female labour, and suggest this was driven bysupply forces - women forced to enter the labour market due to the negative income shocks of102widowhood and the poor marriage market caused by sex-ratio imbalances - and not demandforces caused by the decrease in the male workforce.Similar to Boehnke & Gay, this paper examines post-conflict effects by exploiting varia-tion at the local level in soldier mortality rates, but differs in several key areas. First, whilethe death data of Boehnke & Gay was broken down by Departments, of which there were87, the dataset of British soldier deaths utilized here provides much more specific locationdata. This allows a more localized analysis and improved sample size. For instance, povertyoutcomes are examined at the Registration District level, of which there were over 600 atthe time. Second, while the change from France to Britain may appear merely cosmetic, itserves a specific purpose. Given that much of the Western Front of the war lay within Frenchborders, it appears likely that within those regions mortality rate would also be related toother conflict effects, such as infrastructure damage. Britain, on the other hand, saw nofighting on its soil.1 This makes it ideal for isolating the effect of soldier mortality. Finallyand perhaps most importantly, where their work was silent concerning conflict’s effects onpoverty rates, I am able to make use of the detailed statistics provided by the English PoorLaw system.There are several possible mechanisms through which soldier deaths might impact em-ployment and poverty rates. One obvious way is through a negative labour supply shock: adecrease in working age men may increase wages and employment rates of those left behind.By reducing the population but leaving the stock of capital and land essentially unchanged,capital intensity and land per capita increases, making the remaining population more pro-ductive. This is essentially a Malthusian argument: living standards rise along with thedeath rate. This type of shock is not unprecedented: it has been well documented that realwages grew significantly in the years following the Black Death in the 14th century.2 Indeed,Voigtla¨nder & Voth (2013) point out that conflict played an important role in spreading the1There was a very small amount of bombing targeting London, which is duly excluded from analysis insome specifications as a robustness check (see Section IV). Further information concerning WWI bombingin Britain can be found in Cole & Cheeseman (1984).2See, for instance, Pamuk (2007) or Bridbury (1973).103diesese, and in this way contributed to the “Rise of Europe.” While the demographic changescaused by the First World War may not have been quite as dramatic as those caused by theplague, they still were significant.3 If this were the primary effect, post-conflict survivorsmay actually have benefited in some senses from the terrible loss of life brought about bythe war. Of course, it is also likely that these effects would be at least somewhat mitigatedby migration, with wage differentials pushing men from low to high death regions. The sizeof this effect depends on the prevalence of internal migration in England and Wales at thetime, which is discussed further in the data section. On the other hand, the loss of the mostfit and able young men may have led to local economic depression and increased povertylevels. Due to the patriarchal nature of early 20th century British labour markets, many ofthe soldiers who died would have been their family’s sole breadwinner. It is entirely possiblethat a higher death rate may have resulted in more poverty, forcing families that lost youngmale workers to seek alms. Thus, ex ante it is difficult to predict how soldier death rateswould affect poverty rates.Also of interest is whether or not such effects varied by gender. Examining the deteri-oration of health outcomes in post-conflict nations, both Ghobarah et al. and Li & Mingfind women to be disproportionately affected.4 It is possible to imagine a similar scenarioplaying out in post-war Britain. Given that the vast majority of the workforce at the timewas male, benefits accrued due to a negative labour supply shock may have only passed tomen. On the other hand, it is also possible that communities which endured more severelabour supply shocks turned to women to fill the void.Using a difference-in-difference approach, I find that higher conflict death rates are as-sociated with a fall in a local measure of poverty rates, supporting the labour supply shockhypothesis. There is evidence that the effect varied by gender, being stronger among men3According to Pamuk (2007), from the time the plague hit in the mid-14th century until the centuriesend, Europe’s total population declined by almost a third. In comparison, Winter (1977) estimates that6.7% of British men aged 15-50 died as a result of the First World War.4Both suggest this may be because in nations where conflict often takes place, women tend to enjoyfewer rights than men, and thus are less likely to receive care in times of crisis.104than women. I also find weak evidence suggesting that employment rates rose where deathrates were higher, particularly among women. Taken together, these two findings corrob-orate Boehnke & Gay’s suggestion that increases in female labour were driven by supplyincreases, brought on by fear of poverty.I also examine how the sex-imbalance of war deaths affected the rate of out-of-wedlockbirths. The analysis is motivated by the notion, described and modeled in Willis (1999), thatmen find it easier to attract partners and propagate children without having to invest in themin communities where the male to female ratio is lower among those of childbearing age. Menin these communities have more bargaining power in marriage markets relative to women,and thus are more able to shift the costs of childcare to single mothers. Abramitzky et al.,Bethmann & Krasickova (2013), Brainerd (2017), Battistin (2020), and Alix-Garcia et al.(2020), have all recently examined the impact of war-induced sex ratio changes, and severalhave concluded that fewer males to females result in an increase in the out-of-wedlock birthshare.5 Though the primary focus of this paper is on the effect of war deaths on economicoutcomes, I also confirm these findings, using a more localized and much larger sample sizethan used by any of the previous papers.Soldier death data is gathered from British Army and Navy records. While the originalsources are currently held at the National Archives in Kew, UK, they have been digitizedand made available online by several genealogy companies, including Ancestry, from whichthe data used here were obtained. The remainder of this paper’s data come from numeroussources digitised by the Great Britain Historical Geographic Information System (GBHGIS)Project, a graphical linkage of historical British statistics. The original sources are the 1913and 1920 British censuses, 1913 and 1921 registers of annual total births, and 1912 and 1922reports to parliament concerning pauperage totals.The GBHGIS data are discussed, along with historical context, in Section 3.2. The5Abramitzky et al. examines WWI era France, Bethmann & Krasickova WWII era Bavaria, BrainerdWWII era Soviet Union, Battistin WWII era Italy, and Alix-Garcia et al. Paraguay after the War of theTriple Alliance.105sources, collection methods, and adjustments to soldier death data, along with instrumentsutilised to correct for measurement error, are described in Section 3.3. Section 3.4 discussesthe models used, while Section 3.5 goes over the results obtained. Finally, Section 3.6concludes and outlines suggested areas of future inquiry.3.2 GBHGIS Data and Historical Context3.2.1 Geography and Data AggregationDue to the fact that the microdata for the 1921 census will not be released until 2021,6aggregated data must be utilized. An issue arising from this is that the level of aggregatestatistics reported varied across variables, as can be seen in Table 3.1. This issue is aggravatedby the confusing nature of early 20th century British administrative geography. The basicbuilding block was the parish, of which there were 14,665 within England and Wales in 1911.Parishes were combined to form Local Government Districts (LGDs) (of which there were1,841 in 1911) and Registration Districts/Poor Law Unions (PLUs) (635 in 1911). However,while LGDs typically lay within PLUs, this was not always the case. Thus, it is not a simpletask to aggregate from LGDs to PLUs. To further complicate matters, PLUs combine toform registration counties, of which there were 55 in at the time, while LGDs combine toform administrative counties, of which there were 61 excluding the Isle of Wight. Figure3.1 provides a flow chart describing the geographic hierarchy. Appendix B.1 provides a briefdescription of the powers exercised by each level of government (with the exception of PLUs,the powers of which described later this section).Sex ratios and out-of-wedlock birth rates were reported at the LGD level, employmentrates at the Administrative County level. For analysis regarding pauperage rates, conductedat the PLU level, population statistics are needed but are only provided in the 1911 census,not the 1921 census. As outlined above, simply aggregating LGD populations is not possible,6It is UK policy to release census microdata after 100 years.106due to the fact that not all LGDs lie within a single PLU. Therefore, estimates are determinedfrom LGD and parish level data, exploiting the fact that in 1911, both LGDs and PLUs weremade up of parishes. A detailed description of this estimation is provided in Appendix B.2,while Appendix B.3 describes how possible border changes are addressed.Finally, for the analysis conducted at the PLU level, it must be acknowledged that thesepoverty rates are no doubt closely tied to labour market conditions shared across metropoli-tan areas. Therefore, in cases where a single metropolitan area is broken down into severalPLU, these PLUs are aggregated to the city level.7 This applies to London, Manchester,Newcastle, Birmingham, Liverpool, Bradford, Sheffield, Leeds, Plymouth, Stoke, Hull, andOxford. A list of the PLUs in each city is provided in Table Census DataThe 1911 and 1921 British censuses were conducted on April 2, 1911 and June 19, 1921,respectively. Both enumerated only England and Wales; Scotland and Ireland (NorthernIreland did not exist until 1921 when Ireland achieved independence) each had wholly sep-arate censuses and are thus excluded from the analysis. The census variables used in thisproject are population (by age and gender), employment (by gender and industry type), andmigration data. Population and employment data are described here, while the migrationdata is described in Appendix B.5.The total population of England and Wales in 1911 was approximately 36,070,000, andin 1921 approximately 37,890,000. In the intervening decade the First World War was notalone in having a significant impact on population. It is estimated that approximately200,000 people died in England and Wales as a result of the Spanish Flu between 1918 and1920.8 This is significant, although still much smaller than the estimated number of Englishand Welsh soldiers killed in the war (approx. 620,000).9 If Spanish Flu deaths are correlated7Where metropolitan borders are provided, these are used. Otherwise, density and proximity to citycentre are used as gauges to determine whether or not a PLU belongs to a larger city structure.8Johnson & Mueller (2002), pg. 113.9Winter (1977), pg. 451.107with soldier deaths, the results would be biased. Even if they are not, they add noise to thedata. Chowell et al. (2008) provide evidence that death rates from the Spanish Flu weresignificantly higher in urban areas. It is reasonable to assume that military recruitment, andthus military deaths, would vary along urban and rural lines as well. To take this concerninto account, population density is added as a control in some specifications of the analysis.Summary statistics of total population, by year and geography, are provided in Table 3.3.Note the significant standard deviation for each entry: at each geographic level, populationtotals vary widely. Regressions weighted by population are thus included in the analysis.Total population by gender and age is used as well. Age totals are given in five year bands.Between 1911 and 1921, the age-gender composition of the English and Welsh populationchanged significantly, as can be clearly seen in Figure 3.2. For instance, between 1911 and1921, the ratio of males to females in the 15-40 year age range decreased by over 7%, from0.9103 to 0.8459. It is this large change that prompts this paper’s inquiry into how it mightaffect out-of-wedlock births, as well as how economic effects of war deaths might vary bygender.Concerning employment, 1911 data are drawn directly from census microdata, while1921 data are aggregations at the county level. These are given by gender and occupation,listing the total number of workers aged ten and above. As suggested in the GBHGIS,occupational categories are aggregated into four categories: Agriculture, Service, Staple,and Light. Employment rates, both total and by gender, are calculated, with summarystatistics given in Table 