{"@context":{"@language":"en","Affiliation":"http:\/\/vivoweb.org\/ontology\/core#departmentOrSchool","AggregatedSourceRepository":"http:\/\/www.europeana.eu\/schemas\/edm\/dataProvider","Campus":"https:\/\/open.library.ubc.ca\/terms#degreeCampus","Creator":"http:\/\/purl.org\/dc\/terms\/creator","DateAvailable":"http:\/\/purl.org\/dc\/terms\/issued","DateIssued":"http:\/\/purl.org\/dc\/terms\/issued","Degree":"http:\/\/vivoweb.org\/ontology\/core#relatedDegree","DegreeGrantor":"https:\/\/open.library.ubc.ca\/terms#degreeGrantor","Description":"http:\/\/purl.org\/dc\/terms\/description","DigitalResourceOriginalRecord":"http:\/\/www.europeana.eu\/schemas\/edm\/aggregatedCHO","FullText":"http:\/\/www.w3.org\/2009\/08\/skos-reference\/skos.html#note","Genre":"http:\/\/www.europeana.eu\/schemas\/edm\/hasType","GraduationDate":"http:\/\/vivoweb.org\/ontology\/core#dateIssued","IsShownAt":"http:\/\/www.europeana.eu\/schemas\/edm\/isShownAt","Language":"http:\/\/purl.org\/dc\/terms\/language","Program":"https:\/\/open.library.ubc.ca\/terms#degreeDiscipline","Provider":"http:\/\/www.europeana.eu\/schemas\/edm\/provider","Publisher":"http:\/\/purl.org\/dc\/terms\/publisher","Rights":"http:\/\/purl.org\/dc\/terms\/rights","RightsURI":"https:\/\/open.library.ubc.ca\/terms#rightsURI","ScholarlyLevel":"https:\/\/open.library.ubc.ca\/terms#scholarLevel","Supervisor":"http:\/\/purl.org\/dc\/terms\/contributor","Title":"http:\/\/purl.org\/dc\/terms\/title","Type":"http:\/\/purl.org\/dc\/terms\/type","URI":"https:\/\/open.library.ubc.ca\/terms#identifierURI","SortDate":"http:\/\/purl.org\/dc\/terms\/date"},"Affiliation":[{"@value":"Arts, Faculty of","@language":"en"},{"@value":"Vancouver School of Economics","@language":"en"}],"AggregatedSourceRepository":[{"@value":"DSpace","@language":"en"}],"Campus":[{"@value":"UBCV","@language":"en"}],"Creator":[{"@value":"Martins Secco Luce, Fernando","@language":"en"}],"DateAvailable":[{"@value":"2024-04-24T20:32:13Z","@language":"en"}],"DateIssued":[{"@value":"2024","@language":"en"}],"Degree":[{"@value":"Doctor of Philosophy - PhD","@language":"en"}],"DegreeGrantor":[{"@value":"University of British Columbia","@language":"en"}],"Description":[{"@value":"Chapter 2 analyzes the impact of private colonization on government size and public goods provision. We focus on the Donatary Captaincy system in Brazil, which split the Portuguese colony into strips of land and granted private citizens jurisdiction, rights, and ownership of the territory. Our findings suggest that longer exposure to private colonization led to smaller governments, measured by the number of public employees and public expenditures, and lower provision of public education and health in 1920, approximately 180 years after the end of the system. While some convergence was observed in 2010, negative effects on health outcomes persist over time.\r\n\r\nIn Chapter 3, I study the long-run effects of female slavery in the 19th century on violence against black women. I take advantage of the draft of male slaves by the Brazilian empire during the Paraguayan war (1864-1870) and instrument the share of female slaves using the distance to the war front. I find that Brazilian municipalities with a higher share of female slaves in 1872 have more cases of physical and psychological violence against black women today. The same pattern is not observed for cases against white and brown women.\r\n\r\nIn Chapter 4, we analyze jobseekers' strategic responses to (expected) discrimination in the job market. We run three field experiments with 2,200 jobseekers in the context of Rio de Janeiro's favelas. We partner with a private firm with real job openings to estimate how jobseekers' expected discrimination affects job application behavior and interview performance. Interview performance is 0.13SD higher for jobseekers randomly told their interviewer would know only their name, as opposed to their name \\textit{and address}. In contrast, average job application rates are unaffected by (i) removing the need to declare an address at the application stage and (ii) information that we did not find evidence for discrimination in our audit study. Our findings show experimental evidence that expected discrimination may affect jobseekers' search, especially in in-person interactions.","@language":"en"}],"DigitalResourceOriginalRecord":[{"@value":"https:\/\/circle.library.ubc.ca\/rest\/handle\/2429\/87994?expand=metadata","@language":"en"}],"FullText":[{"@value":"Essays in Economic History and DevelopmentbyFernando Martins Secco LuceB.A., PUC-Rio, 2014M.A., PUC-Rio, 2018a 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)April 2024\u00a9 Fernando Martins Secco Luce, 2024The following individuals certify that they have read, and recommend to the Faculty ofGraduate and Postdoctoral Studies for acceptance, the thesis entitled:Essays in Economic History and Developmentsubmitted by Fernando Martins Secco Luce in partial fulfillment of the requirements for thedegree of Doctor of Philosophy in Economics.Examining Committee:Felipe Valencia Caicedo, Assistant Professor, Vancouver School of Economics, UBCSupervisorClaudio Ferraz, Professor, Vancouver School of Economics, UBCSupervisory Committee MemberMatt Lowe, Assistant Professor, Vancouver School of Economics, UBCSupervisory Committee MemberNathan Nunn, Professor, Vancouver School of Economics, UBCUniversity ExaminerBenjamin Bryce, Associate Professor, Department of History, UBCUniversity ExamineriiAbstractChapter 2 analyzes the impact of private colonization on government size and public goodsprovision. We focus on the Donatary Captaincy system in Brazil, which split the Portuguesecolony into strips of land and granted private citizens jurisdiction, rights, and ownership ofthe territory. Our findings suggest that longer exposure to private colonization led to smallergovernments, measured by the number of public employees and public expenditures, andlower provision of public education and health in 1920, approximately 180 years after theend of the system. While some convergence was observed in 2010, negative effects on healthoutcomes persist over time.In Chapter 3, I study the long-run effects of female slavery in the 19th century on violenceagainst black women. I take advantage of the draft of male slaves by the Brazilian empireduring the Paraguayan war (1864-1870) and instrument the share of female slaves using thedistance to the war front. I find that Brazilian municipalities with a higher share of femaleslaves in 1872 have more cases of physical and psychological violence against black womentoday. The same pattern is not observed for cases against white and brown women.In Chapter 4, we analyze jobseekers\u2019 strategic responses to (expected) discrimination in thejob market. We run three field experiments with 2,200 jobseekers in the context of Rio deJaneiro\u2019s favelas. We partner with a private firm with real job openings to estimate how job-seekers\u2019 expected discrimination affects job application behavior and interview performance.Interview performance is 0.13SD higher for jobseekers randomly told their interviewer wouldknow only their name, as opposed to their name and address. In contrast, average job appli-cation rates are unaffected by (i) removing the need to declare an address at the applicationstage and (ii) information that we did not find evidence for discrimination in our audit study.Our findings show experimental evidence that expected discrimination may affect jobseekers\u2019search, especially in in-person interactions.iiiLay SummaryThis thesis discusses issues related to the long-run impacts of historical events and jobseekers\u2019response to expected discrimination in the labour market. In Chapter 2, I analyze how aprivate colonization system implemented by the Portuguese Crown in Colonial Brazil betweenthe 16th and 18th centuries has impacted government size and public goods provision in themedium and long run. Chapter 3 focuses on the historical impacts of the slaves\u2019 gendercomposition and how it translates into cases of violence against black women in moderntimes. Lastly, Chapter 4 studies how jobseekers react to expected discrimination in the jobmarket, both in the application and the interview stages.ivPrefaceThe research in Chapter 2 is an original, unpublished, and joint work with professors FelipeValencia Caicedo (University of British Columbia) and Humberto Laudares (University ofGeneva). Fernando developed the research design, conducted the empirical analysis, evalu-ated the results, and wrote the text. The other co-authors contributed to the identificationof the research question and the collection of data. Chapter 3 is an original, unpublished,and independent work by the author of this thesis, Fernando Martins Secco Luce. Chapter 4is an original, unpublished, and joint work with PhD candidate Deivis Angeli (University ofBritish Columbia) and postdoctoral fellow Ieda Matavelli (University of New South Wales).Fernando contributed to the development of the research question and design, the knowledgeof the local context, and the interpretation of the results. The other co-authors contributedto fieldwork organization, research design development, and analysis of the results. Chapter4 was written collaboratively by the co-authors.The fieldwork reported in Chapter 4 was approved by UBC\u2019s Behavioural Research EthicsBoard, under approval number H22-03418.vTable of ContentsAbstract . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . iiiLay Summary . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . ivPreface . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . vTable of Contents . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . viList of Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . ixList of Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xiAcknowledgements . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xiiiDedication . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xv1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 12 Private Colonization and State Capacity: Evidence from the BrazilianDonatary Captaincies . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 42.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 42.2 The Donatary Captaincy System in Brazil . . . . . . . . . . . . . . . . . . . 72.3 Empirical Strategy and Data . . . . . . . . . . . . . . . . . . . . . . . . . . . 132.3.1 Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . . . . 132.3.2 Sample . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 142.3.3 Balance Test . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 182.3.4 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 182.4 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 192.4.1 1920 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 192.4.2 2010 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 222.5 Robustness Checks . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 252.5.1 Regression Discontinuity Analysis . . . . . . . . . . . . . . . . . . . . 26vi2.5.2 Spatial Correlation and Non-Linearity . . . . . . . . . . . . . . . . . 282.5.3 Placebo Donatary Captaincies . . . . . . . . . . . . . . . . . . . . . . 292.6 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 313 Slavery and Violence against Black Women: Evidence from Brazil . . . . 333.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 333.2 Related Literature . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 353.3 The Paraguayan War (1864-1870) . . . . . . . . . . . . . . . . . . . . . . . . 373.4 Empirical Strategy and Data . . . . . . . . . . . . . . . . . . . . . . . . . . . 413.4.1 Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . . . . 413.4.2 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 433.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 463.5.1 OLS Estimates . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 463.5.2 IV Estimates . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 493.5.3 Mechanism . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 523.6 Robustness Checks . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 533.6.1 Corrientes as War Front . . . . . . . . . . . . . . . . . . . . . . . . . 533.6.2 Placebo Tests . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 563.6.3 Additional Checks . . . . . . . . . . . . . . . . . . . . . . . . . . . . 583.7 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 594 Expected Discrimination and Job Search . . . . . . . . . . . . . . . . . . . 604.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 604.2 Context, Sample, and Misperceived Discrimination . . . . . . . . . . . . . . 674.2.1 Favelas in Rio de Janeiro . . . . . . . . . . . . . . . . . . . . . . . . . 674.2.2 Audit Study: Measuring Anti-favela Discrimination . . . . . . . . . . 684.2.3 Perceived vs. Actual Discrimination . . . . . . . . . . . . . . . . . . . 694.3 Experiment Design . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 704.3.1 Sample Recruitment . . . . . . . . . . . . . . . . . . . . . . . . . . . 704.3.2 Address Omission Experiment (N=1,303) . . . . . . . . . . . . . . . . 744.3.3 Information Experiment (N=690) . . . . . . . . . . . . . . . . . . . . 754.3.4 Interview Experiment (N=422) . . . . . . . . . . . . . . . . . . . . . 774.3.5 Randomization, Balance, and Estimation . . . . . . . . . . . . . . . . 784.4 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 804.4.1 Address Omission Experiment . . . . . . . . . . . . . . . . . . . . . . 804.4.2 Information Experiment . . . . . . . . . . . . . . . . . . . . . . . . . 814.4.3 Interview Experiment . . . . . . . . . . . . . . . . . . . . . . . . . . . 854.5 Discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 87vii4.5.1 Race and Stigma Visibility . . . . . . . . . . . . . . . . . . . . . . . . 874.5.2 Obfuscation . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 894.5.3 Policy Considerations . . . . . . . . . . . . . . . . . . . . . . . . . . . 904.6 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 935 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 95Bibliography . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 97A Appendix to Chapter 2 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 108A.1 Supplementary Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 108A.2 Supplementary Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 117B Appendix to Chapter 3 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 119B.1 Supplementary Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 119B.2 Supplementary Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 127C Appendix to Chapter 4 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 133C.1 Supporting Tables And Figures . . . . . . . . . . . . . . . . . . . . . . . . . 133C.1.1 Baseline Survey . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 133C.2 Deviations from the Pre-Analysis Plan . . . . . . . . . . . . . . . . . . . . . 151C.3 Audit Study . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 152C.3.1 Audit Study Neighborhoods . . . . . . . . . . . . . . . . . . . . . . . 152C.3.2 Re\u00b4sume\u00b4s . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 153C.3.3 Job Postings . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 155C.3.4 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 156C.4 Materials Used in Experiments . . . . . . . . . . . . . . . . . . . . . . . . . 157C.4.1 Interview Experiment Details . . . . . . . . . . . . . . . . . . . . . . 161C.4.2 Interview Script . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 161viiiList of TablesTable 2.1 Captains, Grant Date, and Background . . . . . . . . . . . . . . . . . . . 12Table 2.2 Captains, Grant Date, and Background . . . . . . . . . . . . . . . . . . . 17Table 2.3 Government Size and Public Expenditure in 1920 . . . . . . . . . . . . . . 20Table 2.4 Public Goods Provision in 1920 . . . . . . . . . . . . . . . . . . . . . . . . 21Table 2.5 GDP and Land Inequality in 1920 . . . . . . . . . . . . . . . . . . . . . . 22Table 2.6 Government Size and Public Expenditure in 2010 . . . . . . . . . . . . . . 23Table 2.7 Public Goods Provision in 2010 . . . . . . . . . . . . . . . . . . . . . . . . 24Table 2.8 GDP and Land Inequality in 2010 . . . . . . . . . . . . . . . . . . . . . . 25Table 2.9 Placebo DC - 1920 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 30Table 2.10 Placebo DC - 2010 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 31Table 3.1 Summary Statistics: Municipal Characteristics . . . . . . . . . . . . . . . 44Table 3.2 Summary Statistics: Violence against Women . . . . . . . . . . . . . . . . 46Table 3.3 OLS Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 48Table 3.4 First Stage . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 49Table 3.5 IV Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 51Table 3.6 Mechanisms . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 53Table 3.7 First Stage - Distance to Corrientes . . . . . . . . . . . . . . . . . . . . . 54Table 3.8 IV Results - Distance to Corrientes . . . . . . . . . . . . . . . . . . . . . . 55Table 3.9 Violence Against Men . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 57Table 3.10 Violence Against Women - Low Levels of Education . . . . . . . . . . . . 58Table 4.1 IV Estimates of How Expected Discrimination Beliefs Affect ApplicationRates . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 84Table 4.2 Information Does Not Affect Application Rates at Endline . . . . . . . . . 85Table A.1 Summary Statistics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 108Table A.2 Geographical Variables . . . . . . . . . . . . . . . . . . . . . . . . . . . . 109Table A.3 Balance Test: Suitability . . . . . . . . . . . . . . . . . . . . . . . . . . . 110Table A.4 Population 1920 and 2010 . . . . . . . . . . . . . . . . . . . . . . . . . . . 111ixTable A.5 Non-SUS Medical Doctors in 2010 . . . . . . . . . . . . . . . . . . . . . . 112Table A.6 Conley SD - 1920 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 113Table A.7 Conley SD - 2010 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 114Table A.8 Non-Linear Measure - 1920 . . . . . . . . . . . . . . . . . . . . . . . . . . 115Table A.9 Non-Linear Measure - 2010 . . . . . . . . . . . . . . . . . . . . . . . . . . 116Table B.1 First Stage Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 119Table B.2 Second Stage - All types of Violence . . . . . . . . . . . . . . . . . . . . . 120Table B.3 Second Stage - Physical Violence . . . . . . . . . . . . . . . . . . . . . . . 121Table B.4 Second Stage - Psychological Violence . . . . . . . . . . . . . . . . . . . . 122Table B.5 Second Stage - Sexual Violence . . . . . . . . . . . . . . . . . . . . . . . . 123Table B.6 Second Stage - Violence with signs of Torture . . . . . . . . . . . . . . . . 124Table B.7 IV Results - Spatial Standard Errors . . . . . . . . . . . . . . . . . . . . . 125Table B.8 IV Results using IHS Transformation on Cases of Violence . . . . . . . . . 126Table C.1 Baseline Statistics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 133Table C.2 Census (2010) Summary Statistics . . . . . . . . . . . . . . . . . . . . . . 134Table C.3 Address Omission Experiment: Randomization Balance . . . . . . . . . . 135Table C.4 Information Experiment: Randomization Balance . . . . . . . . . . . . . . 136Table C.5 Interview Experiment : Randomization Balance . . . . . . . . . . . . . . . 137Table C.6 Comparison of Samples Across the Three Experiments . . . . . . . . . . . 138Table C.7 Effects of Information on Beliefs for Under- and Overestimators . . . . . . 139Table C.8 Audit Study Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 156xList of FiguresFigure 2.1 Map of the Donatary Captaincies . . . . . . . . . . . . . . . . . . . . . . 9Figure 2.2 Donatary Captaincies - Horizontal Borders . . . . . . . . . . . . . . . . . 15Figure 2.3 Donatary Captaincies - New Boundaries . . . . . . . . . . . . . . . . . . 16Figure 2.4 Donatary Captaincies: Private and Public Colonization . . . . . . . . . . 26Figure 2.5 1920 Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 27Figure 2.6 2010 Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 28Figure 2.7 Placebo Donatary Captaincies . . . . . . . . . . . . . . . . . . . . . . . . 29Figure 3.1 Movements of Paraguayan troops (in black) and the Triple Alliance army(in red) during the attack to Corrientes and Rio Grande do Sul. . . . . . 39Figure 3.2 Areas in the sample . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 42Figure 4.1 Predicted vs. Actual Discrimination Rates . . . . . . . . . . . . . . . . . 71Figure 4.2 Experimental Design . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 74Figure 4.3 Information Treatment Delivery . . . . . . . . . . . . . . . . . . . . . . . 76Figure 4.4 Effects of Address Omission . . . . . . . . . . . . . . . . . . . . . . . . . 81Figure 4.5 Information Treatment Shifts Beliefs, But Not Interview Show-up . . . . 84Figure 4.6 Expected Stigma Visibility Affects Interview Performance, Especially forthe Group Expecting High Discrimination . . . . . . . . . . . . . . . . . 87Figure 4.7 Race and Address Visibility Operate as Substitutes . . . . . . . . . . . . 89Figure 4.8 Expected Discrimination May Also Affect Final Interviewer Rating . . . 91Figure A.1 State and Donatary Captaincies Boundaries . . . . . . . . . . . . . . . . 117Figure A.2 Years of Private Colonization . . . . . . . . . . . . . . . . . . . . . . . . 118Figure B.1 Cartoon published in the Brazilian newspaper Cabria\u02dco in December 12thof 1866. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 127Figure B.2 Cartoon published in the Brazilian newspaper Cabria\u02dco in September 22thof 1867. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 128xiFigure B.3 Cartoon published in the Paraguayan newspaper Cabichu\u00b4\u0131 in October 7thof 1867, portraying, in a racist manner, the Triple Alliance soldiers asmonkeys. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 129Figure B.4 Another racist characterization of the Triple alliance army published inthe Paraguayan newspaper Cabichu\u00b4\u0131 in August 5th of 1867. . . . . . . . 130Figure B.5 Map of South America and the Location of Uruguaiana . . . . . . . . . . 131Figure B.6 Map of South America and the Location of Corrientes . . . . . . . . . . 132Figure C.1 Figure 4.4 with Lasso-selected Controls . . . . . . . . . . . . . . . . . . . 140Figure C.2 Figure 4.5 with Lasso-selected Controls . . . . . . . . . . . . . . . . . . . 141Figure C.3 Effects of Information Treatments on Beliefs and Applications by WhetherJobseekers Initially Under- or Overestimated the Favela Callback Rate . 142Figure C.4 Heterogeneous Effects in the Address Omission Experiment \u2013 No Controls 143Figure C.5 Heterogeneous Effects in the Address Omission Experiment \u2013 Double-lassoControls . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 144Figure C.6 Heterogeneous Effects of Information Treatments \u2013 No Controls . . . . . 145Figure C.7 Heterogeneous Effects of Information Treatments \u2013 Double-lasso Controls 146Figure C.8 Heterogeneous Effects of Name-Only . . . . . . . . . . . . . . . . . . . . 147Figure C.9 Predicted vs. Actual Discrimination Rates . . . . . . . . . . . . . . . . . 148Figure C.10 Predicted Audit Study Discrimination Correlates with Other Measures ofExpected Discrimination . . . . . . . . . . . . . . . . . . . . . . . . . . . 149Figure C.11 Belief Update in Information Experiment Occurs for Mare\u00b4 and Non-Mare\u00b4Residents . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 150Figure C.12 Bonsucesso (Non-Favela) vs. Mare\u00b4 (Favela) . . . . . . . . . . . . . . . . . 152Figure C.13 Example Re\u00b4sume\u00b4 \u2013 Mare\u00b4 home address . . . . . . . . . . . . . . . . . . . 153Figure C.14 Example Re\u00b4sume\u00b4 \u2013 Bonsucesso Address . . . . . . . . . . . . . . . . . . 154Figure C.15 Examples of Job Posting . . . . . . . . . . . . . . . . . . . . . . . . . . . 155Figure C.16 Door-to-Door Baseline Survey . . . . . . . . . . . . . . . . . . . . . . . . 157Figure C.17 Predicted Discrimination Baseline Script . . . . . . . . . . . . . . . . . . 158Figure C.18 Partner\u2019s Job Descriptions . . . . . . . . . . . . . . . . . . . . . . . . . . 159Figure C.19 Second Screen of the Application Form of Each Experimental Conditionin the Address Omission Experiment . . . . . . . . . . . . . . . . . . . . 160Figure C.20 Interview Co-Working Space . . . . . . . . . . . . . . . . . . . . . . . . . 161xiiAcknowledgementsThe Ph.D. journey is an intense experience, one that teaches us a great deal about ourselvesand the people that surround us. However, it\u2019s a path that started years before I arrived here.For that reason, I would like to start by thanking those who were always there: my family.First and foremost, I would like to thank my wife, Anna, for embarking on this dream withme and making me live the happiest possible life by your side. You are equally responsiblefor this as I am. To my parents Fernanda and Claudio, and my sister Fabiola, I\u2019m deeplygrateful for your incredible support over my whole academic journey. In moments of doubt,your encouragement kept me on track and reminded me that the love that we share is mygreatest achievement.I would also like to thank all my friends in Brazil, especially Breno, Paula, Ronchini, Gabi,Rodrigo Giga, and the Sino guys. Living abroad means missing out on important celebrations,and I feared that this journey would push me away from you. Yet, you\u2019ve stood by me, and Icould feel your support every step of the way. I hope I\u2019m able to make you feel as supportedas I do. Thank you for everything!To my Brazilian\/Canadian friends Vinicius, Jaque, Let\u00b4\u0131cia (and L\u00b4\u0131via), and Will, thank youfor the countless adventures and memories we created together. I hope to take your friendshipwith me no matter where I am.The academic journey is one filled with challenges, but it is also an opportunity to meetamazing people. First, I want to thank Ieda, for all the support since day one. All themoments we had together made the days in Vancouver unforgettable. I would also like tothank my amazing friends Pablo, Cata, Vinicius, Seb, Valentina, Deivis, Federico, Giulia,Xiaojun, Pascu, Daniel, Bernardo, Pacho, Jan, Max, Sam, Amir, Tiago, Gabi, Paul, andAlejandro for all the years. I would like to extend this acknowledgement to all the friendsthat I made in previous steps of the academic journey, but whose friendships I cherished untiltoday: Roberto, Rodolfo, Alison, Pedro Pessoa and Pedro Americo, thank you!Special thanks to my advisor, Felipe Valencia Caicedo, whose support and mentorship wereinvaluable in this process, and professors Claudio Ferraz, Matt Lowe, Jamie McCasland, andxiiiNathan Nunn for their lessons and guidance throughout this journey.Finally, I would like to thank Fluminense Football Club for giving me the best graduationgift I could have ever received: the 2023 Copa Libertadores!xivDedication\u2013 To my family Anna, Fernanda, Claudio, and Fabiola. Your uncondi-tional love and support are the true reason behind my accomplishments.xvChapter 1IntroductionThis thesis comprises three chapters on economic history and development. Chapter 2 ex-plores the lasting impacts of private colonization on government and public goods provision,in the context of the Donatary Captaincy system in colonial Brazil. I maintain the focus onestimating historical impacts and analyze how female slavery in the 19th century impactedviolence against black women in the 21st century in the third chapter. Finally, Chapter4 studies how jobseekers respond to expected discrimination in labour market interactions,through three field experiments in favelas in Rio de Janeiro.Chapter 2 explores the historical impact of private colonization on government size and publicgoods provision. We evaluate this question in the context of the Donatary Captaincy imple-mented in colonial Brazil. In the early 16th century, the Portuguese Crown was strugglingfinancially and was unable to populate the colony, leaving it exposed to foreign invasions.Their solution was to partition it into strips of land, each encompassing approximately 50leagues of coastline, and assign each strip to a private citizen, granting them jurisdiction andfull autonomy. Between 1534 and 1753, fifteen captaincies were established and each captainbecame solely responsible for implementing a government and stimulating economic develop-ment within their territory. Our empirical strategy builds upon the fact that each captaincywas returned in a different year, and we create a measure of years of private colonization,defined as the difference between the return year and the year of the first settlement. We alsoexploit the fact that borders were defined based on the coastline and restrict our sample tomunicipalities located up to 50 kilometres from the border to alleviate endogeneity concerns.Our findings suggest that longer exposure to private colonization has substantial effects in themedium run, as measured by 1920 outcomes. An additional century of exposure to privatecolonization results in 13% fewer public employees and 12.8% lower public expenditure. Asimilar pattern emerges when we examine public goods. Longer exposure to private coloniza-1tion led to fewer education workers and schools, as well as fewer doctors in 1920. While wedid observe some convergence in 2010, negative effects on health persisted over time. Collec-tively, our results corroborate the historical evidence, which suggests that captains, lookingto retain power, nominated fewer public employees than required (de Saldanha, 2001) andprioritized personal enrichment, resulting in lower investment in public goods (Augeron andVidal, 2007).The third chapter maintains the focus on the lasting effects of historical events and analyzeshow female slavery in the 19th century affected violence against black women in the 2010s. Itis known that slavery societies marginalized black women as a form to reinforce the positionof the dominant elites (Feinstein, 2018). Given the widespread violence in such societies,it is plausible to expect that this behaviour might persist over time, perpetuating violenceacross generations. Consequently, we might anticipate more cases of violence against blackwomen in areas that had a higher proportion of female slavery in 1872. However, a simplecomparison across municipalities with different shares of female slavery might lead to biasedestimates. Therefore, I explore the forced draft of male slaves for the Paraguayan War (1864-1870) as an exogenous variation and instrument the share of female slaves using distance tothe war front. The rationale is that the closer a municipality is to the war front, the greaterthe number of male slaves who are drafted to the war, leading to a higher share of femaleslaves.The IV results indicate that a 1 percentage point increase in the share of female slaves in1872 led to 33.6% more cases of violence against black women in the 2010s. The increaseseems to be driven by cases of physical and psychological violence. Importantly, we do notobserve the same pattern in cases against white women, providing additional evidence thatblack women still bear the consequences of slavery even after its abolition 130 years ago.Finally, chapter 4 focuses on another overlooked minority, namely favela residents, and es-timates jobseekers\u2019 response to expected address-based discrimination. We conduct fieldexperiments in Rio de Janeiro designed to identify how they anticipate and react to discrim-ination in the application and interview stages of the job search. Our first step consistedof a door-to-door survey in three favelas, in which we asked background questions and howmuch discrimination they expected. During the survey, we asked if they wanted to sharetheir professional details with an HR firm, created by the study\u2019s authors. The ones thatagree would be invited to apply for a position with our partner, a large cosmetics firm in Riode Janeiro.Our results indicate that application rates are unaffected by the removal of the addressrequirement and by the information that we did not find any discrimination in a previouslyconducted audit study during the application stage. However, during the interview stage,2participants\u2019 performance improved when we randomly told them that the interviewer onlyknew their names as opposed to knowing their names and addresses. Importantly, we observea positive effect when an address is not required in the application stage, and a strongereffect in the interview stage, when we restrict the sample to white applicants. One possibleinterpretation is that white job applicants feel that they can pass as non-favela residents whentheir addresses are hidden during the job search. Taken together, these findings suggest thatexpected discrimination might affect the job search.3Chapter 2Private Colonization and StateCapacity: Evidence from the BrazilianDonatary Captaincies2.1 IntroductionState capacity stands as a key driver of economic development, primarily through law enforce-ment, tax collection, and the provision of public goods (Besley and Persson, 2011; Johnsonand Koyama, 2017). Despite their importance, we observe large differences in state capacityacross different regions. For instance, Acemoglu (2005) documents that tax capacity varieslargely in the world, and usually correlates with the countries\u2019 income. Furthermore, there isalso a large inequality in the provision of public goods. Around 4 billion people have limitedaccess to health, leaving them vulnerable to shocks (Ortiz and Behrendt, 2017), whereas 258million children are out of school (Schmelkes, 2021).These economic disparities can, in part, be attributed to the historical colonization process.Some studies have shown that different periods of exposure to colonization led to distinctmodern outcomes (Feyrer and Sacerdote, 2009). Others have highlighted the different effectsof being colonized directly by a ruler from the metropolis or the colony (Iyer, 2010). However,much less has been said about the impacts of being colonized by a government agent versusby a private citizen. For example, if private individuals are seeking personal enrichment, theymight focus on short-term projects since they won\u2019t reap the rewards in the long run. Thiscould lead to different government outcomes compared to those results from colonization by apublic ruler. Hence, understanding how the nature of colonization, whether public or private,affects places over time is crucial to understanding contemporaneous regional differences.4In this chapter, we estimate the impact of private colonization on government size and publicgoods provision over time. We explore the Donatary Captaincy system implemented between1534 and 1753 in Brazil. The system split colonial Brazil into strips of land, granting juris-diction and autonomy to private citizens known as captains. These captains were responsiblefor implementing a government and fostering economic development within their captaincy.Exploiting the variation in exposure, we find that being exposed to private colonization forlonger resulted in smaller governments, measured both in terms of the number of publicemployees and public expenditure, and fewer public goods provision in health and educationin 1920. However, results indicate some convergence by 2010, although we find persistentdifferences in health-related public services and outcomes.Our argument rests on the fact that captains had nearly absolute power in their territoriesand, as private citizens, were looking to extract as much rent as possible. The historicalevidence suggests that they nominated fewer public employees than required, potentially toconserve more power (de Saldanha, 2001). Coupled with their focus on personal enrichment,this could have led to lower public expenditure and provision of public goods, especiallyconsidering implementation costs. Once a foundation of small government and limited publicgoods provision was established, this structure might have persisted over time, leading toconsistent differences in government size and public goods offerings.The empirical strategy capitalizes on two particularities of the Donatary Captaincy system.First, we explore the fact that all Donatary Captaincies were eventually returned to thePortuguese Crown. The reasons are mostly due to financial difficulties faced by the captainsor due to the death of the original grantee. We rely on this variation to create a measure ofyears of private colonization, defined as the difference between the year the captaincy wasreturned to the Crown and the year of the first settlement. Second, captaincies\u2019 borders werebased on the size of their coastline, such that each one had 50 leagues. This allows us toconsider the placement of borders plausibly exogenous. Thus, we follow Michalopoulos andPapaioannou (2013) and use state fixed effects, and control for distance to the captaincyborder and geographical variables in all models, besides restricting to municipalities locatedup to 50 kilometres from the border.The results using 1920 outcomes suggest that an additional 100 years of exposure to privatecolonization led to 12.8% fewer public employees per 1,000 inhabitants and approximately13% less public expenditure per capita. Similar trends are observed regarding education andhealth public goods. Each additional century implies a decrease of 14.2% and 12% in thenumber of education workers and schools, respectively, and 21% fewer medical doctors percapita. The results suggest that private colonization affected government outcomes even 150years after the end of the system.5Nevertheless, the impacts seem to diminish over time. When we repeated the analysis using2010 data, we observed some convergence. The effect of private colonization on the number ofpublic employees decreased to 1%, whereas public expenditure is only 2.5% smaller. Similarly,there are no significant differences in the number of public school teachers and public schools.Despite that, we still observe some persistent negative effects on health. Our findings suggestthat being exposed to an additional 100 years of private colonization led to 5.8% fewer publicdoctors, 4.8% fewer health centers and 6.5% more child mortality by 2010.We conducted a series of robustness exercises to support our findings. First, exploiting thefact that two territories were only exposed to 1 and 2 years of private colonization, whiletheir neighbours had around 180 years, we performed a regression discontinuity analysis. Theresults are similar to the ones in the main analysis, despite lacking statistical significance.Moreover, results do not change once we correct our standard errors to account for spatialcorrelation. Finally, when we estimate the effects using placebo Donatary Captaincies1 we donot find any of the results, suggesting that they are not driven by unobservable characteristicsrelated to the latitude.This article relates to various strands of the literature. We contribute to a broad literature onthe historical determinants of state capacity (Besley and Persson, 2008, 2009; Dincecco andPrado, 2012; Gennaioli and Voth, 2015) and public goods provision (Banerjee et al., 2005;Wimmer, 2016; Foa, 2022). Our work relates to Dittmar and Meisenzahl (2020), althoughwe focus on Brazil while they analyze the historical impacts on public goods provision inGerman cities. Their findings indicate that the introduction of institutional arrangements inthe 1500s led to an immediate increase in public goods provision, and these effects persistedfor over 300 years after the policy implementation, which aligns with our results.We also add to the literature that studies the long-term impact of colonial rule (Acemogluet al., 2001; Banerjee and Iyer, 2005; Feyrer and Sacerdote, 2009; Iyer, 2010; Acemogluet al., 2014; Dell and Olken, 2020). Several scholars have highlighted the impact of specificcolonial features, such as forced labour (Nunn, 2008; Dell, 2010; Nunn and Wantchekon,2011; Bertocchi and Dimico, 2014; Faguet et al., 2022; Rivadeneira, 2023; Laudares andValencia Caicedo, 2023) and institutional changes (Porta et al., 1998; Engerman and Sokoloff,2005; Huillery, 2009; Cage\u00b4 and Rueda, 2016; Lowes and Montero, 2021b), but less has beensaid about the different effect of public versus private colonization. In this sense, the closestarticle is Lowes and Montero (2021a). They find that concessions to private companies duringcolonial times led to worse health, education, and wealth outcomes in modern times in Africa.Even though private companies were allowed to freely extract natural resources, they did not1The Tordesillas Treaty divided colonial Brazil in half and assigned the right side to Portugal and the leftside to Spain. We recreated the Donatary Captaincy system, implemented on the right side, on the Spanishportion.6have jurisdiction to implement new institutions and still had to answer to a colonial power.Thus, we contribute as one of the first empirical evidence of private colonization in modernoutcomes.Lastly, we contribute to the literature that studies the Donatary captaincy system. Whilemost works focus on the description of the system (Johnson, 1972; Dutra, 1973; de Saldanha,2001; Augeron and Vidal, 2007), discussing the location of the Donatary Captaincies borders(Gallo, 2002; Cintra, 2013, 2017), and the analysis of its jurisdiction (Cabral, 2015; Feloniuk,2016), very few articles empirically analyzed the consequences of the system. To the bestof our knowledge, Mattos et al. (2012) is the only empirical work in this context. Theauthors analyze how municipalities\u2019 relative age within their captaincy (e.g. how old they arecompared to the newest municipality in that DC) affects inequality and institutional featuresin the long run. As previously mentioned, this chapter takes on a different approach andcontributes to the literature by providing the first evidence on the effect of years of exposureto private captains on the municipalities\u2019 government size and public goods provision acrossDonatary Captaincies.The rest of this chapter is structured as follows. Section 2.2 provides an overview of theDonatary Captaincy system, followed by Section 2.3, which outlines our empirical strategyand data. Section 2.4 presents the results, Section 2.5 covers the robustness checks, andfinally, Section 2.6 concludes.2.2 The Donatary Captaincy System in BrazilThe first Portuguese explorers, led by Pedro A\u00b4lvares Cabral, arrived in Brazil in April 1500.Originally, the expedition was organized with the intention of reaching India to establisha commercial relationship, following Vasco da Gama\u2019s successful route through the Cape ofGood Hope (Vianna, 1961a). However, they ultimately arrived in Brazil. Whether the detourwas intentional remains uncertain (de Holanda, 1960; Vianna, 1961a). The following yearswitnessed a number of Portuguese voyages to the colony, primarily focused on the extractionof Pau-Brasil. The tree\u2019s heartwood, from which a red dye could be extracted, coupled withits resistant wood made it highly valued in Europe. This was Brazil\u2019s first commodity export.The abundance of Pau-Brasil made the shores of Brazil attractive to other European powersdespite the Portuguese monopoly on its trade. Even though Portuguese rights to Brazil hadalready been established in 1494 in the Treaty of Tordesillas (Vianna, 1961a; Laudares andValencia Caicedo, 2023), French vessels were constantly found in Brazil from as early as 1504,increasing the frequency of visits in the subsequent years (Vianna, 1961a; de Carvalho, 2015).The Portuguese Crown attempted to safeguard its colony by patrolling Brazilian waters butfailed mostly due to the size of the coast.7During the first half of the 16th century, Portugal was facing financial difficulties. Decadesof increasing public spending, an earthquake in 1531, and the financial pressure caused bya greater naval presence in the colonies pushed the country into a financial crisis in 1532(Augeron and Vidal, 2007; de Freitas, 2015). Lacking financial resources and manpower toboth defend the territory against foreign invasions and populate it, King D. Joa\u02dco III (1502-1557) decided to replicate a system already in place on the Coast of Africa and AtlanticIslands, establishing a Donatary Captaincy system in Brazil (Johnson, 1972; de Carvalho,2015).2The system consisted of partitioning the colony into smaller territories, called DonataryCaptaincies,3 and granting each one to a private citizen. Fifteen tracts of land were created,typically going from the coastline to the vertical line set by the Treaty of Tordesillas, such thateach had 50 leagues of coastline (Augeron and Vidal, 2007) as shown Figure 2.1.4 Between1534 and 1536, King D. Joa\u02dco III, and the Minister of Finances, Anto\u00b4nio de Ata\u00b4\u0131de allocatedthe Donatary Captaincies to 12 Portuguese citizens. These appointed Captains constituteda mix of military veterans who had participated in the Indian and African campaigns, as wellas members of the royal administration closely allied with the minister (Augeron and Vidal,2007; Bueno, 1999; Dias et al., 1923). Table 2.1 presents each captain\u2019s Donatary Captaincy,the grant date, and a summary of their background.2Donatary captaincies were also introduced in Angola, Sierra Leone, Cape Verde, Sao Tome\u00b4 and Pr\u00b4\u0131ncipe,Madeira Island, and Azores (de Saldanha, 2001).3They are known as Capitanias Heredita\u00b4rias, or Hereditary Captaincies, in Portuguese4In 1530, the King assigned his advisor and Minister of Finances, Anto\u00b4nio de Ata\u00b4\u0131de with the responsibilityof organizing an expedition to thoroughly survey Brazil\u2019s shore. The analysis performed by the crew waslater used to partition the colony (Augeron and Vidal, 2007).8Figure 2.1: Map of the Donatary CaptainciesNotes: The non-colored portion located at the top on the right side of the vertical Tordesillas Line arenon-distributed lands (Cintra, 2013). Each color represents a distinct Donatary Captaincy.Each captain and their heirs were granted jurisdiction and autonomy over the land for theirlifetimes, becoming responsible for the organization of a local government, the implementa-tion of a justice system, and collecting taxes to finance it, as described in their Carta Foral(de Carvalho, 2015).5 Despite the Crown specifying the positions that needed to be filledwithin the Donatary Captaincy government, the captain retained the freedom to determinethe number of officers appointed to each position and whether to create new ones, as wellas set their wages. However, they constantly opted not to appoint officials to every positionand had other public workers accumulate offices in order to retain more power (de Saldanha,2001).Given the persistent threat of foreign invasions, the beneficiaries were also responsible forthe military defence of the territory and populating the region. Captains were requiredto grant out part of the lands, known as sesmarias, to incentivize occupation and economicdevelopment. This was an occupation right, rather than a proprietary one, meaning that theycould only sell or donate the land with the captain\u2019s consent. One important feature is thatthe Crown\u2019s donation letters had legal provisions designed to prevent excessive concentrationof land. For example, Captains were prohibited from granting sesmarias to immediate familymembers (de Saldanha, 2001) or allocating more than 20% of the land to a single individual(Augeron and Vidal, 2007).5The Carta Foral, or Foral Letter, along with the Donation Letter set the rights and duties of eachcaptain, as well as the geographical limits of their territory (de Saldanha, 2001).9Despite the fact that the Crown still retained the trade monopoly over Pau-Brasil and thatCaptains were required to pay a 20% D\u0131\u00b4zimo tax to the Crown, local leaders had full authorityand control over the land (Augeron and Vidal, 2007). There were no royal officials in theDonatary Captaincies, Captains possessed the right to overturn criminal and civil decisions,and no one, apart from nobles, was allowed to appeal a decision made by a captain-appointedjudge in a royal court in Portugal (de Saldanha, 2001; Augeron and Vidal, 2007). Thewidespread use of violence, abuses of power, and disregard for the Crown\u2019s rules were recurringfeatures of their governance, resulting in their widely recognized status as absolutist rulersby members of the Crown (de Saldanha, 2001). This is exemplified in a letter sent to thePortuguese King, in the early 17th century, stating that \u201cDonataries, Bishops, and powerfulproceed in everything with absolute power and Your Majesty is King only in name\u201d.6Complete territorial control also entailed that the extensive financial obligations had to bemet solely by the captain (de Carvalho, 2015). Prior to coming to Brazil, Captains hadto find financiers, sell assets, and assemble a group of individuals willing to live in thecolony to amass sufficient resources to initiate the colonization process. For instance, VascoFernandes Coutinho and Pero do Campo Tourinho liquidated all their assets before embarkingto Brazil (Augeron and Vidal, 2007). In addition to the financial efforts, which remainedconstant through the years, the extensive territory of the DCs (some larger than Portugal),coupled with the distance to markets, posed significant challenges to the colonization process(de Carvalho, 2015).Some Captains were unable to deal with these challenges and decided to sell their DonataryCaptaincies back to the Crown. Faced with this situation, Portugal gradually started theprocess of reincorporating the territories. In 1549, the captain of Bahia, Francisco PereiraCoutinho, passed away, leaving the captaincy to his heirs. When they decided to sell it, theCrown repurchased it and established there the first royal captaincy (Augeron and Vidal,2007). The captaincy of Sa\u02dco Vicente 1 was also incorporated in 1569. Martim Afonsoreturned it to the Crown likely due to the persistent incursions of French explorers (Augeronand Vidal, 2007), and in 1619, Sa\u02dco Tome\u00b4 was repurchased by the Crown from the heirs ofPe\u02c6ro de Gois after his death.Once captaincies were reincorporated, the Crown appointed a royal employee as their gov-ernor. The assigned official would become responsible for implementing a new governmentstructure that was both more complete and cohesive compared to those established by pri-vate captains (Kahn, 1972). The organization of the captaincies adhered to the Ordenac\u00b8o\u02dcesManuelinas, a set of political and judicial procedures developed by King Manuel I to ad-6\u201cOs Bispos, Donata\u00b4rios e poderosos, procedendo em tudo com poder absolute e Sua Majestade ficaso\u00b4 Rei em nome ...\u201d, Biblioteca Nacional de Lisboa, Colecc\u00b8a\u02dco Pombalina, number 674, sheet 69. Authors\u2019translation.10equate the colonies to the metropolis, aiming for greater unity (Gama, 2011; Costa et al.,2011). Moreover, the Portuguese Crown facilitated the colonization process in royal cap-taincies by providing financial support, goods and labour, suspending tax collection for adesignated period, and assisting in the defence of the territory (de Abreu, 1930). It is impor-tant to note that, despite the establishment of royal captaincies and the presence of a generalgovernor responsible for the administration of royal lands, private Captains kept operatingindependently until their territory was incorporated (de Carvalho, 2015).It was not until the latter half of the 17th century that the criticisms of the system gained mo-mentum among the members of the Crown. Some argued that private Donatary Captaincieswere fairing worse than Royal captaincies (de Saldanha, 2001), while others voiced concernsabout the Captains\u2019 inability to prevent foreign invasions (Augeron and Vidal, 2007). Facedwith this pressure, the Portuguese Crown, under the leadership of Marque\u02c6s de Pombal, initi-ated the process of dismantling the system (Carrara, 2016). By the latter half of 18th century,all the Donatary Captaincies had been bought back or confiscated and reintegrated into thedomain of the Portuguese Crown.77Table 2.2 presents the incorporation dates and process on each Donatary Captaincy.11Captain Donatary Captaincy Grant Date BackgroundMartim Afonso de Sousa Sa\u02dco Vicente 1 and Sa\u02dco Vicente 2 06\/10\/1534 Cousin of the Vedor da Fazenda, Antoniode AtaidePe\u02c6ro Lopes de Sousa Santo Amaro, Santana, and Itamaraca\u00b4 01\/09\/1534 Cousin of the Vedor da Fazenda, Antoniode AtaidePe\u02c6ro de Gois Sa\u02dco Tome\u00b4 28\/01\/1536 Captain the surveying expeditionVasco Coutinho Fernandes Esp\u00b4\u0131rito Santo 01\/06\/1534 Military that participated in Africa cam-paignPe\u02c6ro do Campo Tourinho Porto Seguro 27\/05\/1534 Military that participated in India cam-paignJorge Figueiredo Correia Ilhe\u00b4us 26\/07\/1534 Secretary of the Royal TreasuryFrancisco Pereira Coutinho Bahia 05\/04\/1534 Military that participated in India cam-paignDuarte Coelho Pereira Pernambuco 10\/03\/1534 Military that participated in the con-quest of Malaga in 1511Joa\u02dco de Barros e Aires da Cunha Rio Grande do Norte and Piau\u00b4\u0131 08\/03\/1535 Treasurer of Casa da India (Joa\u02dco) andmember of the first expedition to Brasilin 1500 (Aires)Antonio Cardo\u00b4so de Barros Ceara\u00b4 19\/11\/1535 Purveyor general (provedor-geral) of fi-nancesFerna\u02dco A\u00b4lvares de Andrade Maranha\u02dco Unknown Treasurer general of the realmNotes: Joa\u02dco de Barros and Aires da Cunha received two territories to split among them.Source: Augeron and Vidal (2007), Cintra (2013), and de Saldanha (2001)Table 2.1: Captains, Grant Date, and Background122.3 Empirical Strategy and Data2.3.1 Empirical StrategyThe process of reincorporation of the Donatary Captaincies by the Portuguese Crown startedas early as 1548 and continued until 1761. Most of the Captains opted to sell their territoriesdue to the financial burden associated with developing and populating the region (de Sal-danha, 2001; de Carvalho, 2015). For instance, in Sa\u02dco Tome\u00b4, Bahia, and Santo Amaro, theheirs decided to sell the Captaincy back to the Crown after the death of the captain (Augeronand Vidal, 2007; Vianna, 1961b). However, there were exceptions such as Pernambuco, ac-quired by the Crown in a legal settlement where an illegitimate son of the captain claimed theterritorial rights, Sa\u02dco Vicente 1, ceded due to the French invasions, and Ilhe\u00b4us, confiscatedfollowing allegations of the captain plotting against the king (de Saldanha, 2001; Augeronand Vidal, 2007).Motivated by this historical account, we explore the timing each Donatary Captaincy wasreturned to the Crown and construct a measure of the number of years under private col-onization. Years of Private Colonization is defined as the difference between the year thecaptaincy was returned to the Crown and the year that the first settlement was establishedfor each territory after the donation. Table 2.2 outlines the year of the first settlement, theyear that it was returned to the Crown, and describes the reincorporation processes for eachcaptaincy analyzed.8Our aim is to assess the impact of an additional year of private colonization on the state ca-pacity of Brazilian municipalities. The first step is to match each municipality to a DonataryCaptaincy based on the location of the modern municipality\u2019s centroid. We then proceed toestimate the following equation:Yijst = \u03b20 + \u03b21Years of Private Colonizationj + \u03b3Border Distijs + \u039b\u2032Zijst + \u03b1s + uijt (2.1)Yijst are the state capacity and public goods outcomes, both in 1920 and 2010, for municipalityi, that was located in the territory of Donatary Captaincy j, in the state s, for the year t.Years of Private Colonizationj is the number of years under private colonization in captaincyj, Border Dist ijs is the distance to the closest captaincy border for each municipality, andZijst is a vector of geographical controls including longitude, latitude, altitude, distance to thecoast, sunlight incidence, and rainfall for each municipality. Finally, following Michalopoulos8As explained in section 2.3.2, we excluded the northern captaincies due to unclear boundaries.13and Papaioannou (2013), we use state fixed effects \u03b1s to control for any policy variation atthe state level, leading to within-state estimates.9It is possible that some unobservable geographical characteristics could affect both the du-ration of the private colonization period and the state capacity outcomes, possibly resultingin biased estimates. We address this concern by restricting our sample to municipalities thatfall within 50 kilometres from each side of the border, following Michalopoulos and Papaioan-nou (2013). The idea is that the exact location of the border was defined such that eachDonatary Captancy had 50 leagues of coastline, as described in section 2.2. Consequently, byrestricting our analysis to locations near the border, we can presume that each municipalitywas arbitrarily situated within a specific Donatary Captaincy.2.3.2 SampleHistorically, there was a consensus that all Donatary Captaincies borders were horizontal,going for the coastline up to the vertical line defined in the Tordesillas Treaty (1494). Thisinterpretation was initially influenced by the 1586 historical map drawn by Lu\u00b4\u0131s Teixeira(da Mota and Cortesa\u02dco, 1960), which gained acceptance among various authors over time(Varnhagen, 1854; Marchant, 1943; de Holanda, 1960). The wide acknowledgment of thisinterpretation led to its adoption in school textbooks, as can be seen in the map extractfrom the Ministry of Education textbook in Figure 2.2a. Lu\u00b4\u0131s Teixeira\u2019s historical map ispresented in Figure 2.2b.9Figure A.1 presents the intersection between Donatary Captaincies historical boundaries and the 1920state boundaries (panel A), and 2010 state boundaries (panel B). It is important to note that, although4 states were created between 1920 and 2010, state boundaries are unchanged for all municipalities in oursample, with the exception of 73. Those municipalities were located in the state of Goia\u00b4s in 1920 and becamea part of Tocantins in 2010.14(a) Textbook Map (1977) (b) Historical Map (1586)Notes: Panel A presents the map drawn by Lu\u00b4\u0131s Teixeira in 1586, located in da Mota and Cortesa\u02dco (1960),and Panel B shows the map found in the Ministry of Education textbook (Albuquerque