3.4.The economic situation in Britain in 1921 was poor. The average unemployment rate forthe year was 16.9%.10 It is difficult to compare this figure with the 1911 unemployment rateof 3%, as the method of calculation was significantly altered in 1920.11 However it is safe tosay that unemployment rose in the intervening years. The census employment statistics areconsistent with this, showing a fall in the national employment rate from 56.60% to 55.33%.10Denman & McDonald (1996), pg. 611ibid, pg. 8108The causes of high interwar unemployment, which lasted from the early 1920s well into the1930s, are disputed: conventional viewpoints are that it was primarily caused by monetarypolicy; however this is disputed by Cole & Ohanian (2001), who instead blame sectoral shocksand generous unemployment insurance. Given that the analysis below is conducted on thelocal level using differences, these changes should not bias the results unless these other causesare related to the treatment variable of interest: soldier death rates. It seems likely thatsoldier recruitment rates were linked to the sectorial composition of communities. Indeed,certain occupations, including rail workers, as well as some miners and agricultural workers,were exempt from conscription, while even among occupations not facing conscription therewere significant differences in recruiting.12 To account for the correlation between soldierdeath rates and sectoral composition coupled with the latter’s likely effect on economicchanges, sectoral controls are constructed and utilized in the analysis.It is worth noting that despite women taking a far more active role in the economyduring the war years, the female participation rate quickly fell back to pre-war levels afterthe conflict’s conclusion. The percentage of women fully employed rose from 24% in July1914 to 37% in November 1918.13 However, according to Hatton and Bailey (1988), “the FirstWorld War formal collective agreements which opened industrial jobs to women explicitlystated that this was to be for the duration of the War only.”14 It is unsurprising then thataccording to the census data, the national employment rate among females over the age often in 1911 was 31.32%, while in 1921 it was 30.85%. Despite the lack of change at thenational level, it is entirely possible that at the local level decreases in the working malepopulation due to death rates would open up the labour market for women and lead tohigher participation rates relative to other locations. This is investigated in later sections.12Dewey (1984) discusses occupational differences in recruitment in detail.13Hatton & Bailey (1988), pg. 16614ibid, pg. 1661093.2.3 Poor Law Union Pauperage ReportsThe measure for poverty used is pauperage rates. These were obtained via GBHGIS fromreports to parliament. Collected on a biannual basis, these reports tabulated the totalnumber of individuals receiving relief within each Poor Law Union in the months of Januaryand July, often by gender and type of relief. Only the January data is provided by GBHGIS.The 1911 and 1922 data are used, to align with the census and because the 1921 data areincomplete.Poor Law Unions (PLUs) were the primary source of assistance to the poor, and were inexistence until 1930. Two primary types of poor relief were provided: indoor and outdoor.The distinction lay in whether relief was contingent on residency in an institution run by thePLU, typically a workhouse. Those institutionalized were classified as “indoor”, while thosereceiving relief outside of institutions were “outdoor”. Typically, the able bodied seekingrelief were forced to enter workhouses, although there were numerous exceptions to this rule,including the need to care for dependents.15 As can be seen in the summary statistics listedin Table 3.5, indoor relief was much more common.In 1911 the UK began providing unemployment insurance outside of the PLU systemto members of certain industries. Initially, insurance was provided for a maximum periodof 15 weeks to approximately 15% of the workforce, mainly manual labourers.16 However,throughout the war unemployment insurance was gradually extended. By 1920 most pri-vately employed workers were insured, the main exceptions being agricultural and domesticworkers.17 Therefore, comparisons between 1911 and 1921 PLU pauperage rates will likelybe skewed by the extension of unemployment insurance. However, it is important to pointout the stigma surrounding Poor Law relief at the time. As stated in Whiteside (2015):Under Britain’s notoriously punitive Poor Laws, all able bodied males whosought public assistance were judged as unworthy – on the grounds that work15Fowler (2014), pg. 8616Cole & Ohanian (2002), pg. 1917ibid, pg. 20110was available for all who searched for it and who were willing to take no matterwhat job at no matter what price.18Thus, PLU relief was typically viewed as a last resort, both in 1911 and 1921, and as suchpauperage rates in both periods may be more accurately viewed as long-term unemploymentrates, as in 1911 only those who had exhausted all other options would likely seek it out,while in 1921 only who had maxed out their unemployment insurance would. Nonetheless,the fact that only certain industries were included in the 1911 unemployment insurancescheme is another reason to include occupation controls in the models analysed.It should be noted that in 1922 pauperage is only broken down by gender among thosereceiving outdoor relief. Thus in regressions comparing gender effects, the proportion ofoutdoor paupers to the entire population is used.The birth dataset is relatively straightforward. It contains total births both within andout of wedlock occurring each year in each LGD. Unlike previous datasets described, this isdrawn not from the census but from an annual registry of births. Births in years 1913 and1921 are used. Summary statistics of the within wedlock birth share are provided in Table3.6.3.3 Soldier Data, Instruments, and Historical ContextA major component of this project consisted of constructing the soldier death dataset. Twosources were used: “Soldiers Died in the Great War, 1914-1919”, a publication of British armydeaths; and a war graves roll published by the Admiralty containing deaths in the RoyalNavy and Royal Marines. Both list birthplace in the majority of cases. Using this data,estimates of the local death rate at various geographic levels are calculated, which are thenused in the Sections 4 and 5 to determine their effect on local poverty and unemployment.“Soldiers Died in the Great War, 1914-1919” is the principle source, published in 192118Whiteside (2015), pg. 3.111by the British government in 81 volumes containing the names of every non-commissionedsoldier killed in the British army during those years, according to regimental records. Whilethese original documents are still available at the UK National Archives, the informationwas digitised in 1998 by Naval and Military Press. Although there are undoubtedly someomissions or perhaps duplicates, there is reason to believe this dataset is very close to theuniverse of deaths in the British army. Winter (1977) estimates the total to be 673,375, onlyslightly off the number obtained here.Each record lists the soldier’s name, regiment, and death date, as well as their birthplacewhen given. In all, 531,324 records, 78.53% of the total, include a birthplace. For thepurposes of the analysis, the assumption is made that the probability of a soldier’s birthplacebeing omitted is independent of the birthplace. If this assumption holds, along with theassumption that the death total in the data is arbitrarily close to the true death total, thenfor each birthplace, the expected value of the true number of soldiers born in region r thatdied is the sum of soldiers recorded as born there divided by the proportion of records thatinclude a birthplace, in this case 0.7853. This is formally described in Equation 3.1:yˆr = E(yr) =∑nj=1 I(zj = r)s(3.1)where yr is the true death total of soldiers from region r, zj is the birthplace listed for recordj, where j ∈ {1, ..., n} where n is the total number of records, I(zj = r) is the indicatorfunction that is equal to 1 if zj = r and zero otherwise, and s is the proportion of records thatinclude a birthplace. Equation 3.1 is an estimate, and as such there will be measurementerror as a result of it whether the assumptions hold or not. This is addressed below.In addition to “Soldiers Died in the Great War, 1914-1919” – which only lists army deaths– records originally published by the British Admiralty listing Royal Navy and Royal Marinedeaths are also collected. Admittedly, less is known about the origins of these records relativeto the “Soldiers Died” collection. The National Archives, their custodian, catalogues them112among Admiralty records and simply describes them as “a war graves roll, 1914-1919.”19These records were also made available for public use online at Ancestry.com, where theywere scraped for use here. In total, 35,370 records were collected. Winter (1977) estimatesa total of 43,244 naval deaths,20 which suggests this is not as complete a reckoning of navaldeaths as “Soldiers Died” was of army deaths. However, given naval deaths made up a verysmall proportion of total deaths, this is judged to be not a major difficulty. In all, Winter(1976) estimates a total death toll of 722,782 among British forces,21 while our total comesto 711,925. Of the 35,370 naval records, 28,203 provide a birthplace, 79.74% of the total.This frequency is very close to that found in army records (78.53%), supporting the notionthat this failure to report was constant across settings, thus unrelated to birthplace. Forthe remainder of the analysis, naval and army death data is typically combined and referredto as “soldier deaths”, unless otherwise stated. Of the 711,925 deaths are recorded 559,527,or 78.59%, provide birthplace. Summary statistics of the basic death data are provided inTable 3.7.The process of sorting the birthplaces geographically to each administrative unit is out-lined in detail in Appendix B.4. This is done at the LGD, PLU, and Administrative Countylevels. Estimated death totals are then calculated for each region using Equation 3.1, anddeath rates using 1911 population totals. Summary statistics are provided in Table 3.8. Notethe relatively large variation at all levels. At least some of this is random, but some of thevariation is explainable. Regiments were typically tied to counties, and thus soldiers tendedto serve together with those from similar regions. Thus, if some regiments faced higher casu-alties than others, this would be reflected regionally as well. But even within counties, therewas significant variation in death rates. This can be seen in Figure 3.3, which plots deathrates at the PLU. This may partially be due to the existence within regiments of so called19National Archives’s catalogue ADM 242.20Winter (1977), pg. 45121Winter also attributes 6,166 deaths to the Royal Air Force, which was still in its infancy in WWI.Records concerning air force deaths were not available for use, but given the small number of deaths relativeto total military deaths this is likely not a major issue, assuming the birthplaces of air force casualties werenot concentrated in a few locations.113“Pals Battalions”, consisting of soldiers from the same town. These were later deemed illadvised, as if a “Pals Battalion” faced significant losses, whole towns could be devastated.22Additionally, it seems likely that recruitment was tied to local conditions at the start of thewar. For instance, as discussed above, occupation appears related to recruitment.It is worth emphasising what has been calculated here. The estimated death totals arethe total number of deaths by birth region, but to determine the death rates, it is assumedthat birth place was place of residence in 1911. We are seeking the effects war deaths hadon local communities, and therefore place of residence immediately before the war is thevariable of interest. Birthplace is a reasonable proxy for place of residence if migrationbetween communities is assumed to be minimal, but this is admittedly a strong assumption.Birthplace data is thus viewed as residence data with misclassification error. This error willnot be classical, not least because the probability of misclassification due to migration willalmost certainly be related to birthplace. However, measurement error methods seem thebest option for estimating regional death rates. Various methods are attempted, includingan instrumental variables approach and those specific to misclassification of a categoricalvariable.Concerning instrumental variables, the key is to find a measure that is related to the truedeath rate but unrelated to the error caused by migration, and, as is always the case forinstruments, unrelated to the second stage dependent variable. An ideal candidate would berecruitment rates, however these are unavailable: approximately two thirds of British WWIservice records were lost during WWII bombing raid. Instead, two other instruments areproposed. The first is based on the local age structure, while the second is a coastal dummy.It is important to note the age structure of recruits. When the war began, the minimumage requirement of recruits