et al., 1977).Figure 2.2: Donatary Captaincies - Horizontal BordersHowever, there is a growing literature suggesting that the historical borders are not accurate.Contrary to the established belief, the borders were actually vertical for the captaincieslocated in the North, and slightly different for two territories in the South (Gallo, 2002;Cintra, 2013, 2017), as shown in Figure 2.3a. The revised interpretation is supported by theanalysis of the donation letters, the Cartas Forais, and the mining charters of each captain.Despite that, the exact location of some Northern boundaries is still unclear. For instance,boundaries between Maranha\u02dco 1 and Maranha\u02dco 2 were not clearly defined in their donationletters, akin to Rio Grande do Norte. Therefore, we excluded the Northern captaincies fromour analysis, and focused on the Central and Southern captaincies, as shown by the paintedareas in Figure 2.3b.15(a) Cintra (2013) (b) Analysis SampleNotes: The map from Cintra (2013) is shown in Panel A. Panel B shows the sample map, where paintedmunicipalities are included in the analysis.Figure 2.3: Donatary Captaincies - New Boundaries16Donatary Captaincy First Settlement Returned to Crown Reincorporation ProcessSantana 1549 1709 After the death of Pe\u02c6ro Lopes de Sousa, the heirs to MartimAfonso, his brother, also inherited Santana and Santo Amaro.They decided to sell the captaincies to another private citizen afterfacing financial difficulties. However, the Crown, facing pressurefrom members of the royal administration, decided to interveneand purchase the captaincy at the same price.Sa\u02dco Vicente 2 1536 1709Santo Amaro 1536 1709Sa\u02dco Vicente 1 1565 1567 The captain decided to return the captaincy to the Crown due to con-stant French invasions.Sa\u02dco Tome\u00b4 1540 1619 In face of the great financial effort required to develop a captaincy, theson of Pe\u02c6ro de Gois, Gil de Gois, decided to sell the captaincy to thecrown.Esp\u00b4\u0131rito Santo 1535 1715 The Crown bought the captaincy back after extensive negotiations. Themotivation behind the negotiation is unclear, but it was conducted bya private citizen who had previously bought the place from the originalheirs.Porto Seguro 1535 1761 The captaincy was confiscated after the captain was accused of tryingto kill the King.Ilhe\u00b4us 1536 1753 Marques de Pombal, having access to public money that the Crown didnot have before, decided to acquire it. It is unclear why the captaindecided to sell it.Bahia 1548 1549 After the captain\u2019s death, his heirs were not interested in staying inBrazil. The solution was to sell the captaincy back to the Crown.Pernambuco 1537 1716 The captaincy was returned to the Crown after a judicial battle betweenthe Crown and a claiming heir, the illegitimate son of the previouscaptain, in exchange for nobility titles and financial compensationItamaraca\u00b4 1585 1753 Marques de Pombal, having access to public money that the Crown didnot have before, decided to acquire it. It is unclear why the captaindecided to sell it.Notes: We excluded the northern captaincies due to unclear boundaries. More details are in section 2.3.2.Source: Vianna (1961b), Augeron and Vidal (2007), Cintra (2013), and de Saldanha (2001)Table 2.2: Captains, Grant Date, and Background172.3.3 Balance TestA potential threat to our empirical strategy stems from the possibility that municipalitiesin different Captaincies might possess distinct geographical characteristics. Such variationcould potentially confound our estimated effects if these features correlate with our measure ofprivate colonization. To address this, we estimate equation 1 to examine potential differencesacross municipalities using a set of land suitability measures and geographical attributes.Results are reported in Tables A.2 and A.3.Although we find no statistical distinctions in terms of slope and proximity to rivers, weobserve a significant difference in rainfall and sunlight among municipalities. Nevertheless,they are economically small, suggesting that places with 100 years more of private colonizationhave 0.6% less sunlight and 4.0% less rainfall. Furthermore, the geographical differences donot translate into differences in suitability, a critical aspect considering the predominant roleof agriculture and extractivism during this period (Vianna, 1961a; de Carvalho, 2015). Oncethe sample is restricted to municipalities located up to 50 kilometres from the border, weobserve that point estimates are not statistically significant and have a small magnitude acrossfive suitability measures.10 In summary, our findings suggest that there are no significantgeographical differences across municipalities, especially once we focus on those close to theborder.2.3.4 DataThe analysis uses four distinct sets of data. First, we build upon several historical sources(de Holanda, 1960; Vianna, 1961b; de Saldanha, 2001; Augeron and Vidal, 2007; Cintra, 2013)to construct our measure of years of private colonization. On average, Brazilian municipalitiesexperienced 132 years under private colonization, spanning from 1 to 226 years. Figure A.2illustrates its geographical distribution.The second set encompasses 1920 outcomes, which is the first year with available data on mu-nicipalities\u2019 public finance and public goods provision.11 The data on educational and healthoutcomes, Land Gini index,12 the count of public employees, and demographic characteristicssourced from the 1920 Brazilian Census. Fiscal outcomes come from the 1926 Estat\u00b4\u0131stica dasFinanc\u00b8as do Brazil, which has digitized data on municipalities\u2019 public expenditure, decom-10Results suggest that an additional 100 years of private colonization is associated with a less than 2%difference in suitability, except for sugar, where we observe a 3.8% difference.11To maintain the same unit of observation across different periods, we map the 2010 municipalities intothose in 1920. Thus, if two municipalities in 2010 coincide with the location of one municipality in 1920, weassign the 1920 value to both 2010 municipalities. Since all outcomes are measured in per capita terms, theunderlying hypothesis of this approach is that those outcomes are uniformly distributed across the territory,as done by Hornbeck (2010); Maloney and Valencia Caicedo (2022)12This measure was constructed using the number of farms and average size in each of the 11 land sizecategories found in the Census18posed by expenditure category.We rely on 2010 data as our modern outcomes. Public goods provision data comes froma variety of sources, including Sinopse Estatist\u00b4\u0131ca da Educac\u00b8a\u02dco Ba\u00b4sica from the Ministryof Education, DataSUS from the Health Ministry, and IBGE. The public finance data formunicipalities comes from FINBRA, organized by Brazil\u2019s National Treasury. Lastly, geo-graphical characteristics are sourced from the IBGE, with additional suitability data acquiredfrom EMBRAPA.Table A.1 outlines the summary statistics for two distinct groups of municipalities: \u201cLowExposure\u201d, denoting those with years of exposure to private colonization below the median(179 years), and \u201cHigh Exposure\u201d, for those equal or above. The analysis of the raw dataindicates that municipalities subjected to private colonization had fewer public administra-tors, education workers, schools, and medical doctors in the 1920s, alongside lower publicexpenditure compared to places with low exposure to private colonization. However, thesedifferences diminish significantly when we repeat the analysis using the same outcomes in2010. Notably, in the case of public school teachers, we observe a reversal from the 1920s pat-tern, with more teachers in privately colonized municipalities compared to publicly colonizedones. At the same time, we do not observe significant differences in terms of geographicalattributes.2.4 Results2.4.1 1920 ResultsThe historical analysis reveals that the Captains wielded nearly absolute power in their Do-natary Captaincy, often resisting sharing authority with other public officials. They oftenappointed fewer officials than required by the Portuguese Crown (de Saldanha, 2001). More-over, they were responsible for the public expenditures in their territory, a financial burdenthat several Captains struggled to meet (de Carvalho, 2015). Given this context, it is possiblethat both a smaller government and lower public expenditure might have persisted acrossthe years in privately colonized areas. We investigate this by estimating equation 1 using1920 data on government and public expenditure.13Our quantitative evidence is shown in Table 2.3 and supports this interpretation. They indi-cate that an additional 100 years of private colonization led to 12.8% fewer public employeesper 1,000 inhabitants by 1920. Moreover, municipalities with greater exposure to privatecolonization spent between 8.7% and 12.8% less on public expenditure per capita compared13This represents the oldest available data for the number of public employees and public expenditure atthe municipal level.19to less exposed municipalities within the same state. This reduction seems to be driven bylower public expenditure in education, between 16% and 29% less, and, on a smaller scale,by lower expenditure in health, although the point estimates are not statistically significant.Notably, the municipal population size in 1920 is not statistically different across observa-tions (Table A.4). These findings suggest that smaller governments, measured by the numberof employees and public expenditure, persisted for at least 150 years in privately colonizedmunicipalities.(1) (2) (3) (4)Dependent Variable:Municipal PublicEmployees per 1,000ln(Public Expenditureper capita)ln(Public Expenditure inEducation per capita)ln(Public Expenditure inHealth per capita)Panel A: Whole SampleYears of Private -0.0590*** -0.0869* -0.168** -0.114Colonization (in 100 years) (0.0102) (0.0465) (0.0794) (0.0877)Observations 2,619 2,342 1,657 1,713R-squared 0.279 0.523 0.281 0.342Mean Dep. Var. 0.398 0.636 -2.251 -2.695Panel B: Up to 50km of the borderYears of Private -0.0499** -0.128** -0.296*** -0.0428Colonization (in 100 years) (0.0226) (0.0519) (0.0873) (0.103)Observations 1,495 1,327 960 986R-squared 0.355 0.535 0.331 0.383Mean Dep. Var. 0.391 0.689 -2.177 -2.597Notes: All specifications include state fixed effects, and control for the distance to the border and a set ofgeographical variables including longitude, latitude, altitude, distance to the coast, sunlight incidence, andrainfall. Clustered standard errors at the 1920 municipality level are reported in parentheses. ***, **, and *indicate significance at the 1, 5, and 10 percent levels.Table 2.3: Government Size and Public Expenditure in 1920We established that private colonized municipalities spent less and had fewer public em-ployees in the 1920. Given that, the next step is analyzing whether it also impacted theprovision of public goods. Our estimates in Table 2.4 indicate that an additional 100 yearsof private colonization translates into 14.2% fewer education workers, mostly teachers, and12% fewer schools per 1,000 inhabitants, although this estimate is not statistically signifi-cant. Nevertheless, this negative impact on the educational inputs does not translate intoworse educational outcomes. As observed in Column 3, the estimates for literacy rate arenot statistically significant and are small in magnitude, suggesting a negative effect of 3%.20Regarding health-related inputs, we also observed a negative impact. Municipalities have 21%fewer medical doctors per 1,000 inhabitants when exposed to private colonization. Unfortu-nately, the unavailability of 1920 data on mortality hinders the analysis of health outcomes.(1) (2) (3) (4)Dependent Variable:Education Workersper 1,000 inhabitansSchools per 1,000inhabitantsLiteracy RateMedical Doctorsper 1,000 inhabitantsPanel A: Whole SampleYears of Private -0.160*** -0.0144*** -0.00500 -0.142***Colonization (in 100 years) (0.0446) (0.00551) (0.00373) (0.0290)Observations 2,619 2,619 2,619 2,619R-squared 0.405 0.279 0.364 0.461Mean Dep. Var. 1.059 0.107 0.180 0.700Panel B: Up to 50km of the borderYears of Private -0.153** -0.0120 -0.00598 -0.148***Colonization (in 100 years) (0.0659) (0.00830) (0.00502) (0.0377)Observations 1,495 1,495 1,495 1,495R-squared 0.403 0.274 0.370 0.488Mean Dep. Var. 1.076 0.101 0.179 0.696Notes: All specifications include state fixed effects, and control for the distance to the border and a set ofgeographical variables including longitude, latitude, altitude, distance to the coast, sunlight incidence, andrainfall. Clustered standard errors at the 1920 municipality level are reported in parentheses. ***, **, and *indicate significance at the 1, 5, and 10 percent levels.Table 2.4: Public Goods Provision in 1920Lastly, we shift our focus to GDP per capita and land inequality. Given that Captains wereprivate citizens seeking personal enrichment from their colonial endeavour (Augeron andVidal, 2007), one could expect that municipalities in their captaincies were more economicallydeveloped, in terms of GDP per capita, despite neglecting the provision of public goods.However, the results in Column 1, Table 2.5, suggest a different conclusion. Private colonizedmunicipalities had a 7% lower GDP per capita in 1920. At the same time, these municipalitiesdo not exhibit higher land concentration as indicated by the land Gini index in column 2.This suggests that, as discussed in section 2.2, provisions outlined in the donation letters ofthe captaincies indeed prevented an excessive land concentration.21(1) (2)Dependent Variable:ln(GDP per capita) Land GiniPanel A: Whole SampleYears of Private Colonization (in 100 years) -0.0733** -0.0116*(0.0316) (0.00680)Observations 2,362 2,599R-squared 0.511 0.319Mean Dep. Var. -0.679 0.605Panel B: Up to 50km of the borderYears of Private Colonization (in 100 years) -0.0803** -0.0102(0.0335) (0.00760)Observations 1,336 1,479R-squared 0.532 0.312Mean Dep. Var. -0.671 0.614Notes: All specifications include state fixed effects, and control for the distance to the border and a set ofgeographical variables including longitude, latitude, altitude, distance to the coast, sunlight incidence, andrainfall. Clustered standard errors at the 1920 municipality level are reported in parentheses. ***, **, and *indicate significance at the 1, 5, and 10 percent levels.Table 2.5: GDP and Land Inequality in 19202.4.2 2010 ResultsWe provided evidence that municipalities in privately colonized areas had a smaller gov-ernment, measured by the number of public employees and public spending, lower publicgoods provision and lower GDP per capita in 1920. Naturally, this raises the question ofwhether those impacts persist in the modern period. Thus, we repeat the previous exerciseand analyze how private colonization affected municipalities using 2010 outcomes.The results in Table 2.6 indicate some convergence across municipalities in publicly and pri-vately colonized areas. The negative estimates for the number of public employees (Column1) and public expenditure (Column 2) suggest that, although they still have a smaller gov-ernment, the difference went from 13% to 1% in the number of employees, and from 13%to 2.5% in public expenditure. Similarly, we do not observe significant differences in publicexpenditure on education and health.22(1) (2) (3) (4)Dependent Variable:Municipal PublicEmployees per 1,000ln(Current Expenditureper capita)ln(Public Expenditure inEducation per capita)ln(Public Expenditure inHealth per capita)Panel A: Whole SampleYears of Private -0.341 -0.0184* 0.00178 0.00492Colonization (in 100 years) (0.548) (0.00938) (0.0103) (0.0147)Observations 2,618 2,596 2,592 2,586R-squared 0.102 0.152 0.128 0.169Mean Dep. Var. 49.68 6.856 6.198 5.892Panel B: Up to 50km of the borderYears of Private -0.477 -0.0241* 0.00532 0.0280Colonization (in 100 years) (0.707) (0.0124) (0.0148) (0.0227)Observations 1,494 1,486 1,483 1,478R-squared 0.157 0.191 0.135 0.134Mean Dep. Var. 49.59 6.845 6.198 5.865Notes: All specifications include state fixed effects, and control for the distance to the border and a set ofgeographical variables including longitude, latitude, altitude, distance to the coast, sunlight incidence, andrainfall. Robust standard errors are reported in parentheses. ***, **, and * indicate significance at the 1, 5,and 10 percent levels.Table 2.6: Government Size and Public Expenditure in 2010As a consequence, one would anticipate that the distinction in public goods provision wouldalso disappear in 2010. This appears to be true for education, as evidenced in the firstthree columns of Table 2.7. The estimate for the number of public school teachers is nolonger statistically significant, whereas the number of public schools is in fact higher formunicipalities more exposed to private colonization. Despite being significant, the pointestimate for literacy rate is small in magnitude, suggesting that 100 more years of privatecolonization leads to a mere 1% lower literacy rate.Despite the convergence in public health expenditure, persistent differences in health publicgoods were observed in 2010. Columns 4 to 6 suggest that an additional 100 years of exposureto private colonization led to 5.8% fewer medical doctors in the public service (SUS)14 and4.8% health centers per 10,000 inhabitants.15 The negative impact on health inputs alsotranslates into worse health outcomes, with a 6.5% increase in child mortality for every 10014SUS is the Sistema U\u00b4nico de Sau\u00b4de, the public health system in Brazil.15We do not observe the same difference when we analyze non-SUS medical doctors, as shown in TableA.5.23years of private colonization. Even though the difference in medical doctors decreased from21% in 1920 to 5.8% in 2010, the results indicate a persistent effect on public health evenafter 250 years of the Donatary Captaincy system.These findings are consistent with previous results in the literature, which has documenteda growing convergence in education and health-related public goods, and a reduction in in-equality in public spending between Brazilian municipalities over time (Freitas and Cabral,2012; Monteiro Neto, 2014; de Almeida et al., 2021). A plausible explanation lies in the sub-stantial increase in federal transfers to municipalities, complemented by the implementationof social programs, especially in the period following the institution of the 1988 constitutionthat reinstated federalism in the country (Arretche, 2002; Lustig et al., 2013; de Almeidaet al., 2021). The additional funds provided by the federal government allowed municipali-ties with a history of private colonization to narrow the gap with publicly colonized ones interms of both public spending and the provision of public goods.(1) (2) (3) (4) (5) (6)Dependent Variable:Public School Teachersper 1,000 inhabitansPublic Schools per1,000 inhabitantsLiteracy RateSUS Medical Doctorsper 1,000 inhabitantsHealth Centersper 10,000 inhabitantsChild Mortalityper 10,000 inhabitantsPanel A: Whole SampleYears of Private 0.0951 0.0472* -0.0110*** -0.113*** -0.256*** 0.0697Colonization (in 100 years) (0.0860) (0.0243) (0.00140) (0.0235) (0.0894) (0.0509)Observations 2,625 2,625 2,625 2,625 2,615 2,624R-squared 0.244 0.389 0.755 0.273 0.181 0.074Mean Dep. Var. 12.51 1.603 0.822 1.534 5.248 2.148Panel B: Up to 50km of the borderYears of Private 0.135 0.0616* -0.00849*** -0.0889*** -0.257** 0.138**Colonization (in 100 years) (0.115) (0.0335) (0.00187) (0.0324) (0.117) (0.0634)Observations 1,499 1,499 1,499 1,499 1,496 1,498R-squared 0.304 0.435 0.753 0.253 0.233 0.053Mean Dep. Var. 12.70 1.659 0.818 1.531 5.356 2.130Notes: All specifications include state fixed effects, and control for the distance to the border and a set ofgeographical variables including longitude, latitude, altitude, distance to the coast, sunlight incidence, andrainfall. Robust standard errors are reported in parentheses. ***, **, and * indicate significance at the 1, 5,and 10 percent levels.Table 2.7: Public Goods Provision in 2010Finally, although we observed a lower GDP per capita in 1920 due to private colonization,that difference vanished when we repeated the analysis using the 2010 GDP per capita.Table 2.8 shows that the difference, once around 7% in 1920, vanished in 2010, becomingstatistically non-significant. The results for land concentration are similar to the estimate for241920, suggesting that private colonization did not lead to a higher land concentration eitherin 1920 or 2010.(1) (2)Dependent Variable:ln(GDP per capita) Land GiniPanel A: Whole SampleYears of Private Colonization (in 100 years) 0.0162 -0.00719***(0.0142) (0.00241)Observations 2,625 2,393R-squared 0.482 0.127Mean Dep. Var. 9.011 0.814Panel B: Up to 50km of the borderYears of Private Colonization (in 100 years) -0.00400 -0.00428(0.0192) (0.00359)Observations 1,499 1,355R-squared 0.495 0.147Mean Dep. Var. 9.017 0.813Notes: All specifications include state fixed effects, and control for the distance to the border and a set ofgeographical variables including longitude, latitude, altitude, distance to the coast, sunlight incidence, andrainfall. Robust standard errors are reported in parentheses. ***, **, and * indicate significance at the 1, 5,and 10 percent levels..Table 2.8: GDP and Land Inequality in 20102.5 Robustness ChecksWe conducted three sets of robustness exercises to check our findings in the previous section.Our initial check is a case study focused on two Donatary Captaincies that underwent 1 and2 years of private colonization. Employing a regression discontinuity design, we comparedthe outcomes in these regions against neighbouring territories that, on average, experiencedaround 180 years of private colonization. The second set replicates our main exercises whileadjusting standard errors to account for spatial correlation following Conley (1999) for variouscutoff distances. Additionally, we also used a non-linear measure of private colonization tocheck the robustness of the results. Our third and final analysis creates placebo DonataryCaptaincies on the west side of Tordesillas and re-estimates the results. The goal is to check25if any unobservable characteristics, correlated with latitude, could explain our main results.162.5.1 Regression Discontinuity AnalysisGiven that two captaincies, Bahia and Sa\u02dco Vicente 1, have only 1 and 2 years of private colo-nization respectively, we explore this setting and conduct a regression discontinuity analysis.The aim is to compare these territories to their neighbours Pernambuco (179 years of privatecolonization), Ilhe\u00b4us (217 years), Esp\u00b4\u0131rito Santo (180 years), and Santo Amaro (173 years)and estimate the extensive margin impact of exposure to a private colonizer.Figure 2.4: Donatary Captaincies: Private and Public ColonizationNotes: The green areas are privately colonized captaincies, and the pink areas are the public colonizedones.Employing a standard regression discontinuity approach with distance to a privately colonizedcaptaincy as the running variable, we analyzed 1920 and 2010 outcomes. Based on Figure 2.4,this means that we estimated the impact of moving from a publicly colonized region (pinkareas) to a privately colonized one (green areas). Following Michalopoulos and Papaioannou(2013) \u201cthick borders\u201d, and a Donut RD approach implemented by Barreca et al. (2011)and Lowes and Montero (2021a), we used a 5-kilometre buffer around the border to excludemunicipalities located on top of the frontier and restrict the sample to municipalities locatedup to 200 kilometres from it.16For the ease of exposure, we repeated the analysis using a limited number of outcomes. Results for theremaining measures are available upon request.26Results using 1920 outcomes are reported in Figure 2.5 and are similar to the ones in the pre-vious analysis. Although not statistically significant, the estimates suggest fewer municipalemployees, education workers, and medical doctors in areas subjected to private colonization.However, we do not find the same effect in terms of public expenditure, which displays a nullresult in Figure 2.5b.(a) Municipal Public Employees (1920) (b) ln(Total Expenditure per capita) in 1920(c) Education Workers (1920) (d) Medical Doctors (1920)Each graph displays regression discontinuity estimates using the distance to the border of a private colonizedcaptaincy, measured in kilometres, as the running variable. Each marker represents the local average of theoutcome variable, and the continuous line is a quadratic fit with a 95% confidence interval. We restrict thesample to municipalities whose centroid is located between 5 and 200 kilometres from the border. Municipalpublic employees, education workers, and medical doctors are measured per 1,000 inhabitants, whereas totalexpenditure is in per capita terms.Figure 2.5: 1920 OutcomesSimilarly, the modern time analysis mirrors the previous results. It appears that there wasa convergence in the number of public employees and public school teachers. At the sametime, we observe the same negative estimates for public expenditure, number of SUS med-ical doctors, health centers, and child mortality, despite the lack of statistical significance.Cumulatively, the results suggest that having a private colonial administration led to smallergovernments and lower public goods provision in 1920. In 2010, while we observe someevidence of convergence, persistent differences in health outcomes endure.27(a) Municipal Public Employees (2010) (b) ln(Current Expenditure per capita) in 2010(c) Public School Teachers (2010) (d) SUS Doctors (2010)(e) Health Centers (2010) (f) Child Mortality (2010)Each graph displays regression discontinuity estimates using the distance to the border of a private colonizedcaptaincy, measured in kilometres, as the running variable. Each marker represents the local average of theoutcome variable, and the continuous line is a quadratic fit with a 95% confidence interval. We restrictthe sample to municipalities whose centroid is located between 5 and 200 kms from the border. Municipalpublic employees, public school teachers, and SUS medical doctors are measured per 1,000 inhabitants, healthcenters and child mortality are measured per 10,000 inhabitants, whereas current expenditure is in per capitaterms.Figure 2.6: 2010 Outcomes2.5.2 Spatial Correlation and Non-LinearityIt is known that standard errors might be underestimated if spatial correlation is overlooked(Conley and Molinari, 2007). This scenario occurs when two geographically close municipal-ities are very similar, contributing minimally to the estimate precision while decreasing themagnitude of the standard errors due to an increase in sample size. We address these con-cerns by estimating our main equation using Conley (1999) adjustment for standard errors.Since there is no standard procedure to select the distance cutoffs, we estimate it using 6different distances. The results, presented in Tables A.6 and A.7, show that most results are28robust to that adjustment, except for our measure of public expenditure in 1920.Another important aspect stems from the assumption of linearity in our main analysis. Al-though intuitive, we cannot rule out the possibility that the impact stemming from years ofprivate colonization is non-linear. Thus, we tested that by creating a dummy variable forPrivate Colonization. It is equal to 1 if the municipality was exposed to private colonizationfor 179 years (the median in our sample) or more, and 0 otherwise. The results, detailed inTables A.8 and A.9, reveal that most estimates are similar to those found in Section 2.4.2.5.3 Placebo Donatary CaptainciesAs previously discussed, colonial Brazil was divided into two halves following the Treaty ofTordesillas (1494). The west side was assigned to Spain, while the east side, was assignedto Portugal and divided into Donatary Captaincies. In our final robustness exercise, weconstructed artificial Donatary Captaincies on the Spanish side of the Tordesillas line, asillustrated in Figure 2.7. We assigned the same number of years of private colonization as theirPortuguese-side counterparties and re-estimate equation 1. If unobservable characteristicscorrelated with latitude are driving the results, we would anticipate similar estimates tothose observed on the right side of the Tordesillas line. Conversely, divergent results wouldsuggest that those features are not the primary drivers of the effects unearthed in Section2.2.Figure 2.7: Placebo Donatary CaptainciesNotes: Each coloured area represents a distinct Placebo DC.29Table 2.9 provides evidence that unobservable characteristics are unlikely to be the maindriver of the results. We do not observe differences in the number of public employees andmedical doctors between municipalities in our placebo captaincies. The number of educationworkers is, in fact, larger for our placebo DCs with higher years of private colonization.Results on public expenditure are actually similar to those found in the main analysis, whichcould suggest that this effect is less robust.Results using 2010 data led to the same conclusion. Most estimates flip their sign once werestrict to municipalities closer to the border, which was not observed in the main analysis.Furthermore, unlike the main findings, we did not observe a negative and statistically sig-nificant difference in health outcomes. For instance, we showed that the number of healthcenters is larger for placebo DCs exposed to lengthier periods of private colonization. Bothtables suggest that unobservables are unlikely to be the primary drivers of our main findings.(1) (2) (3) (4)Dependent Variable:Municipal PublicEmployees per 1,000ln(Public Expenditureper capita)Education Workersper 1,000 inhabitansMedical Doctorsper 1,000 inhabitantsPanel A: Whole SamplePlacebo Years of -0.00529 -0.430** 0.121** -0.0173Private Colonization (0.0925) (0.166) (0.0605) (0.0712)Observations 1,636 1,357 1,636 1,636R-squared 0.212 0.212 0.398 0.461Mean Dep. Var. 0.695 1.070 1.196 1.326Panel B: Up to 50km of the borderPlacebo Years of 0.00359 -0.304** 0.105* -0.00187Private Colonization (0.101) (0.146) (0.0627) (0.0483)Observations 829 670 829 829R-squared 0.227 0.226 0.388 0.203Mean Dep. Var. 0.739 1.098 1.230 0.916Notes: All specifications include state fixed effects, and control for the distance to the placebo border and aset of geographical variables including longitude, latitude, altitude, distance to the coast, sunlight incidence,and rainfall. Clustered standard errors at the 1920 municipality level are reported in parentheses. ***, **,and * indicate significance at the 1, 5, and 10 percent levels.Table 2.9: Placebo DC - 192030(1) (2) (3) (4) (5) (6)Dependent Variable:Municipal PublicEmployees per 1,000ln(Current Expenditureper capita)Public School Teachersper 1,000 inhabitansSUS Medical Doctorsper 1,000 inhabitantsHealth Centersper 10,000 inhabitantsChild Mortalityper 10,000 inhabitantsPanel A: Whole SamplePlacebo Years of 0.243 -0.00121 0.215* 0.0288 0.345** 0.113Private Colonization (0.818) (0.0144) (0.122) (0.0401) (0.148) (0.0721)Observations 1,681 1,665 1,681 1,680 1,648 1,681R-squared 0.113 0.180 0.133 0.130 0.222 0.129Mean Dep. Var. 48.20 7.076 11.96 1.706 6.594 1.699Panel B: Up to 50km of the borderPlacebo Years of -1.652* -0.0258 -0.0344 -0.0285 0.328** -0.00994Private Colonization (0.956) (0.0172) (0.143) (0.0455) (0.163) (0.0898)Observations 869 859 869 868 856 869R-squared 0.151 0.206 0.131 0.156 0.195 0.159Mean Dep. Var. 46.81 7.020 11.67 1.637 5.825 1.939Notes: All specifications include state fixed effects, and control for the distance to the placebo border and aset of geographical variables including longitude, latitude, altitude, distance to the coast, sunlight incidence,and rainfall. Robust standard errors are reported in parentheses. ***, **, and * indicate significance at the1, 5, and 10 percent levels.Table 2.10: Placebo DC - 20102.6 ConclusionIn this article, we examined the impact of exposure to private colonization on governmentsize and public goods provision over time in the context of Brazil. We exploit the DonataryCaptaincy system, where the Portuguese Crown divided Colonial Brazil, assigning each ter-ritory to a private citizen. Based on that, a measure for years of private colonization wasconstructed as the difference between the year the territory was returned to the PortugueseCrown and the year of the first settlement. To alleviate endogeneity concerns, we includedstate fixed effects, control for distance to the closest DC border, and restricted the sample tomunicipalities located up to 50 kilometres from the Donatary Captaincies\u2019 borders, following(Michalopoulos and Papaioannou, 2013).The estimates suggest that more years of exposure to private colonization led to fewer publicemployees and lower government expenditure in 1920. Educational public goods, such asteachers and schools, as well as the number of medical doctors, were also lower the moreprivate colonization a municipality had. However, we found evidence of convergence in 2010both in government size and educational outcomes. The only persistent difference regardsthe number of public medical doctors and health centers, which is lower, and child mortality,which is higher for private colonized areas.31Our findings are robust to a series of tests. For instance, our case study, where a regressiondiscontinuity analysis using territories with little exposure to private colonization yieldedsimilar results. Moreover, re-estimating the results using placebo Donatary Captaincies ledto null results, ruling out omitted variables explaining the results.A possible future avenue focuses on the impacts on the municipalities\u2019 revenue both in 1920and 2010. Additionally, we plan to further analyze the mechanism behind the convergenceobserved between both periods.32Chapter 3Slavery and Violence against BlackWomen: Evidence from Brazil3.1 IntroductionViolence against women is a worldwide problem. Between 45% and 55% of women in theEuropean Union have experienced sexual harassment since the age of 15 (FRA, 2014), 31.5%have lived through a physical violence case in the United States (DuMonthier et al., 2017)and 1 in 3 women in the world have suffered some kind of violence from a partner or non-partner at least once in their life (Garc\u00b4\u0131a-Moreno et al., 2013). This problem is even morepronounced when we focus on black women. They are twice as likely to be killed by a spouse,have higher rates of rape or sexual assault when compared to white women (Catalano et al.,2009) and suffer more cases of psychological and physical violence when compared to womenoverall (Breiding, 2014).Understanding the causes behind this difference is crucial for achieving both racial and genderequality.1 One potential explanation is an intergenerational transmission of a gender violenceculture. As El Feki et al. (2017) shows, men are more likely to commit an act of psychological,sexual and\/or physical violence against their wives if they witnessed, as children, their fathersdoing the same at home. Similarly, Alesina et al. (2020) have shown that ancestral societieswhere women participated less in the economy have higher rates of violence against womentoday. Cultural characteristics, such as endogamy (the custom of marrying within a socialgroup) and patrilocality (married couples residing in the husband\u2019s village) also predict higherrates of domestic violence. Therefore, it is essential to understand whether past institutionsmight have persistent effects on violence against black women today.1Goal number 5 on the list of Sustainable Development Goals developed by the United Nations.33In this chapter, I analyze how female slavery in the 19th century affects violence againstblack women today using data from Brazil. Slavery societies marginalized black men andwomen, employing violence to maintain their power and reinforce their hierarchical position(Feinstein, 2018). This type of behavior was rooted in the society and it was strengthened bythe absence of laws that forbade physical punishments against the slaves. The use of violenceagainst slaves was routine in Brazil, as documented by Lima (2002), Araujo (2015), Torres(2008), and Nogueira (1999).This institutionalized violence affected black men and women differently. While male slaveswere seen as highly aggressive and, because of that, were more subject to physical punish-ments, female slaves were hypersexualized by society, leading to a culture of sexual violenceagainst them.2 Female slaves who refused their masters\u2019 advances were subject to physicaland psychological punishments, such as the threat of killing or selling their children (Fein-stein, 2018).Having in mind a model of cultural transmission such as Bisin and Verdier (2001), this typeof behaviour may have been transmitted over time. As an example, families used to purchasefemale slaves to satisfy the sexual desire of their sons, likely helping perpetuate this type ofviolence across generations. Hence, in places with a high share of female slaves, this cultureof oppression of black people would be centred on subjugating black women, using sexualand physical violence as instruments. So, in this article, I test how the share of female slavesin the 19th century affects violence against black women today in the context of Brazil.The naive comparison between municipalities with higher and lower share of female slavesmight lead to several biases. On one hand, municipalities might have a higher share of femaleslaves because they are treated better. In this case, they might experience fewer deaths offemale slaves and fewer attempts to run away, which increases their share. If this type ofbehaviour is transmitted over time, those places might have a lower level of violence againstwomen. On the other hand, places where individuals want to commit more gender violence,might have purchased more female slaves than the rest and transmit this type of behaviourto the next generation.Given this setting, I need an identification strategy to deal with endogeneity. In this chapter,I use the distance to Uruguaiana, in the South of Brazil, the war front of the Paraguayan war(1864-1870), as an instrument for the share of female slaves in a Brazilian municipality. Dueto the shortage of soldiers, the Brazilian empire started recruiting male slaves to join the wareffort. They pressured land owners and religious organizations to manumit slaves for the warand started accepting runaway slaves in the army to deal with the small numbers of soldiers.2This can be seen on records from slaves auctions, where female slaves were marketed as virgins, whilethe same didn\u2019t happen with the male slaves (Feinstein, 2018).34Therefore, the closer a municipality was to the war front, the higher would be the numberof male slaves leaving to join the war effort. Since only free men were allowed in the armedforces, the slaves had to be manumitted before joining the army. So, municipalities closer tothe war front will have a plausible positive exogenous variation in their share of female slaves.First-stage results corroborate the hypothesis presenting a negative relationship between theshare of female slaves in a municipality and its log distance to Uruguaiana.The IV estimates indicate that a 1 percentage point increase in the share of female slaves in1872 led to a 33.6% increase in cases of violence against black women today. This increaseis driven by cases of physical and psychological violence against black women and the samepattern is not observed in cases against white or brown women. This result provides evidencethat black women still have to bear the consequences of slavery after more than 130 years ofits abolition in Brazil.3The rest of this chapter is structured as follows. Section 3.2 reviews the literature. I providedan overview of the historical events of the Paraguayan war in Section 3.3. Section 3.4 describesthe empirical strategy and data used in this chapter, while Section 3.5 presents the results.Section 3.6 displays robustness tests and Section 3.7 concludes.3.2 Related LiteratureThis chapter relates to three main strands of the economic literature. First, it is related tothe literature that estimates the persistent effects of forced labour (Nunn, 2008; Dell, 2010;Nunn and Wantchekon, 2011; Bertocchi and Dimico, 2012, 2014; Papadia, 2019; Lambais,2020; Laudares and Valencia Caicedo, 2023). Nunn (2008) showed that African countriesthat exported more slaves during the colonial period are less developed today, while Nunnand Wantchekon (2011) presented a correlation between the number of inhabitants capturedto become slaves and the levels of trust in those areas. However, those papers differ from thisby focusing their analysis on the slaves\u2019 origin countries, instead of the countries that receivedthose slaves. In that sense, this chapter is closer to Dell (2010), which analyses the impact ofa forced mining labour institution called Mita in Peru and Bolivia, and Papadia (2019) andLaudares and Valencia Caicedo (2023) that estimates the impact of slavery on public goodsprovision and economic inequality, respectively, in Brazil, although none of them analysesthe impact of forced labour on violence against women.Second, it contributes to the literature that analyses the historical roots of gender differences.4Alesina et al. (2013) and Giuliano (2015) presented evidence that the historical use of theplough led to lower female participation in the labour market and to parental and inheritance3Brazil abolished slavery in May 13th, 1888.4See Giuliano (2020) for a more extensive literature.35laws that favour men. Similarly, languages with more gender distinctions are associated withworse labour outcomes for women (Gay et al., 2013). Focusing on the colonial period, Teso(2019) found that women in African countries that lost more men for slavery have a higherlikelihood to participate in the labour market, Bertocchi and Dimico (2019) showed thatareas with higher slave density are associated with a higher prevalence of HIV today andGrosjean and Khattar (2019) present evidence that male-biased sex ratios in Australia, dueto the British policy of sending convicts there, led to more conservative attitudes towardsfemale work and lower female participation in the labour market. Finally, this project relatesto Bertocchi and Dimico (2020) that presented evidence that black women were more likelyto be a single head of the household in 1930 if they lived in areas that heavily relied on maleslavery for sugar crops in 1860.Lastly, this chapter adds to the violence against women literature. Most of the articlesfocus on contemporaneous causes such as the reform of divorce laws (Stevenson and Wolfers,2006), the introduction of a legal reform designed to curb intimate partner violence (Ferrazand Schiavon, 2020), gender wage gap (Aizer, 2010) and the emotional cues associated withfootball results (Card and Dahl, 2011). In a more historical approach, Tur-Prats (2019a)estimates lower rates of intimate partner violence in places where stem families (familieswhere one son inherits the properties of the family and keeps living in his parents\u2019 houseafter marriage) are historically prevalent when compared to places where nuclear families(where all children share the inheritance and leave the parental home) are more common.Alesina et al. (2020) shows how cultural characteristics, such as endogamy, patrilocalityand polygyny, and the role of women in the economic activity of ancestral societies relateto violence against women in modern times and its acceptance. Tur-Prats (2019b) mixesbetween historical and modern causes by showing that higher unemployment among malesvis-a-vis females leads to higher intimate-partner violence against women in places with anuclear family tradition and Guarnieri and Tur-Prats (2020) show that individuals from moregender unequal society are more likely to be perpetrators of sexual violence and their victimsare usually people from more equal societies.The present study is more closely related with Alix-Garcia et al. (2022), which shows thatParaguayan women are more likely to raise a child without a spouse and have higher educa-tional levels today in areas more exposed to skewed sex ratios right after the war and, moredirectly, with Boggiano (2020). She takes advantage of a sex ratio skewed towards women toestimate its long-run impacts on intimate partner violence (IPV) in Paraguay. She uses thedistance of the municipality to the nearest war camp as an instrument for the female\/maleratio and finds that women are more likely to suffer IPV today in municipalities that lostmore men in the war. The key difference between our works is that I analyze how the gendercomposition of the slaves affects violence against women in Brazil, while she uses the sex ratio36of the whole population to estimate its impact on intimate partner violence in Paraguay.This chapter contributes to the economic literature by combining those branches of theliterature and studying the relationship between female slavery and violence against women.As far as I know, this is the first work to make that connection.3.3 The Paraguayan War (1864-1870)The Paraguayan War was a conflict between Paraguay and the Triple Alliance, composedof Brazil, Argentina and Uruguay, that took place between December of 1864 and March of1870. It was one of the deadliest wars in South America, leading to the death of more than73,000 members of the Triple Alliance army, including 50,000 Brazilians (Doratioto, 2002),and almost 70% of the Paraguayan population (Whigham and Potthast, 1999).5 The longduration of the war, along with a large number of deaths and a low number of volunteers,has led the Brazilian empire to manumit and recruit slaves to join the Triple Alliance army.6The animosity between Paraguay and Brazil began around 1850 when the Paraguayan pres-ident Carlos Antonio Lo\u00b4pez started putting obstacles for the Brazilian navigation in theParaguay River. This river was extremely important for the Brazilian Empire, as it was theeasiest path between the capital of the empire, Rio de Janeiro, and the province of MatoGrosso, a territory under dispute with Paraguay, until 1910.7 The posture of the Paraguayangovernment was motivated by Lopez\u2019s plan to guarantee their independence and expand thecountry\u2019s influence in the continent, which also included the modernization of the army andthe economy. However, Paraguay wasn\u2019t prepared to fight Brazil for control of the river atthat time, so they signed a treaty that allowed the free navigation of Brazilian vessels in theParaguay River until 1862 (Doratioto, 2002).In that year, the tensions in the continent started to grow again. In 1862, the Uruguayanpresident, Bernardo Berro, decided not to renew a treaty that allowed free navigation forBrazilian ships in the Uruguayan rivers. At the same time, Berro sent Uruguayan forcesto help the Argentinian separatist groups fight the recently instituted centralized power inBuenos Aires. As a response, Brazil and Argentina supported the Colorado revolution againstthe Uruguayan president. Seeing no way out, Berro sought an alignment with Paraguay,governed then by Francisco Solano Lo\u00b4pez, son of Carlos Antonio, and chief of a modern andstrong Paraguayan army. For Solano Lopez, the Uruguayan conflict was an opportunity toincrease Paraguay\u2019s influence in the continent and to gain free access to the Montevideo port,5The estimates vary in the literature from 8.7%, estimated by Reber (1988), to 89% (Washburn, 1871).6Salles (1990) and De Sousa (1996) provide a detailed description of the recruitment of former slavesduring the Paraguayan war.7In 1910, it was inaugurated a railroad between Sa\u02dco Paulo and Mato Grosso.37strengthening the Paraguayan connections with Europe.Facing an imminent failure of diplomatic solutions, Brazil prepared its forces to invadeUruguay to help the Colorado army. In response to the threat, Solano Lopez stated thatan invasion of Uruguay would be understood as a declaration of war from Brazil. However,this threat was not taken seriously by the Brazilian Empire, since up to that point, theParaguayan army had only won one battle, fought back in 1811 (Doratioto, 2002).In October of 1864, Brazilian forces invaded Uruguay to help the Colorado army in theirbattle against the Uruguayan president Atanasio Aguirre. Although Brazil did not expectit, Solano Lopez answered the attack by invading the province of Mato Grosso, in Brazil,in December of 1864 and Corrientes, Argentina in April of 1865. The attacks, along withthe Colorado victory and the establishment of a peace treaty in Uruguay in 1865, led to thesignature of the Triple Alliance treaty, creating an army formed by Brazil, Argentina andUruguay to fight Paraguay. Additionally, it helped Brazil establish a military base on thePrata River.The fact that Brazil did not believe in a Paraguayan strike helps explain the small numberof soldiers in the province that borders Paraguay. Mato Grosso had only 875 soldiers at thattime, insufficient to defeat the 8,000 soldiers sent by Solano Lopez. The Paraguayan armymarched all the way to the city of Coxim, in the middle of the Mato Grosso province andcamped there with only 1,000 soldiers after having occupied the part of the province that wasunder dispute with Brazil. According to Doratioto (2002), the battle in Mato Grosso wasjust secondary and did not influence the outcome of the war, especially after Solano Lopezasked for the return of 7,000 soldiers and the fact that Brazil was unable to send more than2,000 soldiers due to the lack of roads between that region and the rest of the country.8After occupying that region, Solano Lopez turned his attention to the south, where the warwould unravel from 1865 to 1868. Two columns of the Paraguayan army marched towardsthe south of Brazil. One went through the Argentinian margin of the river and the other onthe Brazilian. The attacking army invaded the province of Rio Grande do Sul, in the southof Brazil, through Sa\u02dco Borja, in June of 1865 and from there they marched to Uruguaianafacing little resistance from the Brazilian army. The Paraguayan army found an empty city,and decided to build trenches and a fortification to camp there. The Brazilian army, ledby the emperor Dom Pedro II, marched to Uruguaiana. They received support from theUruguayan army on the Brazilian side and from the Argentinian army, which had won thebattle against the second Paraguayan column, on the Argentinian side. The Paraguayancolumn saw themselves surrounded and in September of 1865, they surrendered to the Triple8As previously mentioned, the best way to go to Mato Grosso was passing by Assunc\u00b8a\u02dco, the capital ofParaguay, through the Parana and Paraguay rivers, which was blocked by Solano Lopez.38Alliance army.Figure 3.1: Movements of Paraguayan troops (in black) and the Triple Alliance army(in red) during the attack to Corrientes and Rio Grande do Sul.Facing this loss, Solano Lopez asked for the return of Paraguayan troops in Brazil andArgentina at the end of 1865. The allied army responded by marching to the province ofCorrientes, in Argentina. From 1866 to 1868, the war was fought in this region, in Corrientes,near the confluence of the Parana and Paraguay rivers. The line of Paraguayan fortificationsin that region, where the most famous is Humaita, allowed Solano Lopez to defend himselffrom his enemies and reorganize his army for the remainder of the battle.During the whole war, Brazil had a lot of difficulties in gathering an army.9 At the beginningof the war, the empire decided to create the Volunta\u00b4rios da Pa\u00b4tria, a corp for volunteersbetween the ages of 18 and 65, that would have larger payment, as well as some othergratifications, to join the army. However, as the war prolonged for more than a year, itbecame even harder to gather more soldiers. Since, by law, only free men could join thearmy, members of the government recommended that slave owners should manumit part oftheir slaves to join the army and allowed drafted men to replace their presence in the armyby manumitting a slave to join in their place (Conrad, 1975; De Sousa, 1996; Rodrigues,9Figures B.1 and B.2 present some cartoons published in Brazilian journals showing the difficulty ofgetting Brazilians to join the army.392009). According to Toral (1995), the empire promised manumission for slaves who decideto join the army, ignoring the fact that they might be runaways. In fact, on January 15thof 1868, the newspaper Opinia\u02dco Liberal documented a conversation, during the boarding ofthe troops to Paraguay, between a slave owner and the emperor Dom Pedro II, in whichthe slave owner claims that one of the soldiers is a runaway slave and that he wants himback. The emperor answers saying that he should deal with the ministry about reparation,showing that he wasn\u2019t willing to lose his soldier over this.10 The Brazilian government alsoimprisoned slaves to send them to war. Only in Rio de Janeiro during the year 1867, therewere 140 complaints of property rights violations and forced draft of slaves (Couto, 2013).Although there aren\u2019t precise estimates on the number of slaves in the army,11 the presenceof freed slaves in the army was felt by both sides. Paraguayan newspapers used to portraythe Brazilian soldiers, in a racist manner, as an \u201carmy of monkeys\u201d, as can be seen in FiguresB.3 and B.4. Duque de Caxias, the commander of the Brazilian forces between 1866 and1869, used the presence of former slaves to justify some of his battles losses. In a letter fromCaxias to the Bara\u02dco de Muritiba in 1868, he said that indiscipline shown on the battlefieldcomes from \u201cmen that don\u2019t understand what is nation, society and family, that still considerthemselves as slaves, having just changed their master\u201d.12The period from 1866 and 1868 was characterized by individual battles, where the allies werevictorious in most of them, in the region of Corrientes. Finally, at the end of 1868, the TripleAlliance army was able to break the defense line built by Solano Lopez, and marched toAssunc\u00b8a\u02dco, the capital of Paraguay, occupying it in January 1st of 1869. At that point, thewar was won by the Triple Alliance and they engaged in negotiations for the organizationof a new government. However, D. Pedro II didn\u2019t accept the return of the Brazilian forcesto Brazil until they captured or killed Solano Lopez. This finally happened in March 1870,when Solano Lopez was killed in Cerro Cora\u00b4, Paraguay.In 1872, Brazil signed the peace treaty with Paraguay, guaranteeing the free navigation ofParaguay river and the recognition from Paraguay of the Brazilian ownership of the regionin the Mato Grosso province. After 5 years of conflict and the death of 50,000 Brazilians,10\u201c - Senhor, aqui esta\u00b4 fardado entre estes soldados um meu escravo. Reclamo que me entregue\u201d. Aoque responde Dom Pedro II: \u201cSim, entenda-se com o ministro, que sera\u00b4 indenizado\u201d. \u201cMas na\u02dco se trata deindenizac\u00b8a\u02dco, senhor! O escravo e\u00b4 minha propriedade e na\u02dco quero dispor dele, nem ta\u02dco pouco autorizei queele assentasse prac\u00b8a\u201d. \u201c- Deixe estar, ha\u00b4 de se ver isso: Fale ao ministro\u201d. Opinia\u02dco Liberal newspaper, Riode Janeiro, January 15th, 1868.11Conrad (1975) estimated that 20,000 slaves were manumitted to join the war, but he doesn\u2019t take intoaccount runaway slaves and Salles (1990) states that it is very hard to estimate the number of slaves in theBrazilian army because the society wanted to hide the importance of the slaves during the war to preventtalks about abolition of slavery.12-\u201cHomens que na\u02dco compreendem o que e\u00b4 pa\u00b4tria, sociedade e fam\u0131\u00b4lia, que se consideram ainda escravos,que apenas mudaram de senhor\u201d. Caxias to Muritiba, December 13th, 1868.40the war was over.3.4 Empirical Strategy and Data3.4.1 Empirical StrategyThe presence of former slaves in the Brazilian army during the Paraguayan war is widely doc-umented in the Brazilian historiography (Conrad, 1975; Salles, 1990; Toral, 1995; De Sousa,1996; Rodrigues, 2009; Couto, 2013). As mentioned in the previous section, the Brazilianempire pressured land owners and religious organizations to donate slaves for the war effort(Couto, 2013) and they authorized drafted men to be replaced by a slave manumitted byhim. The Brazilian army also accepted the enlistment of runaway slaves to help with theshortage of soldiers (Toral, 1995; Rodrigues, 2009).The recruitment of slaves was largely influenced by the pressure made by the military. Mem-bers of the army promoted forced recruitment of soldiers in the streets (De Sousa, 1996;Doratioto, 2002). Since richer men could replace their participation by freeing slaves, theforced draft led to a higher number of slaves in the army. Another common practice of thearmy was to arrest slaves on the street under the accusation of loitering and send them to thewar, regardless of the authorization of their owner (Rodrigues, 2009; Moreira, 2010). Finally,the presence of the military in a city presented a good opportunity for a runaway slave sincehe would be considered a free man after signing up for the army.Since Brazil had prohibited international slave traffic in 1850, the draft of male slaves by theBrazilian army can be understood as a plausible and permanent positive exogenous variationin the share of female slaves. As explained above, this effect seems to be stronger the closer weare to the war front. Therefore, in this chapter, I use the distance to Uruguaiana (the locationof the first war front) as an instrument for the share of female slaves in a municipality.13 Theidea is that the closer a municipality is to Uruguaiana, the more male slaves they would sendto the war and the higher would be the share of female slaves.The first stage equation allows me to capture a plausible exogenous variation in the share offemale slaves, denoted as \u0302ShareFemaleSlavesi,1872. In the second stage, I estimate the effectof this variation on violence against women outcomes, formally described by the equationsbelow:ShareFemaleSlavesi,1872 = \u03b10 + \u03b11ln(DistanceUruguaianai) + \u0393\u20321Zi,1872 + \u0393\u20322Wi,2010 + \u03f5itYi,2010+s =\u03b20 + \u03b21 \u0302ShareFemaleSlavesi,1872 + \u039b\u20321Zi,1872 + \u039b\u20322Wi,2010 + uit13Figure B.5 displays the map of South America and the location of Uruguaiana.41Where ShareFemaleSlavesi,1872 is the proportion of female slaves in municipality i in 1872and ln(DistanceUruguaianai) is the logarithm of the distance between municipality i andUruguaiana. Zi,1872 is an 1872 controls vector that includes the total number of slaves, popu-lation and shares of female, white, foreign, married and catholic populations in municipality iand Wi,2010 is a vector of 2010 controls such as population, municipal GDP, literacy rate andshares of female, white, black, brown, indigenous and urban populations. Lastly, Yi,2010+s isthe set of measures of violence against women in modern days, more specifically, the yearlymean between 2015 and 2017.Since the municipalities in the 19th century are different than those today, I use a similarapproach to Ehrl (2017) and aggregate 2010 municipalities to match an 1872 municipality.Finally, as mentioned before, the presence of the military impacted directly the recruitmentof slaves. Therefore, I restrict my sample to states where the army marched when going tothe war.14 However, it is unclear what was the exact path of the armed forces, so I restrictmy sample to states close to the telegraph line built for communications between the capitaland war front during the Paraguayan war (Figure 3.2b) and to the states near the capital ofthe empire, Rio de Janeiro.