in the British forces was 18. Enlistment was voluntary until 1916,when conscription of all men between the ages of 18-41 was enforced.23 The upper age limitof conscription was later raised to 50 near the end of the war. However, a disproportionate22Chandler (2003), pg. 241-24223With the exception of certain occupations, as previously described. Simkins (2004), pg. 158114number of the dead were on the younger end of military age. Winter (1977) estimates that16.2% of soldiers age 19 and younger perished, 14.9% of those aged 20-24, 9.8% of thoseaged 35-39, and only 5.1% of those aged 40-44.24 As such, one would expect communitieswith higher rates of men in this age range to see higher death rates. Thus the proportionof men aged 10-19 in 1911 is included as an instrument. However, this proportion may berelated to the dependent variables explored in the analysis: poverty and employment rates.Places with a high proportion of men aged 10-19 in 1911 likely would have lower labourforce participation in 1911 than in 1921, as boys in 1911 would be men by 1921. To controlfor this, the change in the proportion of men aged 20-29 between 1911 and 1921 is includedin the regression. Admittedly, the change in the proportion for men aged 20-29 is likely amajor casual channel through which war deaths affect post-war outcomes, thus specificationswithout this instrument and control are also included.The second instrument utilized is a coastal dummy. The rationale behind this instrumentlies in the assumption that men in coastal communities were more likely to enlist in the navy,where the death rate was nearly half that of army.25 The death data does appear to bearthis out: looking at Administrative Counties, the Naval death rate26 is on average over67% higher among those bordering the coast, rising from 0.054% to 0.091%. These figuresare not surprising, given the Navy had considerable historical ties to coastal communities,maintained through the operation of the Royal Naval Reserve (RNR), established in the 19thcentury as a registry of trained seamen that could be drawn upon in times of war. Giventhe lower death rate in the Navy relative to the Army, it is reasonable to assume that theincreased likelihood a serviceman from a coastal community will be in the Navy translatesinto a lower total soldier death rate among coastal communities. The dummy used at theLGD and PLU levels is specified to equal one for all areas within 5 kilometers of the coast.2724Winter (1977), pg. 45125Approximately 6.8% versus 12.9%, according to Winter (1977), pg. 451.26Calculated as the number of recorded naval deaths by place of birth divided by the total 1911 population.27Many LGDs and PLU cover very small areas, and thus the 5 kilometer band is included so as not toexclude communities that lie close enough to the coast to take part in the coastal economy but do not liedirectly along it due to narrow communities between it.115At the county level, I am able to deal with the birth/migration problem directly withoutthe use of instruments. This is because migration data is available from the 1911 census atthe Admin. County level, which one can use to correct the migration misclassification. Thisprocess is described in detail in Appendix D.3.4 SpecificationsThe primary method used for analysis is a difference in difference approach, with the esti-mated soldier death rate acting as a continuous treatment variable. Numerous controls androbustness checks are included, but Equation 3.2 is the basic model:Yr,1921 − Yr,1911 = β0 + β1Dr + βXr + r (3.2)where Y is the dependent variable of interest – either Pauperage or Employment – while ris the region of interest, Dr is the estimated solider death rate of region r, and Xr is a setof controls. This model is equivalent to the following28:Yr,t = δr + λt + τt(β1Dr + βXr) + rt (3.3)where δr is a location fixed effect, λt is a time fixed effect, t ∈ {1911, 1921}, and τt is apostwar dummy equal to one when t = 1921 and zero otherwise.This approach picks up the level effect of each location, as well as the average trend acrosslocations. Thus, for a difference in difference model to be valid, a parallel trend assumptionmust hold. This means that in the absence of treatment (in this case soldier deaths), thechange in the dependent variable in each location must differ from the average change onlyby an error term unrelated to treatment. However, there is some reason to believe this willnot always be the case. As discussed above, due to sectoral shocks as well as welfare reform,28Equivalence between the first difference approach in Equation 3.2 and the fixed effects approach in 3 isonly assured in a two period model such as this one.116locations with different employment compositions may show different trends in pauperageand employment rates. As well, locations with different population densities may also showdifferent trends, given that the Spanish Flu affected urban areas more severely than ruralones. Therefore, population density and measures of labour composition are included ascontrols. It is important to note that it is not the difference of these variables’ valuesbetween 1911 and 1921 that are added as controls. Indeed, in general they changed verylittle. Rather, the 1911 values are used. This is because it is thought to be the level itselfthat affects the trend. For example, the density of most regions changed very little between1911 and 1921, but as discussed density did have a major effect on civilian death rates duringthe Spanish Flu epidemic, and thus the level itself may influence dependent variable change.For the models of change in pauperage rates and employment rates, two main specifi-cations are used. The first is that described in Equation 3.2, but without control variablesX, while in the second X consists of 1911 population density, as well as the proportionsof male and female workers employed in agriculture, staple industry, and services in 1911 ifavailable, 1921 if not.29To be clear, for change in total employment models, the dependent variable is Er,1921 −Er,1911, where employment rate Er,t is the total number employed in region r at time t dividedby the regional population at time t. For change in total pauperage models, the dependentvariable is Vr,1921 − Vr,1911, where pauperage rate Vr,t is the total number of able-bodiedindividuals receiving poor relief (both indoor and outdoor) in region r at time t divided bythe regional population at time t.In addition to analysing the effect of the soldier death rate on the total change in thedependent variables between 1911-1921, this paper also estimates whether or not the soldierdeath rate has stronger effects on males or females. To do this, Equation 3.2 is again used,29Light industry, the fourth and final category, is left out due to the fact that very near to 100% of workerswork in one of these four sectors, and thus inclusion would result in collinearity.117but with the following on the left hand side as the dependent variable:(Yr,m,1921 − Yr,m,1911)− (Yr,f,1921 − Yr,f,1911)where Yr,m,t is either the rate of employment or pauperage in region r for males at time tand similarly Yr,f,t is either the rate of employment or pauperage in region r for females attime t. Thus, we are measuring the difference in the change in male and female rates.Also, as previously discussed, instrumental variable methods are used in some models.To be precise, all Pauperage regressions utilize 2SLS unless otherwise stated, with the firststage estimating the death rate and the excluded instruments being a coastal dummy andthe age structure measure defined previously. At the county level, the available migrationdata allows the measurement error to be dealt with directly, without the need of instruments.Concerning the out-of-wedlock birth rate, the models constructed are somewhat different,as it is the direct effect of the sex ratio among those of reproductive age on the proportionof births within wedlock that we are interested in, not the effect of solider deaths. Thusthe death variable is not included, forgoing the need to correct for measurement error. Itis replaced by the change in the local ratio of men to women aged 15-39 between 1911 and1921. The model is therefore:Lr,1921 − Lr,1911 = β0 + β1(Rr,1921 −Rr,1911) + βXr + r (3.4)where Rr,t is the ratio of men to women at time t in region r and Lr,t is the proportion oftotal births in region r and year t that were within wedlock.Unless otherwise noted, regressions are, unless otherwise noted, weighting by total 1921population. However, there is concern that with the use of weights, a few observations mightoverwhelm the rest of the data due to the high weights given them. At the PLU level, Londonhas well over 100 times the population of the average unit, while Manchester, the secondlargest, still is around 40 times larger than the average and much more than double the118third. To address this concern, regressions excluding London and Manchester are examinedas well.3.5 Results3.5.1 PovertyTable 3.9 shows the effect of the soldier death rate on the change in the total able-bodiedpauperage rate, while Table 3.10 shows the effect on the difference between the changes inmale and female out-door able-bodied pauperage rates. Each table lists the results of fivespecifications, described in detail in the preceding section, testing sensitivity to the exclusionof London and Manchester, the exclusion of weights, and the exclusion of the controls. Withthe exception of column 1 in both tables, all specifications use 2SLS, with a coastal dummyand the proportion of men aged 10-19 in 1911 used as the excluded instruments. The firststage results can be viewed in Table 3.11.Considering the first stage results, the sign on the coastal dummy is always negativeas suspected, indicating a lower death rate in coastal communities due to the comparativesafety of the Navy. The sign on the proportion of males aged 10-20 in 1911 is always positive,also as suspected, as this age range was more likely to perish in the War. In general bothvariables appear strongly significant. Turning to Tables 3.9 and 3.10, we see that the F-statistic for the instruments is always above 10, suggesting that while weak instrumentscannot be fully ruled out, it is not a pressing concern. Hansen’s test of overidentificationstatistics does give a little cause for worry about the instruments validity: while most of thetime the null hypothesis is far from being rejected, in column 4 in Table 10 it is rejected with95% confidence. However, given 10 IV models were tested, it is within the realm of reasonto see one false rejections.Table 3.9 provides strong evidence that the soldier death rate is negatively related togrowth in the total rate of able-bodied paupers. In the preferred specification, shown in119column 3 of Table 3.9, on average a 1 pp increase in the soldier death rate was associatedto an approximate 3.4 pp fall in the proportion of the population receiving able-bodied poorrelief. Given that the standard deviation of soldier death rates at the PLU level was around0.77 pp, this implies that an increase in the soldier death rate by one standard deviation isassociation with a 2.6 pp fall. These results support the Malthusian notion that a higherdeath rate improved the material prospects of those left behind.Interestingly, Table 3.10 provides very strong evidence that soldier deaths caused maleoutdoor pauperage rates to fall more than female outdoor pauperage rates (or rise less asthe case may be). The preferred specification suggests that on average a standard deviationincrease in soldier death rates decreased the outdoor able-bodied pauperage rate by 0.43pp more among males than female. This fits well with the story that women, due to socialcustoms, were largely shut out of the labour market and thus were unable to benefit fromthe increase in capital and land per capita caused by the increased death rate to the sameextent men were. Further, it seems likely that war induced widowhood would have led manywomen to seek alms.3.5.2 EmploymentTable 3.12 shows the estimated effect of the soldier death rate on the total employmentrate and Table 3.13 the effect on the difference between male and female employment ratechanges. Each table lists the results of six specifications testing the robustness of the resultsto the exclusion of controls, weights, and London. These specifications do not use 2SLS, butrather rely on regression calibration and migration adjustment to correct for measurementerror (see Appendix B.5 for details).In Table 3.12, the coefficient on the soldier death rate is positive in all specifications,though not significant when population weights are used. This positive relationship suggeststhat a higher soldier death rate may have resulted in higher employment rates. Thus, whilethe evidence is not conclusive, it again matches with the theory that a high solider death120rate would primarily affect post-war economic outcomes through a negative labour supplyshock, resulting in higher employment rates.Examining Table 3.13, the coefficient on soldier death rates is again only significant inthe unweighted cases. In those cases it is negative, suggesting that male employment rategrowth was lower than female employment rate growth in places with a higher death rate.While at first glance