(a) Map of Brazil - The yellow municipalities are in-cluded in the sample. (b) Telegraph line in 19th Century.Figure 3.2: Areas in the sample14As mentioned before, there were no roads connecting Mato Grosso and the rest of the country. Therefore,it is unlikely that the army marched through Mato Grosso and, for that reason, I excluded it from the sample423.4.2 Data1872 Brazilian Census: The 1872 Census was organized by the Diretoria Geral de Es-tat\u00b4\u0131stica (DGE), a public agency created by the Brazilian empire to collect national data. Ithas data on the number of slaves and demographic characteristics such as race, age, religion,country of birth and marital status for the population in each municipality in Brazil. Aswe can see in Table 3.1 panel A, the mean 1872 municipality has a little less than 20,000inhabitants, with almost 3,750 slaves. As expected, both measures are right-skewed with ahigh standard deviation, which indicates an uneven distribution of population and slaves.2010 Brazilian Census: The modern characteristics of each municipality come from the2010 Census. It is organized by the IBGE (Instituto Brasileiro de Geografia e Estat\u00b4\u0131stica)and provides data on the shares of urban, female, black, brown and indigenous population,as well as the literacy rate, population and municipal GDP. Summary statistics are providedbelow in Table 3.1 in panel B.43Variable Mean SD Min MaxPanel A: 1872 VariablesPopulation (in 1,000) 18.11 20.84 1.57 274.97Total Slaves (in 1,000) 3.74 4.98 0.06 48.94Share Female Slaves (x100) 46.16 3.64 31.62 58.59Share Female 0.48 0.02 0.36 0.60Share White 0.49 0.14 0.08 0.96Share Foreign 0.05 0.06 0.00 0.50Share Married 0.24 0.05 0.11 0.42Share Catholic 0.99 0.03 0.57 1.00Panel B: 2010 VariablesPopulation (in 10,000) 41.37 118.84 0.37 1,614.71Share Urban 0.83 0.14 0.30 1.00Share Female 0.48 0.08 0.00 0.53Share Brown 0.30 0.14 0.04 0.69Share Black 0.07 0.04 0.01 0.19Share Indigenous 0.00 0.00 0.00 0.04Literacy Rate in 2010 0.93 0.03 0.78 0.98GDP (in R$ billions) 1.03 4.11 0.00 60.65Panel C: Geographylog distance to Uruguaiana (in kms) 7.09 0.49 4.70 7.69Latitude -23.04 3.32 -32.79 -15.01Longitude -46.42 3.43 -57.32 -40.07Notes: The sample consists of 260 Brazilian municipalities based on 1872boundaries. Latitude and longitude come from Ipeadata.Table 3.1: Summary Statistics: Municipal CharacteristicsViolence against women data: Since 2014, all cases of violence against women, wherethe victim attended public or private hospitals, must be notified to the Ministry of Healthwithin 24 hours. The data on the gender violence notifications used in this chapter can befound on SINAN (Sistema de Informac\u00b8a\u02dco de Agravos de Notificac\u00b8a\u02dco) at the municipal level.Each case is classified according to the type of violence committed. In this chapter, I focuson the following categories: (i) physical violence, which is any act in which the aggressor usesphysical strength intentionally against his victim, (ii) psychological violence, when the victimsuffers any kind of humiliation, excessive pressure or discrimination, (iii) sexual violence,which is any situation where the aggressor uses their power or physical strength to make thevictim participate or watch sexual interactions and (iv) torture, when there is signs of torturein the victim. Those categories are non-excludable, meaning that one case can be classified44as more than one type of violence.I restricted the sample to cases where the victim is a woman and is more than 15 years old.Also, I\u2019m using the number of violent episodes based on where the case happened, insteadof where it was notified. The summary statistics are presented in Table 3.2. As said before,one case might involve both physical and sexual violence. In that case, it is counted underboth categories, even though it is only one report. That explains why the sum of reports ineach type of violence is different from the total number of cases.For each municipality, I calculate the yearly mean value for each variable between 2015 and2017.15 Then, I aggregated the data at the 1872 municipality level and reported the mean foreach type of violence and measured per 1,000 inhabitants of that race in that municipality.16Most of the reported cases involve physical violence and it is mostly committed againstblack and indigenous women (1.45 cases per 1,000 black inhabitants and 1.37 cases per 1,000indigenous inhabitants).152015 is the first year after the notifications became mandatory and 2017 is the last available yearly datathat has the municipality of occurrence.16Since there isn\u2019t yearly data on the number of people per race at the municipality level, I multipliedthe share of people of a particular race in 2010 by the population of that year to estimate the number ofinhabitants of that race between 2015 and 2017.45Variable Mean SD Min MaxPanel A: Total cases of violence (per 1,000)White 0.85 0.62 0.00 3.78Brown 0.89 0.76 0.00 5.05Black 1.45 1.26 0.00 8.29Indigenous 1.37 3.00 0.00 29.44Panel B: Physical Violence (per 1,000)White 0.67 0.49 0.00 2.46Brown 0.72 0.64 0.00 4.73Black 1.17 1.02 0.00 5.89Indigenous 1.19 2.96 0.00 29.44Panel C: Psychological Violence (per 1,000)White 0.32 0.34 0.00 2.42Brown 0.33 0.35 0.00 2.42Black 0.56 0.67 0.00 5.09Indigenous 0.47 1.19 0.00 8.58Panel D: Sexual Violence (per 1,000)White 0.09 0.07 0.00 0.52Brown 0.10 0.09 0.00 0.66Black 0.17 0.17 0.00 0.98Indigenous 0.23 1.19 0.00 12.79Panel E: Torture (per 1,000)White 0.03 0.03 0.00 0.26Brown 0.03 0.05 0.00 0.57Black 0.05 0.08 0.00 0.61Indigenous 0.05 0.25 0.00 2.24Notes: The sample consists of 260 Brazilian municipalities based on 1872boundaries. All the variables are measured per 1,000 inhabitants of that race.Table 3.2: Summary Statistics: Violence against Women3.5 Results3.5.1 OLS EstimatesTable 3.3 presents the estimates from a regression of the share of female slaves in an 1872municipality on measures of violence against women today. I have restricted for cases of46violence against women of a specific race in each column and for a different type of violencein each panel. All regressions use province fixed effects and controls for latitude, longitude,and socioeconomic characteristics of 1872 municipalities (total number of slaves, population,shares of women, whites, foreigners, married population and catholic population) and 2010municipal characteristics (municipal GDP, population, shares of urban population, women,black population, brown population, indigenous population and literacy rate).Even though most of the estimates in the table are not statistically significant, some ofthem present sizeable results. A 1 percentage point increase in the share of female slaves isassociated with an increase of 6.8% in total cases of violence and an 8.7% increase in casesof physical violence against indigenous women, which might be explained by the fact thatindigenous people were enslaved in Brazil. Similarly, the same increase in the share of femaleslaves is associated with a 2.9% increase in cases of physical violence per 1,000 black peopleand a 4.9% increase in cases of psychological violence.However, those estimates might be biased. And the direction of the bias might go on bothways. Municipalities that treated better female slaves might have a higher share of femaleslaves and have not developed a culture of violence against black women. At the same time,places that are more violent towards female slaves might acquire more enslaved women,increasing the share of female slaves. This aggressive behaviour might be passed on acrossgenerations, leading to a higher rate of violence against black women today. Hence, thoseeffects may bias the estimates towards zero.47(1) (2) (3) (4)White Brown Blacks IndigenousPanel A: Total cases of Violence (per 1,000)Share of Female Slaves (x100) 0.0194 0.00533 0.0329 0.0939(0.0119) (0.0131) (0.0247) (0.0713)R-squared 0.289 0.349 0.283 0.106Observations 260 260 260 259Mean Dep. Var. 0.853 0.892 1.454 1.375Panel B: Physical Violence (per 1,000)Share of Female Slaves (x100) 0.0132 0.00215 0.0343* 0.103(0.00977) (0.0115) (0.0188) (0.0709)R-squared 0.287 0.338 0.305 0.104Observations 260 260 260 259Mean Dep. Var. 0.666 0.722 1.175 1.188Panel C: Psychological Violence (per 1,000)Share of Female Slaves (x100) 0.0134* 0.00952 0.0277* 0.0267(0.00793) (0.00788) (0.0147) (0.0256)R-squared 0.208 0.230 0.179 0.133Observations 260 260 260 259Mean Dep. Var. 0.323 0.330 0.558 0.473Panel D: Sexual Violence (per 1,000)Share of Female Slaves (x100) 0.00345* 0.00364 0.00168 -0.0157(0.00176) (0.00290) (0.00418) (0.0191)R-squared 0.219 0.236 0.126 0.071Observations 260 260 260 259Mean Dep. Var. 0.0894 0.105 0.166 0.232Panel E: Violence with signs of Torture (per 1,000)Share of Female Slaves (x100) -0.000343 0.00109 0.00004 -0.00414(0.000592) (0.00128) (0.00149) (0.00822)R-squared 0.215 0.288 0.218 0.083Observations 260 260 260 259Mean Dep. Var. 0.0289 0.0338 0.0492 0.0473Notes: The dependent variable is the number of cases of violence against women per1,000 inhabitants of that race. All regressions are controlled for 1872 characteristics(total number of slaves, population, share of women, share of whites, share of foreign,share of married people, share of catholic), 2010 characteristics (municipal GDP, pop-ulation, share of urban population, share of females, share of blacks, share of brown,share of indigenous people and literacy rate), latitude, longitude and province FE. Ro-bust standard errors in parentheses. When *** p<0.01, ** p<0.05, * p<0.1.Table 3.3: OLS Results483.5.2 IV EstimatesGiven that the OLS estimates might be biased, I instrument the share of female slaves usingthe log distance to Uruguaiana, the first war front of the Paraguayan war. Due to the shortageof soldiers during the war, the Brazilian empire started to draft male slaves. The closer amunicipality was to the war front, the more male slaves will join the army, and higher willbe the share of female slaves.The first stage results are presented in Table 3.4. Column 1 reports the estimate withoutcontrol variables, expect for latitude and longitude. Column 2 also controls for 1872 municipalcharacteristics and column 3 adds socioeconomic variables in 2010. Finally, in column 4, I alsouse province fixed effects. Throughout the remainder of this chapter, I use the specificationin column 4, with province FE, 1872 and 2010 municipal controls.Consistent with the hypothesis, the results indicate a negative relationship between share offemale slaves and the log distance to Uruguaiana.17 This means that the closer a municipalityis to the war front (the smaller the distance between that locality and Uruguaiana), the higherwill be its share of female slaves. Following Stock et al. (2002), the F statistic is always above10 suggesting that the instrument is strong.(1) (2) (3) (4)VARIABLESln(distance to Uruguaiana) -5.295*** -3.745*** -4.859*** -4.203***(1.214) (1.020) (0.981) (1.059)Observations 259 259 259 259R-squared 0.134 0.477 0.499 0.533Province FE Yes No Yes Yes1872 Controls No Yes Yes Yes2010 Controls No No No YesMean Dep. Var. 46.16 46.16 46.16 46.16F-Stat 19.01 13.47 24.53 15.76Notes: The dependent variable is the share of female slaves, ranging from 0 to100, in each 1872 municipality. The main independent variable is the log dis-tance to Uruguaiana in kms. 1872 controls: total number of slaves, population,share of women, share of whites, share of foreign, share of married people, shareof catholic. 2010 controls: municipal GDP, population, share of urban popula-tion, share of females, share of blacks, share of brown, share of indigenous peopleand literacy rate. Additional controls: latitude and longitude. Robust standarderrors in parentheses. When *** p<0.01, ** p<0.05, * p<0.1.Table 3.4: First Stage17Table B.1 presents the estimates for all covariates.49Unlike what the OLS results suggested, the IV estimates in Table 3.5 show that the share offemale slaves during the 19th century actually affects violence against black women today.18In Panel A, using total cases of violence against women as an outcome, we observe that a1 p.p. increase in the share of female slaves in 1872 leads to an increase of 0.408 cases ofviolence against black women per 1,000 black inhabitants. This translates into an increaseof 33.6% in the number of violent episodes against black women.19 The same pattern is notobserved for white and brown women. The estimates for cases of violence against them arenot statistically significant. However, the estimates for cases against white and indigenouswomen are economically meaningful. The same increase in the share of female slaves led toa 15% and a 35.5% increase in cases against white and indigenous women, respectively. Theresult for white women suggests that the violence might have spilled over to them, whereasthe stronger effect on indigenous women can be explained by the fact that indigenous werealso enslaved in Brazil before and during the Empire (Miki, 2014; Dornelles, 2018; Bucciferro,2013; De La Torre, 2019).When I disaggregate by type of violence, a similar pattern arises. An increase of 1 p.p.in the share of female slaves led to an increase of 21.2% and 65.2% in cases of physicaland psychological violence, respectively, against black women. As before, the estimates forwhite women have a smaller magnitude, despite being significant at 10%. That could be anindication that violence caused by slavery did spill over to other races, although black andindigenous women still carry most of the burden of the slavery heritage.In panels D and E, which focus on cases of sexual violence and violence with signs of torture,no effects were found for any race. There are at least two possible explanations for thoseresults. First, it is possible that women don\u2019t go as often to hospitals in cases of sexual whencompared to cases of physical violence. That would explain why there was an effect in panelB but not on panel D. The second possibility is that, even though sexual violence was one ofthe many aggression committed against female slaves, this behaviour might not have passedon across generations, as physical and psychological violence was.The results presented here indicate that slavery affects violence outcomes today. Since allregressions use the total number of slaves in a municipality as control, the results are notdriven by an increase in inequality due to a higher number of slaves (as shown by Laudares andValencia Caicedo (2023)). In fact, the estimate on the share of female slaves shows that thegender composition of slaves has consequences in modern times. As Feinstein (2018) explains,elites in slave societies used violence against slaves as a way to strengthen their hierarchicalposition in society. Therefore, in a municipality where the majority of slaves were composed18Tables B.2 to B.6 present the estimates for all covariates.19This is equivalent to a 1.18 SD increase in the number of cases of violence against black women for each1 SD increase in the share of female slaves. Results are available upon request.50of women, the next generations would internalize and reproduce the behaviour, committingacts of violence against black women.(1) (2) (3) (4)White Brown Blacks IndigenousPanel A: Total cases of Violence (per 1,000)Share of Female Slaves (x100) 0.128 -0.0189 0.408** 0.489*(0.0894) (0.0629) (0.169) (0.295)Observations 259 259 259 258Mean Dep. Var. 0.853 0.892 1.454 1.375Panel B: Physical Violence (per 1,000)Share of Female Slaves (x100) 0.0929* -0.00788 0.249*** 0.541*(0.0478) (0.0509) (0.0863) (0.293)Observations 259 259 259 258Mean Dep. Var. 0.666 0.722 1.175 1.188Panel C: Psychological Violence (per 1,000)Share of Female Slaves (x100) 0.160* 0.0636 0.364** 0.391(0.0872) (0.0409) (0.182) (0.308)Observations 259 259 259 258Mean Dep. Var. 0.323 0.330 0.558 0.473Panel D: Sexual Violence (per 1,000)Share of Female Slaves (x100) 0.00116 0.00714 0.00584 0.0410(0.00854) (0.0133) (0.0180) (0.0706)Observations 259 259 259 258Mean Dep. Var. 0.0894 0.105 0.166 0.232Panel E: Violence with signs of Torture (per 1,000)Share of Female Slaves (x100) -0.000077 0.00157 -0.00272 0.00449(0.00210) (0.00567) (0.00650) (0.0165)Observations 259 259 259 258Mean Dep. Var. 0.0289 0.0338 0.0492 0.0473Notes: The dependent variable is the number of cases of violence against women per1,000 inhabitants of that race. All regressions are controlled for 1872 characteristics(total number of slaves, population, share of women, share of whites, share of foreign,share of married people, share of catholic), 2010 characteristics (municipal GDP, pop-ulation, share of urban population, share of females, share of blacks, share of brown,share of indigenous people and literacy rate), latitude, longitude and province FE. Ro-bust standard errors in parentheses. When *** p<0.01, ** p<0.05, * p<0.1.Table 3.5: IV Results513.5.3 MechanismHistorically in Brazil, female slaves were predominantly assigned to domestic work, while maleslaves were assigned to more labour-intensive work, particularly agriculture (Muaze, 2016).Hence, the draft of male slaves may have resulted in a shortage of labour in agriculture,forcing female slaves to be relocated to agricultural work from other tasks, such as domesticwork. Once in the plantations, female slaves became more vulnerable to violence, as tasksthat required a great physical effort were usually accompanied by close supervision and theuse of physical violence as control mechanisms during slavery (Fenoaltea, 1984; Klein andLuna, 2009). Therefore, the move from domestic to agricultural could have led to a cultureof violence against black women that reverberates until the 21st century.I test this hypothesis by rerunning my first stage equation using the percentage of femaleslaves assigned to domestic and agriculture as the outcomes. The results, presented in Table3.6 columns 1 to 4, suggest that the closer a municipality is to the Uruguaiana war front,the fewer female slaves were designated to domestic work, while more were allocated toagricultural tasks.If our hypothesis is true, there should have been an increase in the number of female slaves anda decrease in the number of male slaves in agriculture. Consequently, we should expect thatthe gender composition of slaves became more skewed towards female slaves in agriculturalwork, which is observed in columns 5 and 6 when using the share of female slaves amongthose assigned to agricultural work as the dependent variable. Overall, the results offersuggestive evidence supporting the initial hypothesis that female slaves were indeed reassignedfrom domestic to agricultural work. Nevertheless, it is important to mention that eventhough point estimates are sizable, the results are not statistically significant and should beinterpreted with caution.52(1) (2) (3) (4) (5) (6)Dependent Variable:% Female Slaves inDomestic Work% Female Slaves inAgricultural WorkShare Female Slavesin Agricultureln(distance to Uruguaiana) -7.969 -7.717 4.314 4.015 5.952 8.401(6.572) (6.818) (3.647) (4.609) (5.064) (5.517)Observations 259 259 259 259 253 253R-squared 0.160 0.218 0.339 0.378 0.278 0.352Demographic Controls No Yes No Yes No YesMean Dep. Var. 28.66 28.66 27.18 27.18 29.05 29.05Notes: The dependent variable is the percentage of female slaves in domestic work (columns 2and 3), the percentage of female slaves in agricultural work (3 and 4), and the share of slaveswho are women working in agriculture, ranging from 0 to 100, in each 1872 municipality. Themain independent variable is the log distance to Corrientes in kms. 1872 controls: total numberof slaves, population, share of women, share of whites, share of foreign, share of married people,share of catholic. 2010 controls: municipal GDP, population, share of urban population, share offemales, share of blacks, share of brown, share of indigenous people and literacy rate. Additionalcontrols: latitude and longitude. Robust standard errors in parentheses. When *** p<0.01, **p<0.05, * p<0.1.Table 3.6: Mechanisms3.6 Robustness Checks3.6.1 Corrientes as War FrontAs mentioned in section 3.3, the Paraguayan war can be divided into three phases. In thefirst phase, the battles took place in the southern region of Brazil, in Uruguaiana, from 1864and 1865. The second phase happened between 1866 and 1868, where most of the battleshappened in Corrientes, Argentina,20 while the last phase, from 1869 to 1870, consistedmostly on searching for Solano Lopez after the war had been virtually won by the TripleAlliance.Throughout this chapter, I use the distance to Uruguaiana, the war front in the first phase,as an instrument for the share of female slaves. The choice was motivated by the fact that theBrazilian army drafted male slaves as they marched to the first war front (De Sousa, 1996;Doratioto, 2002). However, since Corrientes was the longest phase of the war, the resultsshould hold when choosing distance to Corrientes, the second war front, as the instrument.Table 3.7 suggests that the first stage results are indeed robust to using Corrientes, insteadof Uruguaiana, as the war front. The estimates indicate that the further away a municipality20The map of South America and the location of Corrientes is shown in Figure B.6.53is from the war front (in this case, Corrientes), the smaller will be their share of femaleslaves. The F statistic indicates that this is a strong instrument, as it is above 10 in mostspecifications.(1) (2) (3) (4)VARIABLESln(distance to Corrientes) -1.634*** -1.744*** -1.794*** -1.539***(0.560) (0.527) (0.480) (0.437)Observations 257 257 257 257R-squared 0.115 0.474 0.490 0.527Province FE Yes No Yes Yes1872 Controls No Yes Yes Yes2010 Controls No No No YesMean Dep. Var. 46.16 46.16 46.16 46.16F-Stat 8.529 10.93 13.96 12.39Notes: The dependent variable is the share of female slaves, ranging from 0 to100, in each 1872 municipality. The main independent variable is the log dis-tance to Corrientes in kms. 1872 controls: total number of slaves, population,share of women, share of whites, share of foreign, share of married people, shareof catholic. 2010 controls: municipal GDP, population, share of urban popu-lation, share of females, share of blacks, share of brown, share of indigenouspeople and literacy rate. Additional controls: latitude and longitude. Robuststandard errors in parentheses. When *** p<0.01, ** p<0.05, * p<0.1.Table 3.7: First Stage - Distance to CorrientesAs expected, the second stage results are also robust to using distance to Corrientes asan instrument. The estimates in Table 3.8 indicate that a 1 percentage point increase inthe share of female slaves in 1872 leads to an increase of 0.289 and 0.194 cases of physicaland psychological violence, respectively, against black women per 1,000 black inhabitants.Following what was observed in subsection 3.5.2, the estimates for white and brown womenare somewhat smaller and less precisely estimated. The only exception is the coefficient onphysical violence cases against white women. It shows an increase of 0.707 cases of violence,statistically significant at 10%, indicating that there might be some spillover to other races.Finally, the results for indigenous women reinforce the analysis in section 3.5 that they mightbe directly affected by the heritage of slavery, as they were also enslaved during that periodin Brazil. The estimate suggests a sizable effect on cases of physical violence against them,although it is not statistically significant.54(1) (2) (3) (4)White Brown Blacks IndigenousPanel A: Total cases of Violence (per 1,000)Share of Female Slaves (x100) 0.0610 0.0113 0.326*** 0.275(0.0526) (0.0650) (0.0989) (0.216)Observations 257 257 257 256Mean Dep. Var. 0.853 0.892 1.454 1.375Panel B: Physical Violence (per 1,000)Share of Female Slaves (x100) 0.0707* 0.0298 0.289*** 0.323(0.0374) (0.0529) (0.0791) (0.225)Observations 257 257 257 256Mean Dep. Var. 0.666 0.722 1.175 1.188Panel C: Psychological Violence (per 1,000)Share of Female Slaves (x100) 0.0641 0.0608* 0.194*** 0.0282(0.0429) (0.0357) (0.0684) (0.0631)Observations 257 257 257 256Mean Dep. Var. 0.323 0.330 0.558 0.473Panel D: Sexual Violence (per 1,000)Share of Female Slaves (x100) -0.00203 0.00151 0.00889 0.0670(0.00656) (0.0134) (0.0187) (0.0822)Observations 257 257 257 256Mean Dep. Var. 0.0894 0.105 0.166 0.232Panel E: Violence with signs of Torture (per 1,000)Share of Female Slaves (x100) 0.000832 -0.000231 -0.00853 0.0146(0.00170) (0.00558) (0.00689) (0.0159)Observations 257 257 257 256Mean Dep. Var. 0.0289 0.0338 0.0492 0.0473Notes: The dependent variable is the number of cases of violence against women per1,000 inhabitants of that race. All regressions are controlled for 1872 characteristics(total number of slaves, population, share of women, share of whites, share of foreign,share of married people, share of catholic), 2010 characteristics (municipal GDP, pop-ulation, share of urban population, share of females, share of blacks, share of brown,share of indigenous people and literacy rate), latitude, longitude and province FE. Ro-bust standard errors in parentheses. When *** p<0.01, ** p<0.05, * p<0.1.Table 3.8: IV Results - Distance to Corrientes553.6.2 Placebo TestsThe findings in the section 3.5 suggest that a slave gender composition skewed towardswomen led to more cases of violence against black women as a consequence of violencetargeting female slaves in the 19th century. If this is indeed the case, we should not observeany impacts of slaves\u2019 gender composition on cases of violence against males or against poornon-black women.In my initial test, I rerun the main specification using the total cases of violence againstmales in Panel A, the number of cases of physical violence against males in Panel B, andthe number of male homicides in Panel C. All outcomes are measured per 1,000 inhabitantsof the same race and are sourced from SINAN (cases of violence) or Sistema de Informac\u00b8a\u02dcosobre Mortalidade, (SIM) for homicides.As expected, the results presented in Table 3.9 suggest that the share of female slaves isunrelated to violence against males. Interestingly, the point estimates in Panel C indicatethe gender composition of slaves actually has a negative effect on the number of homicides.56(1) (2) (3) (4)White Brown Blacks IndigenousPanel A: Total Cases of Violence against Men (per 1,000)Share of Female Slaves (x100) 0.00916 -0.0262* 0.0309 0.0108(0.0152) (0.0154) (0.0325) (0.179)Observations 259 259 259 258Mean Dep. Var. 0.276 0.278 0.467 1.575Panel B: Physical Violence against Men (per 1,000)Share of Female Slaves (x100) 0.0120 -0.0231* 0.0263 0.0841(0.0125) (0.0136) (0.0270) (0.170)Observations 259 259 259 258Mean Dep. Var. 0.221 0.229 0.381 1.313Panel C: Male Homicides (per 1,000)Share of Female Slaves (x100) -0.0283** -0.0360** -0.0353** -0.0562(0.0112) (0.0155) (0.0172) (0.0514)Observations 259 259 259 258Mean Dep. Var. 0.119 0.179 0.208 0.137Notes: The dependent variable is the number of cases of violence against men per1,000 inhabitants of that race. All regressions are controlled for 1872 characteristics(total number of slaves, population, share of women, share of whites, share of foreign,share of married people, share of catholic), 2010 characteristics (municipal GDP, pop-ulation, share of urban population, share of females, share of blacks, share of brown,share of indigenous people and literacy rate), latitude, longitude and province FE. Ro-bust standard errors in parentheses. When *** p<0.01, ** p<0.05, * p<0.1.Table 3.9: Violence Against MenAs previously mentioned, an important placebo test involves checking if our main variable,the share of female slaves, affects poor non-black women. This is essential to check if theeffect involves slavery or income differences. Unfortunately, SINAN does not collect data onthe victim\u2019s income. To address this limitation, I use cases of violence against women withlow levels of education, defined as those with an incomplete middle school degree, as a proxy.The results, displayed in Table 3.10, align with the previous estimates. The share of femaleslaves only impacts the number of violent cases involving black women with low levels ofeducation, while no effect is observed in cases of