this seems to contradict the story told by the pauperage effects, theycan be reconciled if one accepts that the male and female employment rates were movingfor different reasons: the male rate due to decreased unemployment, the female rate due toincreased participation. At the time, nearly all men were in the labour force. Thus, anyincrease in the male employment rate was likely due to a decrease in the unemploymentrate. Conversely, among women participation in the labour force was comparatively rare: aspreviously noted, only 31% of women were employed in 1911, compared to well over 80% ofmen. Thus, it seems likely that the increase in the female employment rate was caused bywomen joining the labour market. This fits with the narrative of female dependants beingforced to enter the labour market due to the loss of the breadwinner in the war. This wouldbe more common in areas with a higher death rate.3.5.3 Out-of-Wedlock BirthsTable 3.14 examines the change in the within wedlock birth share brought on by changes inthe ratio of men to women aged 15-39 between 1913 and 1920. The specifications are verysimilar to those seen already, with the notable exception that gender specific occupationcontrols are added, as it was thought that the decision to conceive would likely be heavilyinfluenced by the mother’s employment situation. However, robustness checks are providedin Table 3.15 using non-gender specific occupation controls, as used in previous sections.In all models considered, the point estimates on sex ratio are negative. While theseresults are not significant in the unweighted regressions, they are significant at the 90% levelin all weighted specifications. It should be noted that while significant, the effect is small:121using the preferred specification given in column 4 of Table 3.14, increasing the change in sexratio by one standard deviation (0.14) is associated with a fall in the within wedlock shareby a fifth of a percentage point, or 6.8% of a standard deviation. Nonetheless, these resultssuggest that a decrease in the male to female ratio is related to more out of wedlock births.This supports the findings of others, and bolstering the theory that when men are givenmore bargaining power in the marriage market, they on average will pursue an evolutionarystrategy of picking multiple mates while passing off the costs of childrearing to single mothers.3.6 ConclusionWhile the study of war is likely as old as mankind, little research has been done concerninghow conflict continues to affect economic outcomes even after the shooting has stopped.This paper uses a unique dataset of British First World War soldier deaths to examinethe impact soldier death rates had on employment and poverty rates, exploiting regionalvariation in death rates. After controlling for measurement error and using a difference indifference estimator, I find strong evidence that an increase in the soldier death rate loweredpoverty rates among those remaining after the war, particularly among men. There is alsoweak evidence that higher soldier death rates increased post-war employment rates, perhapsmore among women. Both these findings support the narrative of surviving men enjoyingincreased productivity and/or bargaining power due to increases in capital and land percapita and decreases in the labour supply caused by the high war death rate, while survivingwomen received less of these benefits due restricted access to the labour market, but maynonetheless have been forced to seek out employment due to the loss of a breadwinner. Ialso, using the large swings in the sex ratio caused by the war, find that a decrease in theratio of men to women of childbearing age is associated with an increase in out-of- wedlockbirths. This is consistent with the literature and supports the theory that men find it easierto attract partners and shirk investment in child rearing when the sex ratio is low.122While the results of this paper are of historical interest, I believe they also have contempo-rary value. Given the continued presence of armed conflict around the globe, its aftereffectsremain a depressingly relevant concern.123Tables and FiguresTable 3.1: Original Data Aggregation LevelData Type Original Aggregation LevelSoldier Deaths IndividualEmployment Admin. CountyPauperage Totals PLUPopulation totals Parish, LGD, PLU, Admin. CountyPopulation (by age and sex) LGD, PLU (only 1911), Admin. CountyBirth totals LGD (1911)Migration Admin. CountyTable 3.2: Description of PLU Aggregation into City Level UnitsCity Included PLUsLondon St. George in the East, Whitechapel, Mile End Old Town, Bethnal Green,Shoreditch, Southwark, Holborn, Westminister, Paddington, St. Giles, Is-lington, Stepney, Chelsea, St. Marylebone, St. Pancras, Kensington, St.Olave (Bermondsey), Lambeth, Hackney, Fulham, Poplar, St. George HanoverSquare, Camberwell, Greenwich, Wandsworth, Stand, Hampstead, West Ham,Willesden, London City, Woolwich, Lewisham, Brentford, Richmond Surrey,Edmonton, Croydon, Kingston, Barnet, Hendon, RomfordManchester Manchester, Salford, Chrolton, Prestwich, Oldham, Stockport, Bolton, Bartonupon Irwell, Ashton under Lyne, Bury, Wigan, Rochdale, LeighLiverpool Liverpool, Toxteth Park, West Derby, PrescotLeeds Leeds, Holbeck, Bramley, HunsletNewcastle Newcastle upon Tyne, South ShieldsBirmingham Birmingham, Aston, Kings NortonBradford Bradford, North BierleySheffield Sheffield, Ecclesall BierlowPlymouth Plymouth, East Stonehouse, DevonportStoke Stoke upon Trent, WolstantonHull Hull, SculcoatesOxford Oxford, Headington124Table 3.3: Population Summary StatisticsYear &Geographic LevelMeanStandardDevia-tionMinimum Maximum ObservationsLGD, 1911 19,593 45,166 12 746,421 1841LGD, 1921 20,737 50,323 5 919,444 1827PLU/City, 1911 63,731 318,442 2,396 692,9292 565PLU/City, 1921 66,845 325,304 2,519.71 7,060,177 565Admin County, 1911 680,575 1,008,757 20,346 4,767,832 53Admin County, 1921 714,843 1,037,387 18,376 4,927,484 531 The reason this is not an integer lies in its construction, described in Appendix B.Table 3.4: Employment Rate Summary StatisticsRateYear &GeographicLevelMeanStandardDevia-tionMinimum Maximum ObservationsTotal1Admin. County,19110.5527 0.0214 0.5066 0.6244 52TotalAdmin. County,19210.5321 0.0254 0.4791 0.6064 53MaleAdmin. County,19110.8279 0.0181 0.7900 0.8626 53MaleAdmin. County,19210.8178 0.0197 0.7718 0.8514 53Female1Admin. County,19110.2907 0.0492 0.1580 0.4086 52FemaleAdmin. County,19210.2729 0.0490 0.1673 0.3922 531 Female 1911 labour statistics for Somersetshire are unavailable.125Table 3.5: Poor Law Union Pauperage Rate Summary StatisticsVariable &YearMeanStandardDevia-tionMinimum Maximum ObservationsTotal Rate ofPauperage, 19110.0182 0.0055 0.0058 0.0439 565Total Rate ofPauperage, 19210.0264 0.0186 0.0029 0.1627 565Rate of OutdoorPauperageamongAble-BodiedWomen, 19110.0047 0.0022 0.0009 0.0181 565Rate of OutdoorPauperageamongAble-BodiedWomen, 19210.0042 0.0102 0 0.0876 565Rate of OutdoorPauperageamongAble-BodiedMen, 19110.0011 0.0016 0 0.0125 565Rate of OutdoorPauperageamongAble-BodiedMen, 19210.0049 0.0110 0 0.0852 565126Table 3.6: Within Wedlock Birth Share by LGDYear Mean Standard Deviation Minimum Maximum Observations1911 0.9466 0.0279 0.7654 1 18251921 0.9516 0.0279 0.7500 1 1837Table 3.7: Death Records Summary StatisticsDataset RecordsRecordsProvidingBirthplaceUniqueBirthplacesListed“Soldiers Died” (Army) 675,555 531,324 82,012“War Graves Roll” (Navy) 35,370 28,203 7521Total 711,925 559,527 87,331Table 3.8: Estimated Death Rate Summary StatisticsGeography MeanStandardDeviationMinimum Maximum ObservationsLGD 0.0151 0.0112 0.0002 0.24681 1841PLU 0.0197 0.0077 0.0050 0.0901 565Admin. County 0.0176 0.0044 0.0091 0.0292 53Admin. County(estimated usingmigration data)0.0378 0.0108 0.0153 0.0612 531 This observation (the urban district of Norden) appears to be an outlier: the next highestdeath rate is less than half it, and there is no reason a priori to expect such a high rate,given that its ratio of fighting age males to the rest of its population is normal. Thereforeit is excluded from the analysis in some models.127Table 3.9: Change in Total Able-Bodied Pauperage Rate, 1911-1921(1) (2) (3) (4) (5)VARIABLESDeath Rate -1.149*** -2.472** -3.432** -3.654*** -1.033**(0.284) (1.007) (1.441) (1.141) (0.516)∆(% of Males 20-29) 0.0659 -0.0112 0.0343 0.0461 0.0375(0.111) (0.101) (0.0853) (0.0803) (0.0390)Agriculture -0.0465** -0.0564** -0.0287***(0.0232) (0.0283) (0.0108)Staple -0.0642* -0.0726** -0.0062(0.0366) (0.0338) (0.0190)Service -0.0931** -0.112*** -0.0366**(0.0398) (0.0386) (0.0180)Density 0.719 0.131 2.320**(1.077) (1.509) (1.075)Observations 488 489 489 487 489IV NO YES YES YES YESWeighted YES YES YES YES NOLondon & Manchester YES YES YES NO YESClustered at county level YES YES YES YES YES# of Clusters 53 53 53 52 53F stat excluded instuments 12 11.20 12.09 10.83Hansen J stat p-value 0.795 0.569 0.515 0.560Robust standard errors in parentheses*** p<0.01, ** p<0.05, * p<0.1128Table 3.10: Difference in Growth of Outdoor Able-Bodied Pauperage Rates, Male Growth - Female Growth(1) (2) (3) (4) (5)VARIABLESDeath Rate -0.147*** -0.381** -0.570*** -0.624*** -0.266***(0.0371) (0.152) (0.179) (0.156) (0.0884)∆(% of Males 20-29) -0.0267* -0.0398** -0.0267* -0.0247* -0.0018(0.0134) (0.0160) (0.0139) (0.0143) (0.0059)Agriculture -0.0050* -0.0067** -0.0042**(0.0030) (0.0032) (0.0019)Staple -0.0147*** -0.0161*** -0.0059**(0.0040) (0.0037) (0.0027)Service -0.0176*** -0.0209*** -0.0010***(0.0045) (0.0044) (0.0033)Density 0.163 0.0565 0.224(0.115) (0.176) (0.178)Observations 489 489 489 487 489IV NO YES YES YES YESWeighted YES YES YES YES NOLondon & Manchester YES YES YES NO YESClustered at county level YES YES YES YES YESCounty Fixed Effects NO NO NO NO NO# of Clusters 53 53 53 52 53F stat excluded instuments 12.00 11.20 12.09 10.83Hansen J stat p-value 0.418 0.0987 0.0401 0.241Robust standard errors in parentheses*** p<0.01, ** p<0.05, * p<0.1129Table 3.11: First Stage of Tables 3.9 and 3.10(2) (3) (4) (5)VARIABLESWater Dummy -0.0025*** -0.0028*** -0.0032*** -0.0035***(0.0008) (0.0007) (0.0008) (0.0009)% of Males 10-19 in 1911 0.104*** 0.0560** 0.0512** 0.0204(0.0306) (0.0218) (0.0238) (0.0166)∆(% of Males 20-29) -0.0412 -0.0118 -0.0126 0.0239(0.0254) (0.0188) (0.0193) (0.0245)Agriculture 0.0014 0.0022 -0.0017(0.0045) (0.0043) (0.0047)Staple -0.0196*** -0.0191*** -0.0222***(0.0049) (0.0046) (0.0052)Service -0.0198*** -0.0179*** -0.0200***(0.0038) (0.0034) (0.0044)Density -0.441** -0.304 -0.467*(0.177) (0.244) (0.250)Observations 489 489 487 489Weighted YES YES YES NOLondon and Manchester YES YES NO YESClustered at county level YES YES YES YESCounty Fixed Effects NO NO NO NO# of Clusters 53 53 52 53Robust standard errors in parentheses*** p<0.01, ** p<0.05, * p<0.1130Table 3.12: County Employment Rate Change, 1911-1921(1) (2) (3) (4) (5) (6)VARIABLESDeath Rate (Migration Adjusted) 0.188 0.203 0.717*** 0.0793 0.0909 0.492**(0.238) (0.241) (0.162) (0.336) (0.307) (0.202)Density -0.632 -1.715 -0.372(0.457) (8.585) (0.467)Agriculture -0.147*** -0.151*** -0.117***(0.0430) (0.0428) (0.0414)Service -0.153*** -0.0152** -0.0929*(0.0559) (0.0579) (0.0530)Staple -0.108** -0.107** -0.0478(0.0497) (0.0494) (0.0489)Observations 52 51 52 52 51 52Weighted YES YES NO YES YES NOLondon YES NO YES YES NO YESRobust standard errors in parentheses*** p<0.01, ** p<0.05, * p<0.1131Table 3.13: Difference in growth rates of Employment (Male Growth - Female Growth)(1) (2) (3) (4) (5) (6)VARIABLESDeath Rate (Migration Adjusted) 0.0173 0.00778 -1.568*** -0.216 -0.383 -1.747***(0.238) (0.241) (0.162) (0.336) (0.307) (0.202)Density 0.384 1.604 0.619(0.674) (1.428) (0.908)Agriculture 0.0649 0.110 0.0441(0.0728) (0.0709) (0.0740)Service -0.0114 -0.0342 -0.111(0.0944) (0.0942) (0.0915)Staple -0.0334 -0.0419 -0.137*(0.0815) (0.0760) (0.0813)Observations 52 51 52 52 51 52Weighted YES YES NO YES YES NOLondon YES NO YES YES NO YESRobust standard errors in parentheses*** p<0.01, ** p<0.05, * p<0.1132Table 3.14: Within Wedlock Birth Rate, Using Gender Specific Occupation Data(1) (2) (3) (4) (5) (6)VARIABLES∆(Sex ratio for ages 15-39) -0.0119** -0.0104** -0.00832 -0.0108** -0.00889* -0.00843(0.00539) (0.00456) (0.00577) (0.00517) (0.00469) (0.00615)Density 0.0150 0.148** 0.114(0.0575) (0.0582) (0.138)Agriculture - Male 0.0191** 0.0243*** 0.0137(0.00881) (0.00813) (0.0141)Service - Male 0.0162* 0.0205** 0.00334(0.00939) (0.00888) (0.0166)Staple - Male 0.0140** 0.0161** 0.00380(0.00673) (0.00677) (0.0122)Agriculture - Female 0.0118 0.0102 0.00578(0.0151) (0.0146) (0.0189)Service - Female -0.000319 0.000346 0.00802(0.00541) (0.00441) (0.00932)Staple - Female 0.00717* 0.00505 0.0150*(0.00387) (0.00398) (0.00850)Observations 1,797 1,797 1,797 1,792 1,792 1,792Weighted YES YES NO YES YES NOClustered at county level YES YES YES YES YES YESCounty Fixed Effects NO YES NO NO YES NO# of Clusters 55 55 55 55 55 55Robust standard errors in parentheses*** p<0.01, ** p<0.05, * p<0.1133Table 3.15: Within Wedlock Birth Rate, Using Total Occupation Data(1) (2) (3)VARIABLES∆(Sex ratio for ages 15-39) -0.00940* -0.00812* -0.00760(0.00506) (0.00454) (0.00617)Density 0.0185 0.145** 0.0478(0.0451) (0.0584) (0.141)Agriculture 0.0196*** 0.0265*** 0.0177**(0.00562) (0.00561) (0.00862)Service 0.0131** 0.0197*** 0.00886(0.00607) (0.00663) (0.0116)Staple 0.0161*** 0.0184*** 0.0116(0.00490) (0.00520) (0.00872)Observations 1,792 1,792 1,792Weighted YES YES NOClustered at county level YES YES YESCounty Fixed Effects NO YES NO# of Clusters 55 55 55Robust standard errors in parentheses*** p<0.01, ** p<0.05, * p<0.1134Figure 3.1: Administrative Geographical Hierarchy135Figure 3.2: Changing Sex Ratio136Figure 3.3: Poor Law Union Soldier Deaths to Population Ratio137BibliographyAbramitzky, R., L. 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Philosophical Transac-tions of the Royal Society A: Mathematical, Physical and Engineering Sciences 371 (1986),20110568.147Appendix AAppendix to Chapter 1A.1 Childhood vs Adult Parish of ResidenceIf access to public schooling during childhood is truly driving results, then it should be thecase that childhood parish of residence is what matters, not adult residence. When using thecomplete, unlinked censuses in Sections 1.5 and 1.6, I am unable to view childhood parish ofresidence, and address this issue by dropping individuals residing in a county other than theone of their birth, as these individuals had likely moved since childhood. Using the censuslinkages, however, I directly observe childhood place of residence, and so can keep thesemovers. To show that dropping them in the previous sections had little effect on my results,I rerun the regression displayed in Column (3) of Table 1.6, but using the linked samples.The result is shown in Column (1) of Table A.1.1.As a placebo test, I determine how many years an individual would have been treatedhad they resided in their adult parish of residence during childhood. In Column (2) of TableA.1.1, I show the results using this adult residence treatment variable. As expected, theresults are insignificant and close to zero. Finally, in Column (3) of Table 1.6, I run a horserace regression, including the treatment variables associated with both childhood and adultparish of residence. The results again strongly suggest that it is childhood access to publicschools that is driving results.148Table A.1.1: Childhood vs. Current Parish of Residence(1) (2) (3)Literacy Required Literacy Required Literacy RequiredYears of Treatment (Childhood) 0.000948** 0.00131**(0.000481) (0.000638)Years of Treatment (Current) -0.000251 -0.00102*(0.000561) (0.000611)Observations 2,042,790 1,491,469 1,433,523Childhood Arrival-Age Fixed Effects X XChildhood Arrival Trend Effects X XChildhood Parish Fixed Effects X XCurrent Arrival Trend Effects X XCurrent Arrival-Age Fixed Effects X XCurrent Parish Fixed Effects X XAge Trend Effects X X XRobust standard errors in parentheses. *** p<0.01, ** p<0.05, * p<0.1149A.2 Effect of Boards on School Supply and AttendanceIn this section I verify the positive effects school boards had on school supply and attendance.These ‘stage zero’ results are included as motivation for using the school board reform as aproxy for improved education.Before proceeding, an important note on the data used. The 1888 Education Report,from which parish supply and attendance figures are drawn, provides data at the school level.Where there is ambiguity about what parish a school is located in, the ambiguous schoolsare dropped from school supply and attendance regressions. These dropped schools accountfor around 40% of the total. However, there is no reason to believe a systematic differenceexists between dropped and kept schools, as shown by a comparison of their observables inTable A.2.1.A simple difference-in-differences (DID) specification, shown in Equation A.1, is usedto estimate the impact of school boards on school supply.1 Pre-reform school space andpopulation are drawn from the 1871 education survey, while post-reform figures are from the1888 education report.School SupplyPopulation pt= ωp + γ1t+ γ2(Sp ∗ t) + (Zp ∗ t)β + pt (A.1)where t is a year dummy (1 if 1888, 0 if 1871), ωp is a parish fixed effect, Sp is a schoolboard fixed effect (1 if parish received school board, 0 otherwise), and Zp is a vector of pre-treatment parish controls (interacted with time to allow trend to vary on them). The resultsare shown in Table A.2.2. Columns (1) and (2) show the results of the DID with and withoutpre-treatment parish controls, assuming that parishes unmatched to a school in 1888 hadzero school supply in the latter period. Columns (3) and (4) drop these unmatched parishes.As can be seen, the treatment term (Board∗Time dummy) is significant throughout. Further,the effect is sizeable, given the target ratio of 1/6 (16.67%): depending on the specification,1A parish’s school supply was at the time defined as (total school square footage)/10.150the coefficients suggest a 3.23-5.5 pp increase in the school supply ratio due to school boards.In 1871 the average treated parish had a school supply ratio of 9.2%, implying that schoolboards increased school supply ratio by 35-60% in these parishes.While the DID approach in theory controls for constant parish-level unobservables, itrelies on the parallel trends assumption. That is to say, we must assume that, in the absenceof the reform, both parishes that received the reform and those that did not would haveexperienced on average the same growth in the school space-population ratio, given the pre-treatment controls discussed. Unfortunately, parish-level school supply prior to 1871 is notavailable, and thus testing for parallel trends prior to this period is impossible. Admittedly,one could think of reasons why the assumption might not hold. As described in Section 3,parishes had some control over whether or not they received a board. Thus, if only thoseparishes that were most eager to expand their school supply received boards, the paralleltrends assumption would likely be violated and these results could not be interpreted causally.If it were the case that boards primarily went to eager parishes, one would expect most tohave been formed within a year or two of the passage of the reform, for as previously statedany parish could voluntarily receive a school board whenever they desired. However, as canbe seen in Figure 1.1, this was not the case; parishes that ended up with boards typicallydid not form them until several years after the reform was passed. Thus, it seems likely thatthe opposite was true: parishes that took it upon themselves to supply school space throughprivate means in the years immediately following the reform were not obliged to instituteboards, and thus only those parishes least eager to expand school supply ended up receivingboards. If this is the case, the results shown here strongly support the notion that schoolboards caused school supply to increase, refuting the claims made by West (1970, 1975) thatthe boards actually held back school growth.Attendance figures also suggest boards had a positive impact on education. As attendancefigures are only available for 1888, using DID is not possible. However, simple regressionswith controls, shown in Table A.2.3, suggest boards were correlated with higher school151attendance per capita. Not surprisingly, school supply per capita is highly correlated withattendance rates, but even controlling for this, boards appear to have a strong positiveimpact. Given the inability to control for parish unobservables, these results should obviouslybe interpreted with caution. However, they line up with the fact that boards had moreauthority to enforce school attendance and also subsidized fees. As well, the likely increasein school quality brought by boards may have made attendance more attractive to parentsand students.Whether or not these results can be interpreted causally, they demonstrate that therewas an improvement in the provision of education in parishes that received boards relativeto those that did not. Indeed, these results likely tell only part of the story, as the evidenceof superior instruction given at board schools, discussed in Section 3, is not captured here.However, they motivate the use of the school board reform as a proxy for improved education.Table A.2.1: Merged vs Unmerged SchoolsMerged Unmerged DifferenceSchool Space 190.089 174.972 15.117(6.160) (5.489) (8.608)Attendance 292.694 277.176 15.518(8.332) (7.983) (11.909)Observations 7615 5536Standard errors in parentheses.152Table A.2.2: School Supply Per Capita Diff-in-Diff, 1871 and 1888All Parishes Matched Parishes Only(1) (2) (3) (4)School Supply School Supply School Supply School Supplyto Pop Ratio to Pop Ratio to Pop Ratio to Pop Ratio(Board)*(1888 Dummy) 0.0550*** 0.0355*** 0.0461*** 0.0323***(0.0082) (0.0081) (0.0112) (0.0112)1888 Dummy 0.0352*** 0.128*** 0.112*** 0.192***(0.0035) (0.0217) (0.0088) (0.0300)Observations 22,821 22,558 14,276 14,276Controls NO YES NO YESFixed Effects PARISH PARISH PARISH PARISHRobust standard errors in parentheses. Controls (all interacted with a 1888 dummy): 1871 parish population; distancefrom London; distance from London squared; 1871 school supply per capita; 1871 school supply per capita squared; 1851Church of England attendees per capita 1851 Catholic attendees per capita; 1851 other religious service attendees percapita. *** p<0.01, ** p<0.05, * p<0.1Table A.2.3: 1888 School Attendance RateSchool Attendance School AttendanceVARIABLES to Pop Ratio to Pop RatioBoard Dummy 0.0222*** 0.0210***(0.00290) (0.00257)Observations 7,156 7,156Controls NO YESRobust standard errors in parentheses. Controls: 1871 parish population; distancefrom London; distance from London squared; 1871 school supply per capita; 1851Church of England attendees per capita 1851 Catholic attendees per capita; 1851other religious service attendees per capita. *** p<0.01, ** p<0.05, * p<0.1153A.3 Appendix: Reports to ParliamentFigure A.3.1: 1871 Survey ReportNote: Sample pages from the report to parliament concerning the 1871 survey of parish school supply. All 14,094 parisheswithin England and Wales that lay outside of municipal boroughs are listed. Note that columns headings under “Number ofschools: In operation” are somewhat misleading. “Public” in this case refers to private institutions that were recipients of publicgrants. At the time of the survey, no publicly administered schools were yet in operation. “Private” refers to private non-profitinstitutions not receiving public grants, and “Adventure” refers to for-profit institutions. Source: “Return of Civil Parishes inEngland and Wales under Education Act, of Population, Rateable Value, Number of Schools and Scholars in Attendance”, UKparliamentary paper, 1871, Vol. 55, 201.154Figure A.3.2: 1879 School BoardsNote: Sample page from the list of school boards provided by the Board of Education to Parliament in 1879. Source:“Report of the Committee of Council on Education (England and Wales); with appendix. 1878-79”, UK parliamentary paper,1878-79, Vol. 23, paper C.2342.155Figure A.3.3: 1888 SchoolsNote: Sample page from the list provided by the Board of Education to Parliament of schools, both board and private, receivingpublic grants 1888. Board (public) schools are italicized. Source: “Report of the Committee of Council on Education (Englandand Wales); with appendix 1888-89.” UK parliamentary paper, 1889. Vol. 29, paper C.5804.156A.4 Appendix: Regression Kink ModelIn the following description of the Regression Kink model, I rely heavily on the framework laidout in Dong (2018). Let Y = y(T,R,W ) represent the proportion of jobs within a parishthat make use of literacy, where T is a binary treatment variable representing whetheror not a parish received a school board, and R represents pre-reform school supply percapita. Importantly, treatment status T may be correlated with the error term W . LetYt = y(t, R,W ) for t = 0, 1, so Y1 and Y0 represent a parish’s potential outcomes giventreatment or not, respectively. Let treatment T = 1{P (R)−U≥0}, where U is normalized suchthat U ∼ Unif(0, 1), so P (R) is the probability of treatment given R. For notationalsimplicity, let F+ = limr↓r0F (r) and F− = limr↑r0F (r). Further, let F′+ = limr↓r0∂F (r)∂randF ′− = limr↑r0∂F (r)∂r. Then the identification rests on the following assumptions:Assumption 1 - There exists a point R = r0 such that P′+ 6= P ′−.Assumption 2 - P (r) is continuously differentiable everywhere near r0 except at r0, and iscontinuous at r0.Assumption 3 - y(t, R,W ), for t = 0, 1, is continuously differentiable w.r.t. R everywherenear and including r0.Assumption 4 - The conditional density fR,U |W=w is continuously differentiable w.r.t. Reverywhere near and including r0Let G(r) = E[Y |R = r]. If these assumptions hold, then:G′+ −G′−P ′+ − P ′−= E[Y1−Y0|U = P (r0), R = r0] =∫[y(1, r0, w)−y(0, r0, w)]fR,U |W=w(r0, P (r0))fR,U(r0, P (r0))dFW (w) = τ(A.2)An intuitive proof is provided below. For a more detailed derivation, see Card et al. (2015).157Proof:G(r) = E[Y |R = r] = E[Y1 ∗ T |R = r] + E[Y0 ∗ (1− T )|R = r]= E[(Y1 − Y0) ∗ T |R = r] + E[Y0|R = r]= E[(Y1 − Y0) ∗ 1{U≤P (r)}|R = r] + E[Y0|R = r]Thus, by Assumptions 2 and 3, for r in neighbourhood of r0 but not equal to r0,∂∂rG(r) = P ′(r)E[(Y1 − Y0)|U = P (r), R = r]+∫ P (r)0∂∂rE[(Y1 − Y0)|U = u,R = r]du+ ∂∂rE[Y0]|R = r]Then,G′+ −G′− = P ′+E[(Y1 − Y0)|U = P+, R = r0]− P ′−E[(Y1 − Y0)|U = P−, R = r0]+∫ P+0∂∂rE[(Y1 − Y0)|U = u,R = r]du−∫ P−0∂∂rE[(Y1 − Y0)|U = u,R = r]duBut by Assumption 2, P+ = P− = P (r0), soG′+ −G′−P ′+ − P ′−= E[Y1 − Y0|U = P (r0), R = r0] = τ (A.3)This represents the average treatment effect at r0 among those of type U = P (r0).These are the compliers: the parishes that would not be treated to the right of the kink(T = 1{P+−U≥0} = 0) but would be treated to the left (T = 1{P−−U≥0} = 1). In the presenceof heterogeneous treatment effects, this is somewhat restrictive. However, as pointed out inLee & Lemieux (2010) in the RD context, it is less restrictive than one might assume, asthe effect may be viewed as a weighted average of treatment effects at the kink across theentire population of unobservable types W . This is made clear in Card et al. (2015), which158demonstrates that one may also write Equation A.3 asτ =∫[y(1, r0, w)− y(0, r0, w)]fR,U |W=w(r0, P (r0))fR,U(r0, P (r0))dFW (w) (A.4)where the term∫[y(1, r0, w)− y(0, r0, w)] represents the average treatment effect at the kinkacross all unobservable types W , which in turn is weighted by the probability a complier isof type W = w (represented by the termfR,U|W=w(r0,P (r0))fR,U (r0,P (r0))).A.5 Appendix: Running Variable Density TestsI assess the smoothness of fR(r) using two tests: the McCrary test, and a test of differen-tiability at a point suggested by Card et al. (2012).The McCrary test, common in the Regression Discontinuity literature, tests the conti-nuity of the running variable at the cutoff by binning observations of the running variable,smoothing bin heights using local linear regression within some bandwidth, then comparingthe heights of the bins to the left and right of the cutoff. For the test, I use the CCT optimalbandwidth calculated for the RK, h = 0.0796609. McCrary (2006) suggests that the test isrobust to varying bin width b so long as h/b > 10. Nonetheless, I conduct the test twiceusing two different bin widths, b = 0.003 and b = 0.006. I report the results in the topwindow of Table A.5.1. For both bandwidths, the test fails to reject the null that fR(r) iscontinuous at the cutoff.Card et al. (2012) suggests a test for the differentiability of the running variable atthe cutoff. Similar to the McCrary test, this test bins observations of the running variable,then regresses the number of observations in each bin on polynomial terms of the runningvariable (centered at the kink) and the interaction between the centered running variableand the kink. The coefficient on the linear interaction term estimates the change in thefirst derivative at the cutoff. Its significance thus serves as a test of differentiability at thecutoff. I use a 2nd order polynomial, as the trend in fR(r) to the left of the cutoff, shown in159Figure 1.8, suggests a quadratic. Again, I run the test twice using two different bin widths,b = 0.003 and b = 0.006. I again use the CCT optimal bandwidth calculated for the RK,h = 0.0796609. The coefficients on the linear interaction term are shown in the bottomwindow of Table A.5.1. In both specifications, the test fails to reject the null of no kink infR(r) at the cutoff.Table A.5.1: Smoothness tests of 1871 School Supply density at the cutoffMcCrary Test of ContinuityBin Width Log Difference in Height0.003 -0.08208(0.05291)0.006 -0.07975(0.05290)Card Test of DifferentiabilityBin Width Estimated Kink0.003 29.957(690.854)0.006 -11.592(1089.340)A.6 Appendix: Differences between RK and DDD es-timates: Disproven TheoriesOne possible explanation why the LATE measured by the RK is much larger than the DDDATT is that treatment effects were much larger in parishes with pre-treatment school supplynear the kink. To test this, I run the triple difference regression on the sample of individual160within the optimal bandwidth used in the RK. The results are shown in Table A.6.1. Theestimated treatment effect actually decreases slightly, getting further away from the RKresults, suggesting that the use of parishes near the kink is not driving the difference.Another possibility is that the difference is the result of using different levels of obser-vation: in the RK the parish, while in the DDD the individual. In the RK, the use of theparish seems most appropriate, as that is the level at which the first stage treatment decisionoccurs. However, for comparability, I conduct the RK using the individual as the unit ofanalysis, clustering errors at the parish level. I show the results in Figure A.6.4. Note thatwhile the treatment effect is indeed smaller at the previously used optimal bandwidth ofaround 0.0796 - around 5.5 pp as opposed to 12.8 pp. - the effect grows to levels even higherthan 12.8 pp as the bandwidth is shrunk. Thus, is seems that level of observation is also notthe explanation for the differences.A third possibility is that the DDD is underestimating the effect due to a violation inits “no spillovers” assumption. As discussed above, such a violation is unlikely for variousreasons, but cannot be ruled out. Imagine, for instance, that the introduction of publicschools drew human capital intensive industries to treated parishes, which in turn increasedthe probability of employment in literate occupations for the entire parish population, eventhose too old to attend the public schools. This would bias the DDD estimate downward.To directly test for spillovers across age groups, I run a simple difference-in-differences ononly those over 35, all of whom were too old to be fully treated. Under the “no spillovers”assumption, one would expect the treatment effect estimated by the DID interaction termto be close to zero. The results are shown in Table A.6.2. As expected, the treatment effectis never significant, and is essentially zero when parish fixed effects are included, supportingthe “no spillovers” assumption.161Figure A.6.4: Population Weighted RK162Table A.6.1: Triple Diff Within RK Bandwidth(1) (2) (3)Literacy Required Literacy Required Literacy RequiredYears of Treatment 0.00207** 0.00107* 0.00105*(0.000893) (0.000597) (0.000601)Observations 2,348,501 2,348,500 2,328,572Controls NO NO YESParish Fixed Effects NO YES YESArrival-Age Fixed Effects YES YES YESAge Trend Effects YES YES YESArrival Trend Effects YES YES YESRobust standard errors in parentheses, clustered at the parish level. Controls (all interacted with a 1901 dummy):1871 parish population; 1871 parish population squared; distance from London; distance from London squared; 1871school supply per capita; 1851 Church of England attendees per capita 1851 Catholic attendees per capita; 1851other religious service attendees per capita. *** p<0.01, ** p<0.05, * p<0.1Table A.6.2: Difference-in-differences for those over 35(1) (2)VARIABLES Literacy Required Literacy Required(Treatment)*(1901 Year Dummy) -0.00177 0.000330(0.00358) (0.00374)Observations 1,220,922 1,211,168Controls NO YESParish Fixed Effects YES YESArrival-Age Fixed Effects YES YESAge Trend Effects YES YESRobust standard errors in parentheses, clustered at the parish level. Controls (all interacted with a1901 dummy): 1871 parish population; 1871 parish population squared; distance from London;distance from London squared; 1871 school supply per capita; 1851 Church of England attendees percapita 1851 Catholic attendees per capita; 1851 other religious service attendees per capita.*** p<0.01, ** p<0.05, * p<0.1163A.7 Appendix: Census Linking ProcedureThe method used for both the 1861-1881 and 1881-1901 census linkages is based on thatconducted in a series of papers by Abramitzky, Boustan, and Eriksson (2012, 2014, 2019a).The main area of departure is how I use birthplace variables. The Abramitzky et al. methodutilizes only a single birthplace variable. In the UK censuses, however, there are threepossible birthplace variables to use, each with their own pros and cons. Likely the mostaccurate is the county of birth. However, this is also the least specific, and thus results infewer unique matches. A second variable is parish of birth as reported. Obviously this ismuch more specific than county. However, parishes very often had several acceptable names,and therefore if one name was used in the initial census and another in the later census, thismatch would be missed. To deal with this, the Integrated Census Microdata project, wherethe data was received from, created a “standardized” parish of birth variable. However, sucha standardization consists of some guesswork, and thus undoubtedly contains errors.2 Tomitigate the individual shortcomings of each of these variables, I make use of all three, asdescribed below in the step-by-step procedure used to link the 1861-1881 censuses and the1881-1901 censuses:Begin with universe of men aged 5-25 in the early census (either 1861 or 1881, dependingon linkage), and the universe of men aged 25-45 in the late census (either 1881 or 1901).1. Use code provided by Abramitzky et al. to clean names. This removes non-alphabeticcharacters and also accounts for common nicknames so that, for instance, ‘Ben’ and‘Benjamin’ would match.2. For each birth place variable (county, parish as reported, and standardized parish),run the following steps:(a) For each record in the early census, create a group of possible matches with recordsfrom the late census. Possible matches are defined as any records that share thesame birthplace, first and last initials, and whose birth years are within two yearsof each other.(b) For each possible match, calculate Jaro-Winkler similarity scores for first and lastnames, separately. This is a measure of similarity between two strings, with more2See “Integrated Census Microdata (I-CeM) Guide”, pg. 117,207164weight placed on characters at the beginning of the strings. It is equal to 1 if thestrings are identical and 0 if there is no similarity. Keep only those matches forwhich first name and last name Jaro-Winker scores are both 0.9 or above.3. Run the following steps on the surviving matches determined using county birthplace:(i) For each record in the early census, determine the smallest birth year differencebetween it and its potential matches in the late census.3 Similarly, for each recordin the late census, determine the smallest birth year difference between it and itspotential matches in the early census.(ii) Keep only those potential matches for which the birth year difference is equal toboth the smallest birth year difference for the early side of the match and thesmallest birth year difference for the late side of the match.(iii) For each remaining potential match, keep only if unique for both the early andlate sides of the match.4. Combine the county matches remaining after Step 3 with the lists of matches deter-mined using standardized parish birthplace and parish birthplace as recorded. Dropduplicate matches. For each county match, keep only when both the early and lateside of the match do not appear among any potential parish matches.5. Rerun Steps (i)-(iii) on the remaining potential matches.A.8 Appendix: Middle Initial Test for False PositivesTo test the rate of false positives, I make use of middle initials. Given that middle initialwas not used in the matching process (as it is only available for a subset of individuals),a middle initial shared by both sides of a match is a strong indicator that it is indeed atrue match. While the majority of records do not provide middle names, it is provided byboth the early and late side of 205,476 of the 1861-1881 matches (12.9%) and 469,071 of the1881-1901 matches (19%). Among these, 79.2% of the 1861-1881 matches and 90.2% of the1881-1901 matches have the same middle initial on both sides of the match.It is likely of course that these numbers do not perfectly reflect the distribution of truematches in the linkages. On the one hand, even among matches with identical middle3For example, if an individual was born in year x and any of its remaining potential matches were bornin x, its smallest birth year difference would be 0; if, however, none of its remaining potential matches wereborn in x but some were born in either x-1 or x+1, its smallest birth year difference would be 1.165initials there are no doubt some false matches. Assuming the middle initials on eitherside of a false match follow the distribution of middle initials found in the population, theestimated probability of two individuals incorrectly matched sharing the same middle initial,or Pˆ (MI Match | False Match), is 8.6% in the 1861-1881 linkage and 9.4% in the 1881-1901linkage.On the other hand, it is likely that among many true matches, transcription error resultedin mismatching middle initials. Take, for example, the initial “K”. Among matches whereone side of the match has initial “K” while the other side has a different letter, the otherside’s initial is a similarly shaped letter “H” or “R” 32.1% and 31.1% of the time, respectively,while given the population distribution of middle initials one would expect them to appearonly 17.1% and 4.6% of the time, respectively. To pick out which letter combinations werelikely common transcription errors, I compared each combinations (a) frequency in the datawith (b) how often one would expect it to occur if each letter were randomly drawn fromthe population distribution of middle initials. Assuming the true probability of the lettercombination occurring was (b), if the probability of observing frequency (a) in the data is lessthan 0.000001 then I treat the occurrences in excess of what was expected as transcriptionerrors.Table