violence against women of other races.57(1) (2) (3) (4)White Brown Blacks IndigenousPanel A: Total cases of Violence (per 1,000)Share of Female Slaves (x100) 0.00771 0.00508 0.145*** 0.0137(0.0128) (0.0292) (0.0451) (0.0610)Observations 259 259 259 258Mean Dep. Var. 0.196 0.268 0.539 0.304Panel B: Physical Violence (per 1,000)Share of Female Slaves (x100) 0.00764 0.00904 0.117*** 0.0408(0.0103) (0.0242) (0.0429) (0.0603)Observations 259 259 259 258Mean Dep. Var. 0.153 0.213 0.440 0.256Panel C: Psychological Violence (per 1,000)Share of Female Slaves (x100) 0.0180** 0.0197 0.0972*** 0.000641(0.00819) (0.0155) (0.0351) (0.0225)Observations 259 259 259 258Mean Dep. Var. 0.0798 0.109 0.225 0.0841Notes: The dependent variable is the number of cases of violence against women per1,000 inhabitants of that race. All regressions are controlled for 1872 characteristics(total number of slaves, population, share of women, share of whites, share of foreign,share of married people, share of catholic), 2010 characteristics (municipal GDP, pop-ulation, share of urban population, share of females, share of blacks, share of brown,share of indigenous people and literacy rate), latitude, longitude and province FE.Robust standard errors in parentheses. When *** p<0.01, ** p<0.05, * p<0.1.Table 3.10: Violence Against Women - Low Levels of Education3.6.3 Additional ChecksKelly (2020) states that standard errors might be underestimated if spatial correlation is notproperly taken into account. Therefore, in Table B.7, I use Conley (1999) standard errorsusing different distance cutoffs. All the estimates for cases of violence against black womenhave the same significance level as in the main specification.The last robustness check consists of using the inverse hyperbolic sine of the number of violentcases as a dependent variable. The idea is to test if the results are driven by observations withextreme value, as proposed by Burbidge et al. (1988). The estimates, presented in Table B.8,are very similar to those in the main specification and show an increase in cases of violenceagainst black women due to a higher share of female slaves in 1872.583.7 ConclusionSeveral authors have highlighted the possible long-term impacts of slavery.21 This chapteradds to the literature by investigating how the share of female slaves in a municipality in1872 affects violence against black women today in Brazil. However, this share is likelyendogenous, especially because male and female slaves were seen as suitable for differenttypes of work. The fact that the Brazilian Empire, facing a shortage of soldiers during theParaguayan war (1864-1870), started to draft male slaves for the war, provides a plausible andpositive exogenous variation in the proportion of female slaves in a municipality. Therefore,I use the distance of a municipality to Uruguaiana, the first war front, as an instrument forits share of female slaves.I test this hypothesis using data from the Brazilian Census in 1872 and 2010 and data ongender violence notifications from hospitals. The results indicate that a higher share of femaleslaves in 1872 caused an increase in violence against black women today. A 1 percentage pointincrease in the share of female slaves in 1872 led to an increase of 33.6% in cases of violenceagainst black women per 1,000 black inhabitants, which was mostly driven by increases incases using physical and psychological violence. When I repeat the analysis for cases againstwhite and brown women, I do not find any significant impact of slavery on cases of violenceagainst them.The evidence presented in this chapter indicates that black women still have to bear theconsequences of slavery. I believe that the results might help policy makers develop betterpolicies to prevent violence against black women. Understanding the roots of this problemis the first step to eradicating it and developing a more equal society.21Some examples in the economic literature are: Acemoglu et al. (2012); Bertocchi and Dimico (2014);Buonanno and Vargas (2019); Laudares and Valencia Caicedo (2023)59Chapter 4Expected Discrimination and JobSearch4.1 IntroductionEmployers discriminate along many dimensions, including race, ethnicity, sexuality, and crim-inal history (Neumark, 2018; Rich, 2014; Riach and Rich, 2002). While audit experimentscleanly identify such disparate treatment, they do not reveal the equilibrium effects of dis-crimination. In particular, the equilibrium effects also depend on jobseekers\u2019 beliefs andreactions to discrimination; jobseekers may hold miscalibrated beliefs, and theory shows thatexpected discrimination beliefs can become self-fulfilling (Coate and Loury, 1993). Miscali-bration may be problematic if individuals overestimate discrimination, becoming discouragedor too nervous to give their best performance at an interview. Belief combinations may beself-perpetuating if they make some group appear different on average to recruiters (e.g.,discouraged applicants may invest less in their applications), allowing initial misperceptionsto evolve into actuality. Furthermore, understanding expected discrimination may open newpolicy angles. For example, if jobseekers overestimate discrimination, it might be desirable todisseminate information on actual discrimination rates, and for employers to credibly signalcommitment to anti-discrimination policies.This chapter presents results from three interconnected field experiments with jobseekers,designed to identify how they anticipate and react to discrimination during the applicationand interview stages. Jobseekers in our sample (N=2,200) are favela (urban slum) residentsin Rio de Janeiro, Brazil, where favela residents are negatively stereotyped. We partner witha large cosmetics company to advertise real sales jobs and observe favela jobseekers applyingand interviewing for such jobs. Jobseekers enter our study\u2019s pipeline through our door-to-60door baseline survey, where we find that about 87% of jobseekers overestimate anti-faveladiscrimination \u2013 as measured in an audit study we ran by sending 1,400 job applications.By experimentally varying whether jobseekers expect their addresses to be visible and howmuch discrimination jobseekers may expect, our three labor supply-side experiments revealthat expected discrimination negatively affects interview performance but has a muted effecton job application rates. At the same time, we see that white jobseekers, who are a minorityinside favelas but a majority outside, apply more often and perform better in interviews whenthey believe their addresses are hidden. This could be because, with hidden addresses, whitejobseekers can pass for non-favela residents. Passing is harder for non-whites, who might alsoexpect racial discrimination anyway.In Rio, about 1.5 million people, or 22% of the city\u2019s population, live in favelas. In mostfavelas, criminal organizations hold a monopoly over violence. Favela residents are morelikely to be non-white, immigrants, less educated, and poorer than non-favela residents.The derogatory term \u201cfavelado\u201d, meaning \u201cslummed\u201d, is widely used. In this context, mostrecruiting firms collect home address information from applicants. While this is meant togauge how hard the worker\u2019s daily commute might be, recruiters can also use it to discriminateregardless of distance to work. In our door-to-door survey, over 60% of jobseekers mentionviolent police raids, racial and cultural prejudice, antipathy for favela residents, and fear ofcrime and violence as important reasons why firms avoid hiring people from favelas.Our focus on expected anti-favela discrimination provides two main advantages. The firstis that we can manipulate stigma visibility to randomize expected discrimination \u2013 and bystigmas, we mean the applicants\u2019 characteristics that employers use to discriminate, asso-ciated with negative stereotypes (Loury, 2002). Manipulating the expected visibility of amore visible stigma, like race, would not be as effective since jobseekers would expect it toquickly become visible (e.g., at the interview stage). This also let us study how visible andinvisible stigmas interact: the stigma of living in a favela may be visible or not (similarto a criminal history stigma), and it might compound with or substitute for other stigmas.Here, we study how address visibility interacts with a racial stigma. The second advantageis that we can study a type of discrimination that may be relevant in perpetuating povertytraps in many contexts. Almost a billion people live in urban slums (UN, 2016), and evenin developed countries, we see urban divides (e.g., public housing projects in the US). Canexpected discrimination play a role in perpetuating such divides?Most favela jobseekers overestimate the anti-favela discrimination in callback rates we findin our audit study. For the audit study, we created a set of fictitious workers\u2019 profiles andre\u00b4sume\u00b4s and then made copies that only differed in name, phone, and address. We used themto apply for 700 sales jobs in Rio, sending two different-profile applications to each. We find61very similar callback rates, 19.3 and 19.6%, for favela and non-favela re\u00b4sume\u00b4s (p=0.38 to0.87 for the difference). We incentivized jobseekers in our door-to-door survey to predict ouraudit study\u2019s callback rates. Over 85% predict anti-favela discrimination, while about 60%predict that having a favela address would cause callback rates to drop 50% or more.To measure how jobseekers actually respond to expected discrimination, we set up an HRfirm that advertised real sales job opportunities in a large cosmetics firm.1 At the beginningof the door-to-door survey, after some background questions, jobseekers could agree to sharetheir professional details with this HR firm (described as a partner in the study). Within thenext few days, the HR firm texted the jobseeker with an invitation to apply. Then, since allparticipants met minimal requirements, the HR firm invited all applicants for interviews atits office in Downtown Rio. We used this structure to run three field experiments. In eachexperiment, we randomized an intervention to shift perceptions of discrimination, with twoexperiments at the job application stage and one at the interview stage.Our experiments used two complementary strategies to explore how expected discriminationaffects application rates. Two of our experiments \u2013 the Address Omission and the InterviewExperiment \u2013 randomized expected address visibility, at the application and interview stagesrespectively. The idea behind randomizing expected address visibility is that if jobseekersthink the employer does not know their address, they should not expect anti-favela discrimi-nation. The other strategy was to shift beliefs about market-level discrimination by randomlyinforming some jobseekers about our audit study findings. We describe the Interview Ex-periment first, and we will explain how these approaches complement each other along theway.We ran the Interview Experiment (N=422, out of the 2,200 invited to apply) in an officestaffed with one receptionist and up to two interviewers. We scripted interviews and interac-tions. On arrival, the receptionist asked jobseekers to confirm their name, date of birth, andaddress, then told them to wait. Moments later, the receptionist told the jobseeker that theinterviewer was ready, and that, to keep the process objective, \u201cthe interviewer will only knowyour name\u201d (Name-Only condition) or \u201cyour name and address\u201d (Name-and-Address). Thetwo conditions differ only by two words: \u201cand address\u201d. The interviewer evaluated the can-didate immediately after the interview, and jobseekers filled out a form with self-assessmentquestions at the reception desk before leaving. Interviewers were blind to the whole pro-cedure and learned about the jobseekers\u2019 neighborhood of origin only after the end of theexperiment, so any differences must be triggered by changes in the interviewees\u2019 behaviorsor beliefs.1These are not strongly gendered jobs: in our study, the application rate for males was 37%, and fornon-males, it was 44%.62Our main interview performance measures are aggregates of the interviewers\u2019 and intervie-wees\u2019 evaluations. Interviewers coded, on 0\u201310 scales, i) how well the interviewee performedoverall, ii) how nervous the interviewee was, and iii) how professionally the interviewee be-haved. Interviewees filled out self-assessments for the same three dimensions. To maxi-mize statistical power and reduce the risk of multiple hypothesis testing, we construct aninverse-covariance-weighted index of impressions for the interviewers and for the interviewee(Anderson, 2008). As our primary aggregate measure, we average the two.Hearing that the interviewer will only know one\u2019s name increases the aggregate performanceindex by 0.13SD (p=0.03). The effects are stronger on the self-assessment index (0.17SD,p < 0.01). The effect size on the interviewer\u2019s evaluation index is 0.09SD, and it is notstatistically significant (p=0.28) nor different from the effects on self-assessment (p=0.34).Nevertheless, when we split the sample into groups that expected below-median and at-or-above-median discrimination when predicting the audit study, we see that expected stigmavisibility has a statistically significant negative effect of about 0.2SD on the interviewer\u2019sevaluation index among those expecting high discrimination, consistent with high expecteddiscrimination actually damaging interviewer-assessed performance. Hence, in interviewsoutside our experiment, expected discrimination can exacerbate the effects of whatever dis-crimination exists. It can lead to self-fulfilling prophecies, at least in the narrow sense that ifa jobseeker expects a worse evaluation (because of their address), they indeed get one, evenif there was no discrimination.There is little reason to believe that expected discrimination would have the same effects atdifferent points of the application procedure. The visibility of certain characteristics, stakes,costs, and psychological pressure can differ widely from when filling out an application to thetime of the job interview. To understand the role of expected discrimination at earlier jobsearch stages, and selection into interviews, we conducted two complementary experiments:the Address Omission Experiment and the Information Experiment. Together, they provideevidence that expected discrimination may not play a major role in job application decisions.In the Address Omission Experiment (N=1,303), we manipulate stigma visibility by random-izing the content of the application invite message and the application form. In our maintreatment condition, Address Omission, the text message stated that address informationwas unnecessary at that stage, and the form did not mention address at all. In our StatusQuo condition, the text message listed the home address as necessary information for apply-ing, and people need to fill it in. The address requirement does not affect jobseeker behavior;we find an application rate of 42.7% in Status Quo and 41% in Address Omission (p=0.62for the difference). Considering all the invited applicants, 19.3% of those in Status Quo showup for the interview, and 19.8% in the Address Omission (p=0.64 for the difference).63One possible explanation for the null effect is that people \u201cpass\u201d as non-favela residents (e.g.,by declaring a different neighborhood or a relative\u2019s address) in the Status Quo condition.Consistent with this, 28% of the Status Quo applications obfuscate their address. To explorethis channel, our design included an additional condition, Known Address, in which we shutdown the possibility of obfuscation. Known Address was the same as Status Quo except thatthe online application form already contained the applicant\u2019s home address, and applicantsjust needed to double-check it. Nevertheless, this third experimental condition generatedapplication rates similar to the others. It could be that such differences in expected addressvisibility matter only for those who expect substantial discrimination, but we also see noeffect heterogeneity on that dimension.The manipulation in the Address Omission condition might have been too weak. For instance,jobseekers might have thought that their address would eventually be required anyway. An-other possibility is that our manipulations changed how jobseekers saw the HR firm. Forinstance, those in the Known Address arm might have believed the HR firm preferred hiringpeople from favelas, since they were being contacted despite their addresses. We designedthe Information Experiment (N=690) to circumvent these issues.In the Information Experiment, we manipulated expected market-level discrimination. Therewere three experimental conditions: i) No Info, ii) Favela Info (revealing the audit studycallback rate for a favela), and iii) Full Info (revealing that favela and non-favela callbackrates were the same). Full Info reveals both the discrimination and callback level, so FavelaInfo works as an alternative control condition, holding constant the knowledge of favelacallback rates. We verify that both information treatments shift beliefs by immediatelyeliciting incentivized posterior beliefs about the callback rates the partner HR firm wouldimplement in different neighborhoods. Further, in an endline survey, we see some evidencethat Full Info decreases expected discrimination even after two weeks (at least in relation toFavela Info). Regardless, jobseekers in the three conditions make it to the interview stageat the same rate of about 20%. We also estimate null effects on self-reported applicationsfor other jobs, as measured in our endline survey. We conclude that expected discriminationdoes not affect average application decisions.Race, a stigma correlated with favela residence, strongly predicts treatment effects in theInterview Experiment and partially explains the null results on application rates. In theinterview stage, white applicants benefit more from believing their interviewers knew onlytheir name: for all three performance indexes, we see statistically significant positive effects ofexpecting to have a hidden stigma, and these effects are at least 0.18SD larger than the effectson non-whites. One interpretation of these results is that when white applicants can hide64their addresses, it is easier to pass for a non-favela resident.2 For non-white applicants, evenif their addresses are hidden, they might believe interviewers would still associate them withfavela residents. Another possibility is that visible stigmas are \u201csubstitutes\u201d, i.e., once onestigma is exposed (either race or address), that is enough for jobseekers to expect significantdiscrimination, leading to similar reactions. In our pre-interview experiment (the AddressOmission Experiment), we also find that reducing expected address visibility affects whitejobseekers: they are 57% (9 p.p.) more likely to show up for an interview if they did nothave to declare an address to apply (p=0.05 for the test of a heterogeneous effect of AddressOmission on white jobseekers, against the other two conditions pooled).Our field experiments are the first focusing on estimating the effects of expected discrimina-tion. While many experiments measure whether agents discriminate in the labor market (seeNeumark 2018; Rich 2014; Riach and Rich 2002 for reviews) and other contexts (reviewed inBertrand and Duflo 2017), the supply side has received much less experimental attention.3Three related field experiments experimentally vary the language used in job ads (Del Carpioand Fujiwara, 2023; Burn et al., 2023), or how they describe the selection process (Averyet al., 2023), finding effects on the composition of the applicant pool which could be explainedby expected discrimination. Nevertheless, these studies cannot provide decisive evidenceabout how expected discrimination changes behavior. For instance, the non-gendered (asopposed to gendered) job ads in Del Carpio and Fujiwara (2023) also signal different jobvalues, statuses, or amenities, which can appeal differently to males and females. We gofurther than these experiments in three main ways. First, we elicit incentivized beliefs aboutdiscrimination at baseline, allowing us to estimate whether expected discrimination predictseffect intensity. Second, we designed our experiments to vary only expected stigma visibility,while keeping job desirability and other factors as constant as possible, and our InformationExperiment manipulates market-level expected discrimination, which is not subject to thosesame issues. Third, we provide a more comprehensive picture by also studying face-to-faceinterview performance.2A third of the favela population in Rio self-identifies as white, according to the 2010 Census. Outsidethe favela, that number is 56%. Hence, if white jobseekers are careful not to hint at their home addressby revealing information directly or through how they speak, an interviewer should not guess that they arefavela residents. In interviews, only 4% of all jobseekers revealed that they were favela residents.3A few observational studies find evidence consistent with expected discrimination affecting human capitalacquisition or job search decisions. Several studies document behavior consistent with strategic signaling inresponse to discrimination. That could be, for instance, disclosing more information to separate oneself(Lepage et al., 2022), investing in easily-observed human capital (Dickerson et al., 2022; Lang and Manove,2011), or hiding a stigma even when it is costly (Agu\u00a8ero et al., 2023). Pager and Pedulla (2015) usesadministrative data, complementing it with a survey on earlier experiences with discrimination, and findsthat Black jobseekers cast wider nets in their job searches and that breadth correlates with past discriminationexperiences. Findings from natural experiments in Glover et al. (2017) and Kuhn and Shen (2023) could alsobe consistent with expected discrimination, but it is not possible to pin it down as a mechanism.65We build on two lab studies that test whether jobseekers change how they present themselvesin response to expected discrimination. Kang et al. (2016) shows that non-white college stu-dents craft \u201cwhitened\u201d re\u00b4sume\u00b4s (e.g., listing a Western name or omitting some job experiencethat could reveal ethnicity) but decrease the use of such strategies when asked to craft are\u00b4sume\u00b4 for a pro-diversity employer. A different lab experiment with UK college studentsfinds that females are less likely to pick gender-matching avatars in a virtual labor market ifthey know they will compete for a male-dominated task (Charness et al. 2020). Both studiesshow people may change how they present themselves when expecting discrimination. Wego beyond these studies by studying actual job application and interview performance, andby observing obfuscation strategies in the field.4We also see our study of interview performance as a major contribution. Early work mea-suring employer discrimination (see Riach and Rich 2002) found little discrimination at theinterview phase, and more recent work focused almost exclusively on measuring discrimina-tion at the callback stage.5 The role of interviews has remained understudied, and even ifemployers discriminate less at the interview stage, it can still be the case that anticipateddiscrimination plays a significant role. For instance, Goldin and Rouse (2000) find that fe-male hiring increases after orchestras adopt \u201cblind\u201d auditions. That effect could be bothbecause evaluators lose the ability to discriminate and because females might perform bettermusic knowing that they will be evaluated only on merit.Our study speaks to a broader literature on how beliefs about discrimination can be im-portant. Theoretical work has shown that discrimination can appear without differences ingroup endowments: beliefs might be enough to make a group of workers acquire less humancapital in response to expected discrimination (Coate and Loury 1993; Lundberg and Startz1983). While human capital accumulation decisions are out of the scope of this chapter, weshow how anticipated discrimination can be detrimental later on in the matching process.6As we randomize stigma visibility in two experiments, our study also has a connection withstereotype threat, which is the idea that when people feel at risk of confirming some negativestereotype (e.g., females being worse at math), they may perform worse and confirm that4In a lab-in-the-field experiment, Hoff and Pandey (2006) shows that having a stigma (caste, in theircase) made visible can lead to drops in productivity and risk-taking, which is also consistent with expecteddiscrimination. See also Fryer et al. (2005) for a classroom game using the Coate and Loury (1993) framework,and Aksoy et al. (2023) for an experiment on anticipated discrimination against LGBTQ+ supporters in thecontext of prosocial behavior.5In a study with college and high-school students, Word et al. (1974) provides a thought-provoking studyof how even non-verbal interviewer cues triggered by a racial mismatch between interviewer and intervieweescan lead to worse interview performance. The effects of expected discrimination on the job can also be im-portant. See Glover et al. (2017) and Hoff and Pandey (2006) for empirical studies of on-the-job\/productivitycontexts.6In this sense, we join a recent literature focus on understanding the importance of jobseekers\u2019 beliefsand misperceptions (Spinnewijn 2015; Mueller et al. 2021; Bandiera et al. 2023; Ja\u00a8ger et al. 2022).66prophecy (Steele and Aronson 1995). While the stereotype threat literature overwhelminglyconsiders test performance or other laboratory outcomes (see Spencer et al. 2016 and Liuet al. 2021 for recent reviews), we provide evidence that it can be relevant in a high-stakesjob market context.4.2 Context, Sample, and MisperceivedDiscrimination4.2.1 Favelas in Rio de JaneiroBrazilian favelas are areas of dense informal settlements. In Rio de Janeiro, the state hasbeen unable to hold the monopoly of violence over favelas, which are home to one-fifth of thepopulation. According to the 2010 Census, 66% of favela households had a per capita incomeof one minimum wage (\u224810 USD\/day) or less. Outside the favela, that rate is 30%, and percapita income is 3.5 times larger. Favela residents are also less likely to be literate (84%are literate inside favelas, 92% outside them), to have completed high school or an advanceddegree, or to self-identify as white (33% in favelas and 57% outside).Jobseekers in our study lived in one of three large adjacent favelas in the North Zone of Rio,home to about 200,000 people, or 3% of the city\u2019s population. These neighborhoods grew tooccupy their current areas throughout the 20th century, without proper urban planning orpublic services. They are now part of a contiguous metropolitan area, sharing borders withother favelas and regular \u201casphalt\u201d neighborhoods. We conducted most of our fieldwork inMare\u00b4, which is the most populous favela in Rio and is usually referred to \u201cMare\u00b4\u2019s Complex\u201d,as it is composed of 16 (sub-)favelas.Favela jobseekers have limited formal work opportunities in their own neighborhoods. Forinstance, according to a Census of Mare\u00b4\u2019s Businesses conducted by a local NGO from 2011to 2013, 75% of these businesses were entirely informal. In total, they employed 9% of thefavela\u2019s working-age population (REDES, 2014). Hence, most jobseekers, and especially thoseaiming to build a career, must go outside the favela to find jobs.Residents in all three favelas are regularly exposed to violence or its imminent risk. In Mare\u00b4,three criminal groups \u2013 two of which exploit the illegal drug market, and another workingmainly as an extortion racket \u2013 hold the monopoly of violence. Criminal groups were alsopresent in the two other favelas during our fieldwork, but police were sometimes present in67some of their areas.7 Over our five months of fieldwork, police raids interrupted our surveyactivities 14 times and prevented us from including an extra region in this study. Thesepolice raids are generally unpredictable and violent. During a raid, favela residents will takerefuge at their homes to avoid the crossfire. Workers may miss work days, favela businesseswill close, and communication will be hampered as internet connections may stop working.Furthermore, it is usually unclear when a police raid ends, typically disrupting residents\u2019lives for several days.When there is no police raid in progress, favela residents can typically go in and out ofthe favela without any issues. Some may work in the asphalt neighborhoods adjacent totheir favela or commute to wealthier areas of the city for work. Commuting to these richerareas (e.g., Rio\u2019s Downtown or South Zone) using public transportation may take 30 to 90minutes. The Downtown office of our HR firm, where we held interviews, was within a50-minute commute for almost all participants.4.2.2 Audit Study: Measuring Anti-favela DiscriminationThere is little experimental evidence on whether employers discriminate against favela job-seekers. In