A.8.1 shows the letter combinations meeting this criteria.4 The included combi-nations rarely if ever surprise; in general they are what one would expect as a result oftranscription error.I can now estimate Pˆ (False Link | No MI Match), taking the the number of mismatchedmiddle initials less the estimated number of transcription errors, and dividing it by the totalnumber of mismatched middle initials. Doing this, it is estimated that only 56.5% of linkswith mismatched middle initials in the 1861-1881 linkage are actually false, and 60.4% inthe 1881-1901 census.4Note that this criteria was applied separately to the 1861-1881 and the 1881-1901 linkage. Due to thelarger sample size in the later linkage, there are a number of letter combinations that only meet the criteriathere.166Using Pˆ (MI Match | False Match) and Pˆ (False Link | No MI Match), along with theproportion of mismatching middle initials Pˆ (MI Match), I can estimate the true match rate:P (True Link) = 1− P (False Link)= 1− P (False Link ∩ No MI Match)P (No MI Match)= 1− P (False Link | No MI Match)P (No MI Match)1− P (MI Match | False Link)(A.5)The results, reported in Table A.8.2, suggest that 87.2% of the 1861-1881 links and 93.5%of the 1881-1901 links are true.Table A.8.1: Overrepresented Combinations among Differing Middle InitialsA D, H, O, R I F*, J, S*, T R A, B, K, N, PB D*, P*, R J F, G, I, L, S, T S G*, I*, J, L, P, TC E, G, L, O K H, R, W† T F, I, J, L, P*, S, Y*D A, B*, L*, O L C, D*, F*, J ,S, T U N*, V, WE C, G M H*, N, W V N*, O, P*, UF H*, I*, J, L*, P*, T N H, M, R, U*, V*, W W H, K†, M, N, UG C, E, J, S*, Y O A, C, D, V Y G, T*H A, F*, K, M*, N, W P B*, F*, R, S, T*, V*† Only identified in and applied to 1861-1881 linkage* Only identified in and applied to 1881-1901 linkage167Table A.8.2: Estimated Linking CharacteristicsPˆ (MI Match Pˆ (False LinkPˆ (No MI Match) | False Link) | No MI Match) Pˆ(True Link)1861-1881 LinkagesStandard 0.208 0.086 0.565 0.872Unique in 5-Year Band, Age Exact 0.171 0.084 0.451 0.916Unique in 5-Year Band, Age & Name Exact 0.165 0.084 0.447 0.9191881-1901 LinkagesStandard 0.098 0.094 0.604 0.935Unique in 5-Year Band, Age Exact 0.071 0.091 0.442 0.965Unique in 5-Year Band, Age & Name Exact 0.069 0.092 0.428 0.968168A.9 Appendix: More Conservative Matching Proce-duresEvidence presented in Appendix A.8 strongly suggests that the method used to link cen-suses in this paper (described in detail in Appendix A.7) generated very few false positives.Nonetheless, to ensure that these few false positives are not driving results, the mobilityregressions are rerun on linkages constructed using more conservative methods. Both of theconservative methods used create subsets of the baseline linkage. These methods, while likelyomitting many of the baseline method’s true matches, should lead to fewer false matches.The first new method matches more strictly on age, while the second matches morestrictly on both age and name, creating a subset of the first. Both methods require thateach match’s early and the late records have identical ages and have no other possible matcheswithin the five year window created by adding or subtracting two from age. In contrast, thebaseline match simply requires each match’s early and the late records be within two yearsof each other and have no other possible matches equal to or closer in age. The strictestmethod also demands that the early and late records within each match have identical firstand last names, while the baseline and other conservative method only require both the firstand last name Jaro-Winkler similarity scores to be 0.9 or above.As reported in Table A.8.2, it is estimated that the baseline method results in true matchrates of 87.2% and 93.5% for the 1861-1881 and 1881-1901 linkages, respectively. In contrast,the estimated true match rates using the age-conservative method are 91.6% and 96.5%, andusing the name-and-age-conservative method are 91.9% and 96.8%.Table A.9.1 shows the results of rerunning the mobility regressions using the more con-servative linkages. In all regressions, both public school access’s absolute effect on lower classchildren’s outcomes and the difference between this and its effect on higher class children arelarger than those found using the baseline linkage (shown in Table 1.16). While it shouldbe borne in mind that the more conservative linkages may be less representative of the total169population than the baseline model, these results nonetheless suggest that if anything theresults reported in the paper should be taken as a lower bound.170Table A.9.1: Social Mobility Triple Difference, Matches Unique Within 5-year BandPerfect Matches Perfect Matches onon Age Name & Age(1) (2) (3) (4)Years of Treatment 0.00234** 0.00494** 0.00227** 0.00596**(0.00102) (0.00221) (0.00111) (0.00256)(Years of Treatment)*(Father Class Dummy) -0.00407** -0.00353 -0.00557*** -0.00532(0.00192) (0.00411) (0.00208) (0.00457)Observations 768,988 301,498 655,729 247,857Controls Included YES N.A. YES N.A.Birth Parish-Class Fixed Effects Included YES N.A. YES N.A.Arrival-Age-Class Fixed Effects Included YES YES YES YESAge-Class Trend Effects Included YES YES YES YESArrival-Class Trend Effects Included YES N.A. YES N.A.Brother Fixed Effects Included NO YES NO YESRobust standard errors in parentheses, clustered at parish level. Controls (all interacted with a 1901 dummy, and includinginteractions with father’s class dummy): 1871 parish population; 1871 parish population squared; distance from London;distance from London squared; 1871 school supply per capita; 1851 Church of England attendees per capita 1851 Catholicattendees per capita; 1851 other religious service attendees per capita. *** p<0.01, ** p<0.05, * p<0.1171A.10 Appendix: Alternative Mobility MeasuresIn the paper, occupations that make use of literacy are used as a proxy for good, high payingwork in the mobility regressions. This is made necessary by the fact that wage data fromthe period is scarce. However, other income proxies do exist.One such proxy is OCCSCORE. This records the median total income by occupation inthe 1950 US Census, and is commonly used as an proxy for US wages in earlier periods.Admittedly, the difference in both time and place in this case suggest a somewhat weakrelationship with true income. But its prevalence in the literature merits its usage, if onlyas a source of comparison. As demonstrated in the first two columns of Table A.10.1, themobility results presented in the paper are robust to replacing the literate occupation dummywith ln(OCCSCORE) or percentile as determined using OCCSCORE.The other proxy tested is a ranking of occupations based on the prospects of practitioners’sons. The core assumption used in its construction is that sons of better employed fathersare more likely to end up better employed themselves. To create this ranking I used thefollowing recursive procedure:1. For each occupation, determine the proportion of practitioners’ sons who in adulthoodare practitioners of an occupation in one of the top two categories of the seven categoryHISCLASS variable.2. Assign each occupation a percentile based on these proportions.3. Using these percentiles, determine for each occupation the expected percentile of apractitioner’s son’s adult occupation.4. Redetermine each occupation’s percentile based on these expected percentiles.5. Repeat Steps 3-4 until the ranking of occupations stabilizes.Using the percentiles generated by this procedure, I again estimate the effect of public schoolaccess on lower and higher class children. Once again, the results affirm those shown in thepaper.172Table A.10.1: Social Mobility Triple Difference, Alternative Measures(1) (2) (3)VARIABLES OCCSCORE Recursiveln(OCCSCORE) Percentile PercentileYears of Treatment 0.00181** 0.104* 0.0820**(0.000828) (0.0539) (0.0398)(Years of Treatment)*(Father Class Dummy) -0.00288** -0.152* -0.0363(0.00123) (0.0867) (0.0731)Observations 1,096,626 1,096,970 1,411,146Controls Included YES YES YESBirth Parish-Class Fixed Effects Included YES YES YESArrival-Age-Class Fixed Effects Included YES YES YESAge-Class Trend Effects Included YES YES YESArrival-Class Trend Effects Included YES YES YESRobust standard errors in parentheses, clustered at parish level. Controls (all interacted with a 1901 dummy, and includinginteractions with father’s class dummy): 1871 parish population; 1871 parish population squared; distance from London;distance from London squared; 1871 school supply per capita; 1851 Church of England attendees per capita 1851 Catholicattendees per capita; 1851 other religious service attendees per capita. *** p<0.01, ** p<0.05, * p<0.1173A.11 Appendix: Advantage of Higher Class ChildrenTo determine the advantage of higher class children in 1901 absent the treatment effect, Iregress the literate occupation dummy (Y ) on father’s class, controlling for age and parish ofbirth and using only those in the 1881-1901 linked sample who did not receive any treatment.Note that this includes individuals of all ages in untreated parishes as well as those in treatedparishes too old to receive treatment. The baseline regression equation looks as follows:Yiapc = β(FCi) + αa + ηp + uiapc (A.6)where αa represents age fixed effects and ηp parish fixed effects.To verify that age effects do not vary by parish treatment status, I replace age fixedeffects with arrival year-age fixed effects:Yiapc = β(FCi) + αar + ηp + uiapc (A.7)Finally, if high class children concentrate in parishes with high opportunity for literatejobs, including parish fixed effects would bias the effect downward. Thus I also run thebaseline regression excluding parish fixed effects:Yiapc = β(FCi) + αa + uiapc (A.8)The results of regression on Equations A.6 - A.8 are shown in columns (1)-(3) of TableA.11.1, respectively.174Table A.11.1: Advantage of Untreated High Class Children, 1901(1) (2) (3)VARIABLES Literacy Required Literacy Required Literacy RequiredFather Class Dummy 0.19976*** 0.19974*** 0.23850***(0.00212) (0.00212) (0.00259)Observations 740,118 740,118 740,461Parish Fixed Effects YES YES NOAge Fixed Effects YES NO YESArrival-Age Fixed Effects NO YES NORobust standard errors in parentheses, clustered at the parish level. *** p<0.01, ** p<0.05, * p<0.1175Appendix BAppendix to Chapter 3B.1 Administrative Unit DescriptionsParishes: While administrative parishes, or civil parishes, were originally based on theChurch of England’s ecclesiastic parishes, they had actually become separate entities in the1860s. Major border changes to civil parishes in subsequent decades made the link evenmore tenuous. See Gregory & Southall (2000) for more details. According to the 1894 LocalGovernment Act, the powers of Parishes at the time consisted primarily of managing localrecreational grounds, footpaths, and common areas. They were also to choose a local overseerto administer poor relief provided by the PLU. For further details see Part I, Sections 5-19of the 1894 Local Government Act.Local Government Districts (LGDs): Known as Sanitary Districts until 1894 then LocalGovernment Districts thereafter, these actually consisted of several types of authorities, eachwith slightly different powers. The vast majority were either “Urban Districts” or “RuralDistricts”, but there were also “County Boroughs”, which were essentially urban districtsbut due to historical reasons were given additional rights. In general, however, the powersof LGDs were primarily over sanitation and highways. For additional details see Gregory &Southall (2000) or Part II of the 1894 Local Government Act.176Poor Law Unions (PLUs): The powers of poor law unions are discussed in detail inSection 2’s description of pauperage statistics, however it is also worth noting their useas “Registration Districts”. According to “Vision of Britain”, the public website of theGBHGIS, these were created in 1837 aligned with PLUs but with the separate function ofcollecting data on births and deaths. They were also the primary reporting units of thecensus until after 1911, when LGDs began to be instead. However, as noted below, PLUscontinued to exist into the 1930s.Counties (Administrative & Registration): As the names suggest, Administrativecounties had administrative powers, overseeing LGDs. Registration counties merely servedas reporting units for the census until 1911. There are 55 Administrative and 61 Reg-istration counties. The major geographic differences are that in the Administrative set,Lincolnshire is divided into three, Suffolk and Sussex are divided into east and west, the Isleof Ely is separated from Cambridgeshire, and the Soke of Petersborough is separated fromNorthamptonshire. However, even among counties that were not split, the borders betweenthe Administrative set and the Registration set do not line up completely, due to the factthat the constituent PLUs and LGDs do not always line up.177B.2 Estimation of PLU 1921 PopulationsTotal 1921 PLU population can be estimated with reasonable precision from the pauperagedata, as it includes both total number of paupers as well as the percentage that total isof total population levels, given to the hundredth of a percent. Thus by simply dividingthe total pauperage amount by the proportion of total population, the total population canbe reverse estimated. However, population broken down by age and gender is also needed,which in 1921 is only available at the LGD level. While again the vast majority of LGDs(1687) in 1921 lie fully within a single PLU, the remainder are spread across many of PLUs,meaning that restricting observations to only those PLUs made up of fully contained LGDshas a significant impact on sample size. Therefore, estimates are determined from LGD andparish level data, exploiting the fact that in 1911, both LGDs and PLUs were made up ofparishes.1PLU age/gender population totals are estimated in the following manner. First, theproportion of each LGD’s population that lies within each PLU is determined by groupingparishes that lie within the same PLU and LGD, summing their populations, then dividingby the total LGD population. This is expressed mathematically below:xi,j =nj,i∑k=1populationi,j,k,1911populationj,1911(B.1)where populationi,j,k represents the total population of parish k within PLU i and LGD j in1911, k ∈ {1, . . . , nj,i} where nj,i is the number of parishes lying in both PLU i and LGD j,populationj,1911 is the total population of LGD j in 1911, j ∈ {1, . . . , n} where n is the totalnumber of LGDs, and xi,j is the proportion of LGD j’s total 1911 population that lies withPLU i. xi,j is then multiplied by the age/gender 1921 totals of LGD j to find an estimationof the totals by age/gender living in LGD j and PLU i in 1921, which are then summated1Given that PLUs did not adjust in 1921 to parish adjustments, this does not hold exactly true in 1921.178to find an estimation for the entire PLU:populationa,g,i,1921 =n∑j=1(xi,j)(populationa,g,j,1921) (B.2)where populationa,g,i,1921 represents the estimation of the population in PLU i within ageband a and of gender g in 1921, while populationa,g,j,1921 is the population in LGD j withinage band a and of gender g in 1921.Obviously, the validity of this estimation rests on several assumptions. The first is thatfor each age and gender group in LGD j, the proportion living in PLU i is equal to theproportion of the total population of LGD j that lives in PLU i. This will hold true if thegender and age ratios within a LGD are uniform, which is to say no matter how you dividean individual LGD, all its constituent parts will have the same age and gender ratios. Whilethis obviously will not hold exactly, it does not appear an entirely unreasonable assumption,given that LGDs are already divided along rural and urban grounds, and are geographicallyquite small, meaning that parishes within them are likely very similar to each other in termsof density and labour markets. The other assumption this estimation implies is that theproportion of LGD j living in PLU i does not change between 1911 and 1921. This obviouslywould not hold true if LGD j significantly changed its borders, or if there was significantdifferences in migration rates within LGD j. In order to minimize this measurement error,each PLU’s total population estimated by this method is compared with the total populationreverse engineered using pauperage totals and percentages. If the difference is more than 1%,the PLU is dropped from the sample. This still retains significantly more observations thanwould be the case if only those PLUs made up of only fully contained LGDs were included.179B.3 Possible Border ChangesBetween 1911 and 1921, while PLU borders remained static, LGD and parish borders didnot.2 The large majority of LGDs (1,640, or nearly 90%) remained unchanged, but the re-mainder were adjusted when necessary to keep up with parish changes, and also occasionallyfaced additional adjustment. Where these changes were major, the GBHGIS gives the LGDa new identifier; however in the vast majority of cases (1,798, or nearly 98%) GBHGIS links1911 LGDs with 1921 LGDs even if minor border changes have occurred.3 For the purposeof this paper, the LGDs identified by the GBHGIS as experiencing major border changesbetween 1911 and 1921 are dropped, but the remainder are kept for the primary analysis.Given that all the outcomes examined are rates and thus adjusted by population, includingLGDs that experienced minor border changes between 1911 and 1921 should not be a sig-nificant source of measurement error, assuming the added or subtracted areas were typicallysimilar to the LGD as a whole.2One can only assume that due to their discontinuation of use as the primary census reporting unit in1911, it was not felt necessary to realign PLU borders to keep them in line with parish changes.3These changes mean that in 1921 there were only 1827 LGD, down from 1841 in 1911180B.4 Matching Administrative Geographies with Sol-dier BirthplacesThe process of sorting the birthplaces geographically to each administrative unit is outlinedbelow. Death records were aggregated by birthplace listed, of which there proved to be87,331 unique places. These places initially proved difficult to link to a single geographiclevel, as some were Parishes, others were villages or towns, while still others were streetsor specific addresses. In order to find the total number of casualties born within eachof the geographic levels used in this analysis, the following method was used. First, thegeographic coordinates of each unique birthplace was obtained using the Google geocodingAPI.4 This API is relatively simple: when provided with a place name as input, coordinatesof the locations centroid (along with other information, including boundary coordinates andmailing address) are given as output. One fear is that a place name may not be unique, inwhich case Google lists the most likely place first (based on its own algorithms), followedby other possible places. In order to decrease the likelihood of such an event polluting thedata, the suffix “UK” was added to the end of each birthplace before it was provided tothe API. It is worth noting at this point that not all the birthplaces listed in the recordswere within the UK. There are several reasons for this, one being that the forces includedsome immigrants. As well, many regions of the British Empire provided soldiers to servein the British forces.5 Perhaps most importantly, Ireland, at the time still under Britishrule, provided many soldiers to British forces. In general, the API was unable to find thesebirthplaces, as they did not exist once the “UK” suffix was added. This of course is noproblem to the analysis, as these locations are not included anyway. It is possible that in afew cases a birthplace outside of the UK was falsely attributed to a UK location; howeverthis seems relatively unlikely, as records of births that took place outside the UK typically4Documentation regarding the Google geocoding API can be found athttps://developers.google.com/maps/documentation/geocoding, accessed on Aug. 31, 20165Indeed, whole regiments consisting of Indian and African soldiers are among the regiments whose deathsare provided in “Soldiers Died”.181included country of birth, making the full place name relatively unlikely to also occur withinthe UK.6Once coordinates were obtained for each birthplace, these were placed on a map ofBritain and overlaid with maps of the administrative levels described in Section 2.7 Each setof coordinates was also tied to the total number of soldier deaths records listing that placeof birth. Thus, the total number of soldiers born in a region that died and were recorded canbe found by simply grouping all birthplace coordinates that lie within the borders of saidregion and summing their death totals.6For instance, one can imagine a “Paris, UK” existing, but it is much less likely that a “Paris, France,UK” exists.7The maps were obtained from GBHGIS. Note that in the case of LGD and Admin. Counties, bordersshifted from 1911 to 1921, so for consistency sake death totals by 1911 borders are always used.182B.5 Measurement error caused by migration and birth-place exclusionFor all counties k and m, the number of people born within county k and currently residingin county m is recorded. Let θkm be the number of people born within county k who residedin county m. Using this data, an attempt to directly correct the migration misclassificationis undertaken.8 Letγkm = Pr(R = m | B = k) (B.3)where B is the birth county, and R is county of residence in 1911.P =γ11 . . . γ1n.... . ....γn1 . . . γnn (B.4)where n is the total number of counties. γˆkm is estimated from the migration data as follows:γˆkm =θkm∑nj=1 θkj(B.5)Pˆ is in turn calculated by replacing each term in Equation B.4 with its equivalent fromEquation B.5. What we want to find ispim = Pr(killed | R = m) (B.6)for all m. However, this is unavailable to us. What we do have is an estimation of the totalnumber of deaths by birthplace. Let yˆk be the estimated total number of soldier deaths in8The basic concepts of the following model are drawn from Shieh (2008), pg. 2, a literature review ofmisclassification methods.183birth county k, as defined in Equation 3.1. Further, letρk = Pr(killed | B = k) ≈ ρˆk = yˆr∑nj=1 θkj(B.7)Let us assume that, conditional on county of residence, the probability of being killed isindependent of birth county.9 Then, by application of Bayes’s Rule:ρk = Pr(killed | Bi = k) =n∑j=1Pr(killed ∩R = j | B = k)=n∑j=1Pr(B = k | killed ∩R = j) Pr(killed ∩R = j)Pr(B = k)=n∑j=1Pr(B = k | R = j) Pr(killed ∩R = j)Pr(B = k)=n∑j=1Pr(R = j | B = k) Pr(killed ∩R = j)Pr(R = j)=n∑j=1Pr(R = j | B = k) Pr(killed | R = j)=n∑j=1γkjpij(B.8)It is easy then to see thatρ = Ppi (B.9)where ρ = (ρ1 . . . ρn)−1 and pi = (pi1 . . . pin)−1. Then we can estimate pi as follows:pˆi = Pˆ−1ρˆ (B.10)This estimation is done using the migration and death data. The summary statistics of theestimated death rates are provided in Table 3.8.10 This analysis rests on the assumption that9Given that the military units were structured not on the basis of birth places but on places of residence,this seems plausible.10It should be noted that in general, the estimated death rates are higher that the na¨ıve estimates. Thisis likely because instead of dividing by total population, as in the na¨ıve estimate, this estimate is divided184the proportion of military aged males born within county k and residing in county m is thesame as the proportion of the total population born in k and residing in m. Unfortunately,age-migration data is not available, so it is difficult to test this assumption.The use of yˆk, the estimated total number of deaths in birth county k, presents anotherconcern. Around 20% of death records do not provide birthplaces, meaning yˆk containsmeasurement error. Assuming the rate of birthplace exclusion does not vary across counties,this error can be modelled and accounted for in county level regressions. The probability thatany given death record will include birthplace can be modelled as a Bernoulli trial, with sprobability of success, where s, as defined previously, is the proportion of death records thatinclude birthplace (in this case 0.7853). Then the total number of death records providingbirthplaces can be modelled as a binomial variable B(n, s), where n is total deaths. Usingthis model, measurement error due to excluded birthplace data is estimated using a bootstrapmethod, described below. With the estimate of this measurement error, it can be accountedfor in regressions using the regression calibration method. While regression calibration is notexplored in detail here, a brief overview is provided.11 Essentially, it regresses on a predictedvalue of the variable with measurement error. Let x be the variable of interest, and w be aproxy for it measured with error. The regression calibration model regresses onxˆi = w¯ + κˆ(wi − w¯) (B.11)where κˆ is the reliability matrix, defined asκˆ =V̂ ar(x)V̂ ar(x) + V̂ ar(x− w)(B.12)only by total population born within England and Wales. This excludes all immigrants, including those fromScotland and Ireland. Therefore, the point estimates should be used cautiously. However, if one assumesthat the ratio of immigrants to native-born is similar across counties, then the estimates are merely off by ascalar factor. This assumption is likely untrue in the case of London, but may not be too strong for otherregions. For this and other reasons regressions excluding London are included in the analysis.11For a more complete treatment, see Buonaccorsi (2010), pg. 191-193185Bootstrap methods are used to estimate κˆ. Using the death rates pim for each county ofresidency m estimated using the migration data, a bootstrapped replication yˆbkm, representingthe number of killed soldiers born in county k who in 1911 resided in county m, is generatedfrom a binomial distribution B(θkm, pim). The bootstrap estimate of the number of deathrecords listing county k as birthplace is then determined from the binomial distributionB(yˆbkm, pim). From there, yˆbk is determined from this bootstrapped number of death recordsusing Equation 3.1. pˆib is then estimated using yˆb. This is done for 250 bootstrap samples.The variance of the measurement error (x− w) for each county k is then estimated asV̂ ar(xk − wk) =250∑b=1(pˆik − pˆibk)2/250 (B.13)The mean of these variances is used as V̂ ar(x−w). This is calculated to be 1.31e-06 which,given the mean value of pˆik was calculated to approximately 0.038, appears to be very small.186


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