Brazil, Westphal (2014) conducted an audit study with re\u00b4sume\u00b4s from differentfavelas and found no discrimination on average \u2013 but with some heterogeneity.8 Since theWestphal (2014) estimates are ten years old, we conducted an audit study to estimate anti-favela discrimination in callbacks for entry-level sales jobs \u2013 similar to the real jobs used inour experiments.We created four fictitious workers\u2019 profiles, two male and two female. Age, job experiences,certifications, and re\u00b4sume\u00b4 templates varied across profiles. All profiles displayed completehigh school, some job experience, and some professional certificates related to sales. Withthe help of a local consultant, we picked characteristics that would not be unrealistic for anunemployed favela resident.For each profile, we created two copies that differed in name, email, phone number, andaddress \u2013 one from Mare\u00b4 and one from Bonsucesso, which is a non-favela neighborhoodadjacent to Mare\u00b4. We selected addresses that unambiguously mapped to either Mare\u00b4 orBonsucesso, and that kept the estimated commuting difference similar between re\u00b4sume\u00b4s fromthe two neighborhoods (see example re\u00b4sume\u00b4s in Appendix C.3). Mare\u00b4 is a widely recognized7See Lessing (2021) for a conceptualization of the symbiotic interaction of such criminal groups and thestate. See also Monteiro et al. (2022) for an empirical account discussing the economic trade-off these gangsface, and Barnes (2022) for an ethnographic account of how gangs have responded to state action in recentyears.8Zanoni et al. (2023) hired recruiters to evaluate favela and non-favela re\u00b4sume\u00b4s in Argentina, findingsubstantial discrimination.68favela in Rio, so employers can immediately tell the Mare\u00b4 re\u00b4sume\u00b4 is from a favela. Also,jobseekers from Manguinhos and Jacarezinho in our Information Experiment acknowledgethat information about Mare\u00b4 and Bonsucesso is relevant for them since they update theirbeliefs about their own neighborhoods similarly to Mare\u00b4 residents when learning about theMare\u00b4 and Bonsucesso callback rates (see Figure C.11).We collected sales job postings (e.g., sales associate, telemarketing salesperson) no olderthan two weeks from five popular job search websites.9 We discarded positions requiringsome skill, experience, or course that any fictitious profiles did not have. We also discardedpositions in neighborhoods more than two hours away by public transport from our set ofaddresses. Then, research assistants applied to each job posting with two different profiles,with randomized addresses.10 We submitted 1,400 applications for 700 jobs between Februaryand May 2023. Research assistants monitored the phone numbers and emails until the endof June and coded all non-automatic, non-negative replies as callbacks.The resulting callback rates are very similar across both groups: for favela resumes, it is19.3%, while for non-favela resumes, it is 19.6%, giving a 0.3 p.p. difference between them(p=0.38 to 0.87, depending on the specification, see Table C.8 for details). These similarcallback rates do not imply a total absence of discrimination against favela residents. Forinstance, if recruiters believe favela residents are ceteris paribus more likely to accept a joboffer, that might offset callback differences caused by anti-favela taste-based discrimination(Kessler et al., 2019). Another possibility is that employers anticipate that some Mare\u00b4residents obfuscate their neighborhood and instead say they live in Bonsucesso (as we observein our experiments discussed below), making the declared address uninformative. Even ifthe audit study measure is imperfect for measuring whether discrimination exists or not, itprovides a real benchmark for jobseekers\u2019 beliefs, allowing us to measure whether they under-or overestimate discrimination in this setting.4.2.3 Perceived vs. Actual DiscriminationIn our door-to-door survey \u2013 discussed in detail in the next section \u2013 we collected incentivizedpredictions of what callback rates we would find in our audit study (similar to the method usedin Haaland and Roth (2021)). We focus on predictions about the jobseekers\u2019 neighborhoodand the adjacent non-favela neighborhood, which are more directly relevant to the perceived9Catho, Indeed, Infojobs, LinkedIn, and Riovagas.10The exact randomization procedure was that, for each job posting, we first randomly ordered the fourprofiles. Then, we randomly picked one of the first two and one of the second two randomly ordered profilesto have favela addresses. A research assistant applied to each posting with two profiles, following the order.The third and fourth profiles were backups, and were only used for gendered jobs. If a job were gendered,the research assistant would still follow the suggested order but skip the profiles of the \u201cwrong\u201d gender. Thisskipping happened in 9% of the selected jobs, and results are similar if we drop those jobs.69discrimination one might suffer, and compare that with our audit study findings.11The top panel in Figure 4.1 compares callback rate predictions against those estimated inthe audit study. On average, jobseekers predict a callback rate of 63% for their adjacentnon-favela neighborhood, with 81% predicting callback rates of at least 50%. Jobseekers\u2019guesses are closer to the audit estimates when estimating callback rates for favelas but are,on average, too optimistic: the average prediction for one\u2019s favela callback rate is 30% \u2013 over50% larger than the audit study estimates.The bottom panel in Figure 4.1 shows the distribution of implied discrimination rates, i.e., thepercent drop in callback induced by having a favela instead of a non-favela address. Here, wesee that 87% predict discrimination (i.e., a decrease in callback), and 84% predict decreaseslarger than the upper bound of our 95% confidence interval for the discrimination rate in theaudit study. The median jobseeker predicts a 50% discrimination rate, substantially morethan the 17.5% upper bound given by our audit study.While audit study measures of discrimination generally do not capture the full picture ofemployers\u2019 discriminatory behaviors (e.g., because they focus only on the callback stageand cover only certain jobs), we expect jobseekers\u2019 predictions of the audit results to bestill informative of the extent to which they expect to face discriminatory behavior. Thatis because i) expected discrimination in the audit study strongly correlates with a Likertmeasure of discrimination and discrimination in relation to a hypothetical \u201cclone\u201d of therespondent in the adjacent non-favela (see Figure C.10), and ii) providing information oncallback rates also decreases an incentivized measure of discrimination regarding the HRfirm (see Section 4.2.2).In our survey, we also asked some (N=1,497) jobseekers about the main reasons why employ-ers would discriminate against favela residents. Jobseekers mentioned a mix of productivity-related and taste-based reasons. The most common reasons were loss of workdays because ofpolice raids (mentioned by 74%), racism (68%), dislike because of cultural differences (e.g.,speech) (66%), and dislike of favela residents (65%).4.3 Experiment Design4.3.1 Sample RecruitmentField Team. We recruited all our surveyors locally, in each favela, through local NGOsnetworks. This strategy guaranteed our door-to-door survey could be conducted safely since11We reach similar conclusions if we instead always use beliefs about Mare\u00b4 and Bonsucesso, which are theaudit study neighborhoods, see Figure C.9)70Audit Estimates0100200300400500Number of Respondents0 10 20 30 40 50 60 70 80 90 100Predicted callback rate (%)Own favela r\u00e9sum\u00e9 Adjacent non-favela r\u00e9sum\u00e9Audit Estimate0100200300400Number of Respondents-50 -25 0 25 50 75 100Predicted callback decrease in audit study if resum\u00e9 is from favela (%)Outside audit's 95% CIWithin audit's 95% CINote: The top panel shows the distribution of the guesses for the callback rates in an audit study using re\u00b4sume\u00b4swith addresses from the respondent\u2019s favela or with that favela\u2019s adjacent neighborhood. The bottom panelplots the distribution of the implied discrimination rates, measured as the percent drop in callback ratecaused by using a favela address. Predictions of more than 50% negative discrimination (i.e., discriminationagainst non-favela residents) are bunched at the leftmost bin. Vertical dashed lines show the audit studypoint-estimates. In the bottom graph, guesses are color-coded by whether they fall into the 95% confidenceinterval of discrimination against Mare\u00b4 (vs. Bonsucesso) re\u00b4sume\u00b4s (calculated using our audit study).Figure 4.1: Predicted vs. Actual Discrimination Ratesfavela residents are more likely to trust other residents, and the local surveyors were ableto quickly identify and avoid risks related to criminal activity or police actions. Our localteams also facilitated obtaining the approval of multiple residents\u2019 associations, the relevantpolitical brokers between the local powers.Sampling. Surveyors worked door-to-door to identify favela jobseekers who: i) were between18 and 40 years old, ii) had completed high school or would complete it by 2023, and iii)were looking for a full-time formal job, even if they were employed. To avoid spillovers (sinceall our randomizations are at the individual level) and maximize privacy, surveyors would a)interview at most one person per household, b) conduct surveys one-on-one, without listeners,and iii) would not knock on homes adjacent to a former participant. Every participantreceived R$5 (\u22481 USD) and was entered into a lottery for R$500 (see Figure C.16 for photosof in-progress interviews).Survey. Surveyors completed 2,392 valid interviews. There were four blocks of questions.71The first block collected general background information and labor market experience. Thesecond block introduced the HR firm as a partner and asked for the jobseeker\u2019s permission toshare their basic background with the firm. The third block was about skills, and the finalblock was about anti-favela discrimination and expectations about one\u2019s future in the labormarket.After collecting background information, the surveyor introduced the existence of a partnerHR firm, which operated in Rio, assisting large companies with their recruitment. Thesurveyor then asked permission to share the respondent\u2019s basic profile information with theHR firm so the jobseeker could receive invitations to apply for available vacancies. We, asthe researchers, operated this HR firm. Our choice not to present the HR firm as part of thestudy was deceptive to the extent that jobseekers could not have anticipated that researcherswould observe their interactions with the firm. This was strictly necessary for the design, andthe only element of deception in this study. We presented the HR firm as separated from thestudy to emulate regular labor market interactions. That is because researchers and researchactivities are commonly linked with local NGOs in that context, and so were some of oursurveyors. Hence, if the surveyors said that the research team directly invited respondents toapply for a job, jobseekers might believe they would receive special treatment. At any rate,the HR firm invited jobseekers to apply for real jobs and indeed acted as an intermediary inthe recruitment process.12,13To describe our survey and sample in more detail, we focus on the 2,167 eligible to participatein our experiments \u2013 167 did not share their data with the HR firm, and 61 of those who didprovided an invalid phone number. Table C.1 presents summary statistics for this sample:62% were recruited in Mare\u00b4, 30% are male, 22% are white, and the average age is 26. Inaddition, 25% had never worked before, and 32% reported currently working full- or part-time(most in the informal sector).After choosing whether to share data with the HR firm, surveyors moved to a block on skills.The block started by asking jobseekers whether they had completed courses or trainingprograms relevant to the job market and then asked for self-ratings on computer and softskills (e.g., punctuality, salesmanship, and leadership). At the end of this block, participantscould take an incentivized one-minute test. The test consisted of answering as many basicalgebra questions as possible to receive an extra R$0.25 for each correct answer. We use thismath test as one of the three components in our skill measure. The other two components12Our debriefing procedures include (i) carefully debriefing those eventually hired by our partner and (ii)inviting participants who applied for the job for a meeting to discuss the study\u2019s findings and the use of theirdata.13For the duration of the study, we kept a website and a contact email running, in case any jobseekersearched online for the firm.72are education (self-reported) and communication skills, which are assessed privately by thesurveyor on a Likert scale at the end of the survey. We standardize and average thesemeasures to form an index and classify those above the median as \u201chigh-skill\u201d.Finally, we move to questions about job market prospects and anti-favela labor market dis-crimination in the fourth block. Almost one-third of our sample has heard of somebody whodid not get (or lost) a job only because they were from a favela, and a similar number re-port having personally suffered the same. Before initiating the Information Experiment, oursurvey also included questions on why jobseekers believed firms would discriminate againstfavela residents.Measuring Expected Discrimination. As our main measure of expected discrimination,we incentivized jobseekers to predict the callback rates we would find in our audit study,paying an extra R$100 (\u224820 USD) to the ten people who got closer to the true estimates(see Figure C.17 for the full elicitation script). For both Mare\u00b4 and Manguinhos, we usedBonsucesso as the adjacent non-favela neighborhood. For Jacarezinho, we used Maria daGrac\u00b8a since Bonsucesso is not immediately adjacent (see Table C.2 for Census summarystatistics for each neighborhood). As our audit study compared only Mare\u00b4 and Bonsucesso,we elicit incentivized predictions for these other neighborhoods by initially stating that weonly knew the correct answer for some of the questions and would pay incentives based onthose.Partners. To advertise real jobs to participants, we partnered with one of Latin America\u2019slargest cosmetics franchise and retailer chains. This firm is interested in increasing diversityamong its workers and allowed us to advertise three entry-level sales jobs. They committedto giving full consideration and fast-tracking promising applicants recruited through ourpipeline. We partnered or kept in touch with several NGOs in each favela. These institutionswere extremely important since they could provide recommendations on locals who couldwork as surveyors, as well as feedback and advice on our survey, logistics, and researchquestions.14Overview of the experiments. Figure 4.2 shows how the Address Omission, Information,and Interview experiments fit together. We introduced the Information Experiment as wephased out the Address Omission Experiment.15 Hence, the sample in each of those pre-interview studies differ with respect to their favela of origin and some other covariates (seeTable C.6 for a comparison). All jobseekers who completed the application form and attended14We are also working with a Jacarezinho NGO to produce a policy report and disseminate our findingslocally, on the media, and inform policymakers.15There was an overlap of 174 participants between the two pre-interview experiments when phasing outthe Address Omission Experiment and launching the Information Experiment. For simplicity, the main textpresents results for the non-overlapping samples.73the interview participated in the Interview Experiment.Note: The figure shows a simplified diagram of the flow of participants from door-to-door survey to jobinterview, for the earlier and later fieldwork periods. See Section 4.3.1 for details.Figure 4.2: Experimental Design4.3.2 Address Omission Experiment (N=1,303)As the door-to-door survey proceeded, we organized the applicants in batches for the AddressOmission Experiment. Every few days, the HR firm would send personalized invitations toapply via WhatsApp to a new batch of applicants, each applicant receiving a unique link.Batch sizes varied from 50 to 117 to accommodate logistical capacity. Given that, mostjobseekers received invitations to apply up to ten days after answering the door-to-doorsurvey.Treatment. In this experiment, we randomize the expected stigma (address) visibility atthe application stage. The application invite and application form sent to each applicantcould belong to one of three experimental conditions i) Address Omission, ii) Status Quo,and iii) Known Address. Applicants in Address Omission received a WhatsApp messagefrom the HR firm inviting them to apply and saying that a home address is not needed forapplying. Those in Status Quo and Known Address receive a message saying an address isneeded. See the exact messages below. The difference between the experimental conditionsin which the address is necessary is that in Status Quo, the jobseeker fills in the address(the common practice in our context), allowing us to observe how often applicants obfuscatetheir real addresses. In Known Address, the form states that the research team has sharedthe jobseeker\u2019s address (besides name and phone number), so they just need to double-checkit. Hence, in Known Address, we make sure that obfuscation is not possible, allowing usto test whether making address visible affects application behavior (see Figure C.19 for thedifferences across forms).74WhatsApp Invite Messages:Hi [NAME], how are you? This is Vanessa from SAM HR. I\u2019m contacting youbecause you are one of the people in our database who fits the requirements forsome of our vacancies. In addition to salary, these jobs offer benefits such asdaycare and health insurance.You have been selected to participate in one of our streamlined processes! In thisstage, you need to provide your education and any courses or experiences.Your home address is [NOT\/ALSO] required.It takes just 5 minutes! Personal link: go.samrh.com\/lyhW1DS5The application form started with a brief description of three full-time jobs: i) (in-store)Sales Consultant, ii) Direct Sales Promoter, and iii) Direct Sales Supervisor with our partner(see Figure C.18 for full job descriptions). Then, it confirmed the jobseeker\u2019s name, phonenumber, and address (or not, as implied by each treatment arm). Then, it proceeded as astandard application form and ended with a screen in which the jobseeker had to declaretheir availability for an interview.Outcomes. Our main pre-registered outcomes relate to application progress: (i) clickingthe link in the WhatsApp message to open the application form, (ii) application completionrates, and iii) interview show-up rates. The latter typically takes place up to two weeks afterapplication since the HR firm could always schedule an interview within days of the appli-cation completion. The click-through outcome happens before the differentiation betweenStatus Quo and Known Address, so we should not expect any difference in click-throughrates between those arms.Address Obfuscation. We also calculate the address obfuscation rate for those in the StatusQuo arm. We consider that a favela jobseeker has obfuscated their address if the declaredneighborhood is neither a favela nor the postal service neighborhood of the jobseeker\u2019s realaddress (recorded by the surveyor in the door-to-door survey).4.3.3 Information Experiment (N=690)The Address Omission Experiment ran until May 2023. In the following month, we embeddedthe Information Experiment in our door-to-door survey (which proceeded to cover all threefavelas) to address two limitations of the Address Omission Experiment. First, jobseekers inthe Address Omission arm might have believed their addresses would be required or revealedanyway in later stages of the application procedure, leading to a weak treatment. Second,while we only vary the information required for applying, there could still be a concern thatthis changed perceptions of other characteristics of the selection procedure or the job. Hence,75the Information Experiment aimed to manipulate beliefs about market-level discrimination.Treatment. We randomized participants into three treatment arms: (i) Favela Info, in whichwe disclosed only the favela\u2019s callback rate (19.3%, from our audit study), (ii) Full Info, inwhich we showed both the favela and non-favela callback rates (19.6%) \u2013 thus revealing thatwe find no discrimination in callback rates, and (iii) No Info, in which no information wasdisplayed. See Figure 4.3 for the graphs the surveyors used to convey the treatment.Similar to the Address Omission Experiment, the HR company later invites respondents toapply for our partner\u2019s jobs, with two main differences. First, to emulate the most realisticapplication procedure, we only use Status Quo procedures (i.e., we ask applicants to providetheir home address). Second, since there is no randomization in the application procedure,we can decrease the batch size and invite jobseekers to apply more often, one to four daysafter they answer the door-to-door survey.(a) Favela Info (b) Full InfoNote: This Figure shows the images we used to convey the Information Experiment. We showed either oneof the plots (or none) to participants immediately after the belief elicitation presented in Figure C.17. Thesurveyor read the text above each graph when showing it to the respondent.Figure 4.3: Information Treatment DeliveryOutcomes. Besides the application progress outcomes used in the Address Omission Ex-periment, we also pre-registered address obfuscation and immediate belief updates as mainoutcomes. As updated beliefs, we chose the incentivized predictions of what callback ratesthe partner HR firm would implement in each neighborhood. There is no ground truth forthese callback rates, since we operated the HR firm and invited only favela jobseekers toapply. We incentivized these beliefs by including them in the set of questions in which weelicited beliefs about our audit study callback rates. The surveyor introduced this set ofquestions with a statement clarifying that we only knew the answer to some of the questions,and accuracy would be calculated based on those.Endline survey. We conducted an endline survey to check whether the belief shift caused by76the Information Experiment persisted and to collect a self-reported number of job applicationssent after answering the door-to-door survey. To minimize attrition, we only asked multiple-choice questions with four possible choices each. We asked these questions over WhatsApptwo weeks after each jobseekers participated in the survey. As a participation incentive,respondents were entered into a lottery for R$200 (\u224840USD).4.3.4 Interview Experiment (N=422)The HR firm invited all jobseekers who completed the application form for a job interviewin an office in Downtown Rio. Attendees received a R$25 (\u22485 USD) transport subsidy \u2013enough to cover bus fares and a meal. We rented a reception desk and interview rooms ina co-working space, so applicants first had to go through the building\u2019s reception and thentake the elevator up to the co-working floor. Interviews took about ten to fifteen minuteseach, and we scheduled them with enough of a gap so that jobseekers would rarely, if ever,meet or interact at the premises. Appendix C.20 presents pictures of the co-working space.Treatment. In this experiment, we randomize expected stigma visibility at the job in-terview. A receptionist greeted jobseekers when they reached the right floor. Next, thereceptionist asked to confirm the applicant\u2019s name, date of birth, and address and told themto wait. Moments later, the receptionist told the jobseeker that the interviewer was ready,and, to keep the process objective, \u201cthe interviewer will only know your name\u201d (Name-Onlycondition) or \u201cyour name and address\u201d (Name-and-Address). Hence, the conditions differedby two words only: \u201cand address\u201d. Interviewers were blind to the whole procedure untilthe end of all interviews. Later, we debriefed the interviewers to learn their impressionsand avoid participant deception \u2013 i.e., \u201cthe interviewer will know your name and address\u201dwas an ambiguous statement with respect to timing and the exact address information theinterviewer would eventually receive.Interview. We hired an experienced HR consultant to revise our interview script and trainour two interviewers. The script contained a set of standard interview questions for sales jobs.For instance, it included questions about strengths, weaknesses, the candidate\u2019s comparativeadvantages, and past work experiences. The interview also included an activity where theapplicant had to pick an item and provide a sales pitch for it (see Appendix C.4.2 for thecomplete script).Outcomes. The interviewer evaluated candidates immediately after each interview, andinterviewees filled out a form with self-assessment questions at the reception desk beforereceiving the transport subsidy. Interviewers coded, on 0\u201310 scales, i) how well the intervie-wee performed overall, ii) how nervous the interviewee was, and iii) how professionally theinterviewee behaved. Interviewees filled out self-assessments for the same three dimensions.77We construct z-scores for each of the six dimensions by normalizing the scores by the meanand standard deviation of those in the Name-and-Address condition. For the interviewer-assessed dimensions, we normalize interviewer-wise to account for fixed effects and dispersiondifferences across interviewers.To maximize statistical power and reduce the risk of multiple hypothesis testing, we constructan inverse-covariance-weighted index of impressions for the interviewers and for the intervie-wees (Anderson, 2008). As our primary aggregate measure, we average the two. While thisaveraging risks mixing different dimensions, it allows us to extract a more accurate signal.At any rate, we also present broken-down estimates in the main text.4.3.5 Randomization, Balance, and EstimationRandomization for the Address Omission Experiment proceeded in batches. We assignedtreatments with the same probability, stratifying by expected discrimination (batch-wise),with equal probability of each treatment within each stratum. We proceeded similarly forthe Interview Experiment, randomizing in batches after jobseekers completed the applicationform. Nevertheless, due to logistical issues, we had to randomize the treatment status of someparticipants as they arrived at the interview office. The offline survey app on the surveyors\u2019tablets implemented the randomization for the Information Experiment on the spot \u2013 alsowith the same probabilities. All randomizations were independent across experiments.Tables C.3, C.4, and C.5 display randomization balance checks. Given the necessity ofrandomizing batch-wise (for the Address Omission Experiment and Interview Experiment)or on the spot (for the Information Experiment), we could not stratify on multiple variablesor at all in the latter case. Hence, we see some imbalances. Out of the 45 comparisons tothe \u201ccontrol\u201d groups in Tables C.3, C.4, and C.5, one is significant at the 1% level, three atthe 5% level, and four at the 10% level, which is not far from what one would expect fromrandomness.To test for the effect of expected stigma visibility in the application procedure and plot theaverage outcomes of each experimental group, we estimate a saturated model:yi =\u03b2SQStatus Quoi + \u03b2KAKnown Address i + \u03b2AOAddress Omission i + \u03b5i (4.1)where yi \u2208 {0, 100} (to yield percentages), and each coefficient captures the outcome level foreach treatment group. Given randomization, results with controls are very similar. We showresults with double-lasso selected controls in Appendix C.1. We present robust standarderrors for all models, calculating the variance-covariance matrix using the HC3 approach(Long and Ervin, 2000).78We use the same specification as in Equation 4.1 to estimate average treatment effects inthe Information Experiment (i.e., one indicator for each treatment). We also conduct anadditional exercise to estimate the effects of shifts in expected discrimination and expectedown-favela callback rate on application outcomes. That is, assuming our treatments onlyaffect application through beliefs, we use Favela Info and Full Info to instrument the posteriorbeliefs about the discrimination rate the HR firm to estimate:yi = \u03b1 + \u03b2discPosterior Discrimination i + \u03b5i, (4.2)where Posterior Discrimination i is the expected HR firm callback percentage decrease dueto a favela address. Under the IV assumptions, estimating \u03b2disc yields a quantitative testof how expected discrimination affects application outcomes, leveraging variation from bothtreatments. As our information treatments can shift the expected callback rate level, we alsoestimate:yi = \u03b1 + \u03b2\u02dcdiscPosterior Discrimination i + \u03b2favelaPosterior favela callback rate i + \u03b5i, (4.3)allowing us to estimate the effects of expected discrimination rates and the expected callbacklevel. For the IV specifications, we focus on overestimators of both Posterior Discrimination iand Posterior favela callback rate i to guarantee our instruments have a monotonic effect onthe endogenous variable.Our interview performance outcomes are normalized z-scores, or their inverse-covariance-weighted averages (Anderson, 2008). Hence, only differences across groups are informative,and we simply estimate:yi = \u03b1 + \u03b2NOName-Only i + \u03b5i. (4.4)To show robustness to the inclusion of controls, we pick them flexibly using double-lasso.Finally, we pre-registered four heterogeneity analyses: by expected discrimination, race, skill,and gender. The heterogeneity by expected discrimination is key to confirming our mecha-nism of interest. For comparisons, we define the group of jobseekers expecting high discrim-ination as those who expect 50% discrimination or more when predicting the audit study(i.e., at or above median).16 The race heterogeneity allows us to observe how the favelastigma interacts with an always-visible stigma correlated with favela residence. The skillheterogeneity could tell us how expected discrimination changes the talent pool available toemployers, and the gender heterogeneity can inform us about whether favela males \u2013 whoare more likely to be gang members \u2013 or females react more to expected discrimination. We16This definition pools jobseekers who expect fairly high discrimination rates with those who expect none.Nevertheless, results are similar when considering a cut-off of, for instance, 25%.79discuss the heterogeneity by expected discrimination together with our main results (since itis our mechanism of interest), and we present all four heterogeneity breakdowns in AppendixC.1.4.4 Results4.4.1 Address Omission ExperimentAddress visibility does not affect average job application rates (left panel, Figure 4.4).If expected discrimination discourages applications and expected stigma visibility dictateswhether the jobseeker should expect discrimination, we should see Address Omission in-creasing application rates in comparison with Status Quo (unless jobseeekers use strategieslike obfuscation to fully avoid expected discrimination under Status Quo). Known Addressshould do the reverse, except for the clicking outcome, since the difference between StatusQuo and Known Address is whether the application form address field is pre-filled or not.Instead, we see little variation across treatments: click-through rates hover just over 60%,form completion rates hover from 41% to 45%, and interview show-up rates are just below orat 20%. The p-values for tests of equality between any two conditions for all three applicationoutcomes are all above conventional significance thresholds.The right panel in Figure 4.4 presents results for the subgroup that should react the most tostigma visibility: those who expect discrimination of 50% or more in the audit study. We seea very similar pattern, providing no evidence that expected discrimination affects averageapplication rates.At the same time, we observe address obfuscation in the Status Quo arm, consistent with astrategic reaction to expected discrimination. In that arm, applicants were free to declaretheir addresses, and 25% declared obfuscated addresses. Conditional on applying, that rate is45%. We also verify that the Known Address treatment is effective in preventing obfuscationsince only 8% of the applicants in that condition provide a corrected address in place of theone recorded by the surveyor, and none tried to obfuscate their neighborhood. Hence, thetreatment arms changed the address the jobseekers expected the firm to know, at least atthe moment of application.Three theories could explain the null results. First, jobseekers might have believed thatrecruiters would eventually figure out their neighborhood of origin, and that, in such case, anygains from hiding address in the initial stage would be erased. Second, jobseekers may haveinferred more than just variation in stigma visibility when reading the ads. For instance, somein the Known Address arm might have inferred that the HR firm was especially interested80Note: This figure displays shares of all jobseekers in the Address Omission Experiment reaching each stageof the application process. Clicked, means clicking the link in the WhatsApp invite. Applied stage meansfinishing the online application form, and Show Up means showing up at the interview. The left panelshows results for the full sample, and the right panel shows results conditional on expecting 50% (median)discrimination or more when predicting the audit study. Sample size in each arm is shown at the bottom ofeach bar. Vertical error bars display 95% confidence intervals, and horizontal bars with tips show p-valuesfor pairwise comparisons above them.Figure 4.4: Effects of Address Omissionin favela workers, since they were invited despite the firm knowing their addresses. Third,expected anti-favela discrimination might not have been marginal in the application decision.For instance, jobseekers might have used simple heuristics to decide whether to apply, e.g.,whether they need a job, and whether the job opening fits their schedule or skills. OurInformation Experiment avoids the issues related to the first two explanations, since it shiftsbeliefs about market-level discrimination.4.4.2 Information ExperimentWe begin by discussing the \u201cfirst-stage\u201d effects of learning the callback rate estimate of19.3% for the favela re\u00b4sume\u00b4s (taken from our audit study) in Favela Info. Learning FavelaInfo does not change the average expected callback rate for jobseekers\u2019 own neighborhoods \u2013see Figure 4.5. That is because the effects on under- and overestimators of the favela callbackrate balance out. For instance, considering only overestimators, the average expected callbackrate goes from 41% in No Info to 37% in Favela Info (p=0.09, see Figure C.3 for effects onunder- and overestimators of the favela callback rate). When jobseekers learn both callbackrates in Full Info, underestimators become even more optimistic about their own favelacallback rates, and overestimators become more pessimistic. For both subgroups, there isa statistically significant shift in expected callback for one\u2019s own favela when learning Full81Info. Hence, jobseekers use favela and non-favela information to update about favela callbackrates.Considering beliefs about the non-favela callback rate, we also see that jobseekers use in-formation on both favela and non-favela callback rates to update. Since 92% of the sampleoverestimate the non-favela callback rate, that update is evident even when looking at thefull sample in the top-right of Figure 4.5. Hence, both Favela Info and Full Info decreaseexpected discrimination, and the decrease is larger for Full Info since it provides more infor-mation. The average posterior discrimination rate for the No Info, Favela Info, and Full Infogroups are, respectively, 35%, 28%, and 15%, with group differences significant at the 5% or1% level. The top-right graph in Figure 4.5 shows a similar pattern for the subsample whoexpected high discrimination from the start.Before proceeding, consider what would be the effect of shifting beliefs about one\u2019s ownfavela callback rate on application. A simple model in which agents do not care about non-favela callback rates shows that applications may either increase or decrease with callbackprobability. Let n be the number of applications chosen by the jobseeker, p be expectedcallback probability, c a constant marginal cost and the callback value V (n, p) be such thatVn > 0 and Vnn < 0. If the jobseeker maximizes V (n, p) \u2212 nc finding an internal solution,the inverse function theorem yields \u2202n\u2217\u2202p= \u2212 Vnp(n\u2217,p)Vnn(n\u2217,p) , which has the same sign as Vnp(n\u2217, p).Taking, for instance, a jobseeker that only cares about getting the first callback, i.e., V (n, p) =1 \u2212 (1 \u2212 p)n, then one can have Vnp(n\u2217, p) > 0 for low p and Vnp(n\u2217, p) < 0 for high p.Intuitively, at a low p, an increase in p makes a marginal application more valuable. But, ifyou already expect to receive \u201cenough\u201d callbacks, an increase in p allows you to decrease thenumber of costly applications while still getting enough callbacks.Learning how the non-favela callback rate compares to the favela callback might also changeapplication decisions in different ways. For instance, for a jobseeker with initially accuratebeliefs about callback rates, information can still increase applications if it decreases expecteddiscrimination in later stages (e.g., the interview). And for a jobseeker that has overlyoptimistic beliefs but acts according to the model above, Favela Info and Full Info can havereinforcing or opposite effects on applications since Full Info can lead to a stronger updatein p, with a potentially non-monotonic application response.In the bottom-left of Figure 4.5, we see that the average click rates are 60% for the No Infogroup, 68% for the Favela Info group (p=0.1 in comparison to No Info), and 67% for the FullInfo group (p=0.14 in comparison to No Info). We see a similar pattern (i.e., informationincreases application) considering the shares of jobseekers completing the application form,but those increases are not significant. These increases in the initial interest in the jobconcentrate in the group that initially overestimate the Mare\u00b4 callback rate (see Figure C.3).82Still, the pattern vanishes when considering interview attendance. These results suggest thatsome jobseekers behave as in the model above, in which they might initially expect to have\u201cenough\u201d callbacks, but increase application rates when they learn the callback rate is lowerthan expected.The bottom row in Figure 4.5 also includes average obfuscation rates by information con-dition. Applicants in Favela Info obfuscate the most, and the difference is larger in thesubsample expecting higher discrimination. That would be consistent with strategic obfus-cation: if I learn that my neighborhood\u2019s callback rate is lower than expected, obfuscationbecomes more attractive. If I further learn that using an adjacent non-favela address (i.e.,the typical obfuscation strategy) does not lead to higher callback rates, obfuscation ratescan decrease again. Nevertheless, we only see one statistically significant difference: in thegroup expecting high discrimination, those receiving Favela Info apply obfuscating 13% ofthe time, more than double the share in No Info (p=0.1). When breaking up the sample bythose who underestimated or overestimated discrimination, we see that Favela Info seems todecrease obfuscation for underestimators and increase it for overestimators, consistent withstrategic obfuscation.As we are interested in describing the effects of beliefs on applications, and since both infor-mation treatments shift both types of beliefs (about callback level and discrimination), wepresent IV estimates of the effects of both beliefs in Table 4.1. To guarantee a first stage, wefocus on the subsample that overestimates the favela callback and discrimination rates (asour treatments lower both beliefs). Regardless of whether we only instrument the posteriordiscrimination rate or also include the posterior beliefs about one\u2019s own favela callback rate,we see no statistically significant effects of beliefs on application behavior. Considering pointestimates, the only cases when expected discrimination discourages application is when weconsider clicking and completing the form as outcomes, without including own-favela beliefsin the estimated equation. Considering the application-progress outcomes when we includeown-favela beliefs (columns (5) to (8) in Table 4.1), point estimates suggest that jobseekersthat overestimate the favela callback (and are affected by the treatment) are in the regime inwhich they already expect \u201cenough\u201d callbacks and the difference in application rates mattersless (as in the toy model previously discussed). The point estimates of the effects on obfus-cation rate in the more flexible model (column 8) also suggest that jobseekers strategicallydeclare a neighborhood that would maximize their callback rates. So, another reason we donot see people being discouraged from applying when they are told they were too optimisticmay be because they have the option to obfuscate in such cases.83Note: The top row of graphs displays average posterior beliefs of what callback rates the HR firm wouldimplement for jobseekers in each experimental condition. Non-favela and Own favela stands for the callbackrate prediction for a respondent\u2019s favela and adjacent non-favela. Disc is the implied discrimination rate.The bottom row displays outcomes from the application process. Clicked, means clicking the link in theWhatsApp invite. Applied means finishing the online application form, and Show Up means attending theinterview. Obfuscates in app means declaring (in the application form) a neighborhood that is neither afavela nor the postal service neighborhood of the true address. The left column of graphs shows results forthe full sample, and the right column shows results conditional on expecting 50% (median) discriminationor more when predicting the audit study. Sample size in each arm is shown at the bottom of each bar.Vertical error bars display 95% confidence intervals, and horizontal bars with tips show p-values for pairwisecomparisons above them.Figure 4.5: Information Treatment Shifts Beliefs, But Not Interview Show-up(1) (2) (3) (4) (5) (6) (7) (8)Clicked (%) Applied (%) Show Up (%) Obfuscates in app (%) Clicked (%) Applied (%) Show Up (%) Obfuscates in app (%)Posterior Exp. Disc. (%) -0.289 -0.217 0.031 0.007 0.924 0.703 0.152 0.886(0.343) (0.346) (0.277) (0.192) (1.602) (1.290) (0.591) (1.193)Own favela -4.457 -3.380 -0.446 -3.231(5.185) (4.107) (1.902) (3.847)Observations 447 447 447 447 447 447 447 447Sample Overestimators Overestimators Overestimators Overestimators Overestimators Overestimators Overestimators OverestimatorsNo Info Mean 56.85 37.67 19.18 6.16 56.85 37.67 19.18 6.16Note: Two-stage-least square estimates of the effect of posterior beliefs about discrimination on applicationoutcomes. The instrumented variable is the predicted drop in the HR firm\u2019s callback rate, and the instrumentsare information treatment dummies (Favela Info and Full Info). See Figure 4.5 notes for definitions of theoutcomes. Sample includes only individuals who overestimated the audit study discrimination rate. Robuststandard errors between parenthesis.Table 4.1: IV Estimates of How Expected Discrimination Beliefs Affect ApplicationRates84Our endline survey generally confirms the findings above. There was no differential attritionin participation \u2013 Table 4.2, column (1). In column (2), there is evidence that the decreasein expected discrimination caused by Full Info persists for at least two weeks, at least incomparison with Favela Info (p=0.06). In a pooled comparison of Full Info against the twoother arms (not shown in the table), we see p=0.09. Nevertheless, in column (3), we stillsee null results on application rates, but now on a self-report of the total number of jobs therespondent applied to in the last two weeks.(1) (2) (3)Responded toendline (0\/1)Expecteddiscrimination(categorical, 1-4)# of apps sent(categorical, 1-4)Favela Info 0.020 0.060 -0.019(0.046) (0.097) (0.135)Full Info 0.017 -0.116 0.021(0.047) (0.103) (0.142)Observations 690 389 389Controls No No NoNo Info Mean 0.55 2.29 2.53Favela=Full p 0.96 0.06 0.76Note: Information Experiment treatment effects on endline survey outcomes. The outcome in column (1) isa dummy for responding the endline survey. The outcome in column (2) takes values from one to four, codingfor believing that a favela jobseeker would [NOT suffer=1\/suffer A BIT more=2\/ suffer A LOT more=3\/sufferEXTREMELY more=4] discrimination than someone from the adjacent non-favela when applying to jobs.The outcome in column (3) equals 1 if the jobseeker applied for zero jobs, 2 if applied for a single job, 3 ifapplied from two to five, and 4 if applied for more jobs than that over the last two weeks. Robust standarderrors are shown in parentheses.Table 4.2: Information Does Not Affect Application Rates at Endline4.4.3 Interview ExperimentWe do not see evidence for expected discrimination affecting application rates in both pre-callback experiments. Nevertheless, expected discrimination could still damage interviewperformance since there are many differences between the application decision and one\u2019sbehavior in an interview. During the interview, the jobseeker must quickly adjust behavior85in response to the interviewer, who directly observes and judges performance, making theinterview interaction very different from the \u201ccold\u201d decision of whether to apply. Hence, wemight see expected discrimination affecting performance in the Interview Experiment.Hearing that the interviewer will only know the interviewee\u2019s name increases interview perfor-mance (top panel, Figure 4.6). Regardless of whether we use double-lasso to select controls,the direction of the effects on all performance dimensions (three self- and three-interviewerassessed) is consistent with a negative relationship between stigma visibility and interviewperformance. When we aggregate all the self-assessed dimensions into an index, we get anaverage effect of 0.17SD, with p < 0.01, regardless of whether we use double-lasso. For the in-dex of the interviewer-assessed dimensions, we see a non-significant effect of 0.09SD (p=0.28)without controls and a smaller estimate with controls. We also cannot reject that the dif-ference between the effects on the interviewer- and self-assessment index is zero (p=0.34 or0.33, with or without controls). The effect on the aggregate index is 0.13SD (p=0.03) withoutcontrols and 0.1SD (p=0.06) using double-lasso.The average treatment effects leave us in a position of ambiguity since we do not havepower to reject the null of no effect of stigma visibility on the interviewer assessment. Oneway to proceed is to consider that both the interviewer- and the self-assessed indexes arenoisy measures of interview performance and then use the aggregate index as our best guessfor both. Nevertheless, there might be bias in jobseekers\u2019 self-assessments. Another way toproceed is to check whether our hypothesized mechanism (i.e., expected discrimination) worksfor both the self- and the interviewer-assessed measures. If interviewers see those expectinghigh discrimination as worse performers when they believe their addresses are visible, thatwould be evidence that expected discrimination hurts performance.The bottom panel in Figure 4.6 shows that the effects on the index outcomes strongly con-centrate on the group expecting high discrimination from the start, consistent with expecteddiscrimination hurting performance. This pattern is the same regardless of whether we lookat the interviewer- or self-assessed index. When looking at the subgroup expecting 50% ormore discrimination (at or above the median), we see performance increases of about 0.2SD,no matter which index we look at. These effects are always significant \u2013 one of them atthe 10%-level and all others at 5% or less. Comparing the effects on the low- against high-expected discrimination group yields statistically significant differences at the 5%-level whenthe outcome is either the interviewer or aggregate index. Hence, expected discriminationhurts interview performance \u2013 as assessed by the interviewer \u2013 at least for those who expecthigh discrimination from the start.86Double-lasso ControlsNo Controls  Aggregate IndexSelf IndexOverall PerformanceCalmProfessionalInterviewer IndexOverall PerformanceCalmProfessional-.5 -.4 -.3 -.2 -.1 0 .1 .2 .3 .4 .595% CI90% CIdiff p-val=0.04 (No Controls) 0.04 (Double-lasso)diff p-val=0.220.24diff p-val=0.050.04Double-lasso ControlsNo ControlsAgg.*High Exp. DiscAgg.*Low Exp. DiscSelf*High Exp. DiscSelf*Low Exp. DiscInterv.*High Exp. DiscInterv.*Low Exp. Disc-.5 -.4 -.3 -.2 -.1 0 .1 .2 .3 .4 .5Effect of Name-Only on Interview Performance (SDs)95% CI90% CINote: The top graph shows average treatment effect estimates using either no-controls (blue) or double-lassoselected controls (red). The interview performance outcomes are listed on the left-hand side and described inSection 4.3.4. The bottom graph shows estimates of heterogeneous effects by expected discrimination. Foreach outcome, we estimate a single model with saturated dummies for expected discrimination, and we showp-values for the equality of the effects on both groups in the left-hand side. Thicker error bars show 90%confidence intervals, and thinner bars show 95% intervals.Figure 4.6: Expected Stigma Visibility Affects Interview Performance, Especially forthe Group Expecting High Discrimination4.5 Discussion4.5.1 Race and Stigma VisibilityIn our door-to-door survey, 68% of jobseekers mentioned racism as an important reasonwhy employers discriminate against favela residents, and 70% believe firms discriminate alot against Black jobseekers.17 Furthermore, white people are a majority of the populationoutside favelas, but only one-third of the favela population. Hence, race is a visible stigma17In the original survey, we use the word \u201cnegro\u201d, which according to the Census classification means thesum of \u201cpreto\u201d (most closely translate to \u201cBlack\u201d), and \u201cpardo\u201d, which may be thought of as \u201cmixed-race\u201d,commonly of partly African descent.87correlated with favela residence, an \u201cinvisible\u201d stigma. These stigmas can interact in differentways, and we highlight two of them. First, a visible stigma might hint at an invisible one sincethey are correlated. Hence, a white jobseeker may easily pass for a non-favela resident (ifthey are careful about what information they disclose directly and in their way of speaking),but that is harder for non-whites. This asymmetry suggests that address visibility can bemore relevant for white jobseekers, since non-white jobseekers might always expect to beenseen as a favela resident with high probability. Second, jobseekers might be similarly stressedor expect employers to treat them similarly no matter whether one or more stigmas arevisible (e.g., one source of expected discrimination might be enough to discourage). In thelatter case, since race is always eventually visible, we should further expect null effects onnon-whites. In both of these mechanisms, the visibility of the race and address stigmas workas substitutes. We will show evidence of that substitutability in this section.At the job interview, race becomes immediately visible. In the top-right panel in Figure 4.7,we see that expecting address to be hidden during the interview increases performance forwhite jobseekers by about 0.3SD for the aggregate and the broken-down indexes, and theeffect is always significant at least at the 10%-level. Further, the effects on non-whites are atleast three times smaller (but still significant at the 10% level, considering the self-assessedindex), suggesting that these stigmas act more as substitutes than complements.Moving back to when we randomized address visibility at the Address Omission Experiment,we see that white jobseekers applied and showed up more often when the invite messagesaid their addresses were not necessary at the application stage \u2013 see the bottom of Figure4.7. Furthermore, white jobseekers are about twice as likely to attend an interview underthe Address Omission treatment compared to the Known Address treatment. In a pooledcomparison of Address Omission against the two other arms, we see a 10 p.p. increase in theapplication (p=0.1) and show-up (p=0.05) rates. Those are large increases, of 25% and 57%,respectively. Looking at non-white jobseekers, we see null effects of Address Omission, as ifnon-whites expected any gains from applying without an address to be undone later whentheir race becomes visible. Since 77% of jobseekers in the Address Omission Experimentare not white, the negative (not statistically significant) effects of Address Omission in thatsubsample cancel out the positive effects on white jobseekers, yielding the average null.1818In the Information Experiment, as we do not vary expected stigma visibility, we do not have the samepredictions for the race heterogeneity. The effects of information could depend, for instance, on how non-whites update their beliefs about racial discrimination in response to the callback information. We displaythe pre-registered heterogeneity cuts for the Information Experiment, including race, in Figure C.7.88diff p-val=0.090.03diff p-val=0.200.12diff p-val=0.140.04Double-lasso ControlsNo ControlsAgg.*WhiteAgg.*Non-whiteSelf*WhiteSelf*Non-whiteInterv.*WhiteInterv.*Non-white-.5 -.4 -.3 -.2 -.1 0 .1 .2 .3 .4 .5Effect of Name-Only on Interview Performance (SDs)95% CI90% CINote: Graphs show heterogeneous treatment effects by self-identified race (white vs. non-white jobseekers).See notes in Figures 4.6 and 4.4 for details on outcomes and graph elements.Figure 4.7: Race and Address Visibility Operate as Substitutes4.5.2 ObfuscationWe see address obfuscation throughout our experiments, and it correlates positively withexpected discrimination. Among all jobseekers who finished a Status Quo application form(i.e., those who freely declared their addresses), 28.5% obfuscated. This share was 24% amongthose who expected low discrimination and 34% for those who expected high discrimination(p=0.01 for the difference). At the interview, the receptionist also asks for an address whenthe applicant arrives: 17% of those expecting low discrimination obfuscate, and 29% of thoseexpecting high discrimination do the same (p < 0.01 for the difference).19 We see this asevidence of jobseekers indeed expecting discrimination from the HR firm and attempting to19For these correlations, we use a classification based on the latest measure of expected discriminationavailable for each jobseeker \u2013 i.e., for those who went through the Information Experiment, we use expecteddiscrimination regarding the HR firm instead, and split into low and high groups based on the same 50%threshold as before.89avoid it.Obfuscation might have contributed to our findings of null effects of information aboutmarket-level discrimination on application in the Information Experiment. Section 4.4.2presented some suggestive evidence that jobseekers picked obfuscated addresses to maximizethe expected callback rate. To see how that could induce null results on applications, con-sider a jobseeker such that i) if she learns no new information, she applies for the job, andii) learning the actual favela callback rate would discourage her from applying (e.g., becauseshe was too optimistic). Then if she learns that she was too optimistic about the favelacallback rate in Favela Info, she might \u201cpick\u201d a higher callback rate by choosing to declarea non-favela address. If she instead learns both callback rates, her expected callback rateshould decrease for all possible addresses, but she might also think jobs outside the favelaare more attractive because now she also expects lower on-the-job discrimination. So, forthis jobseeker, the option to obfuscate prevents Favela Info from decreasing callback rates,leading to no difference in her behavior. If jobseekers of this \u201ctype\u201d are numerous and couldnot obfuscate, we might have seen Favela Info decreasing application rates and Full Infobringing it back up.4.5.3 Policy ConsiderationsRelevance of the Effects on Interview PerformanceOne key issue for deriving policy implications from our Interview Experiment findings iswhether expected discrimination also affects the interviewer\u2019s ultimate judgment of who torecommend. Above, we have shown evidence that the aggregate interview-assessed perfor-mance is negatively affected by stigma visibility in the subsamples of white jobseekers andthose expecting high discrimination. While those two heterogeneities confirm that expecteddiscrimination can affect the interviewer\u2019s impressions, we have less power to evaluate whetherexpected discrimination impacts the interviewers\u2019 final judgment. That judgment is codedin the overall performance rating, which is one of the three components of the interviewerassessment index.Hearing that the interviewer would only know the jobseeker\u2019s name (Name-Only) has aneffect of 0.06SD (without controls) or 0.03SD (with lasso-selected controls) on the overallperformance rating z-score, and neither is statistically significant. Nevertheless, when esti-mating heterogeneous effects by expected discrimination and race, we see some evidence thatwhite jobseekers and those expecting high discrimination get better overall ratings underName-Only (see Figure 4.8). As before, the gap is wider for the race comparison, wherewe see a positive and statistically significant effect of Name-Only on the overall interviewer90rating. This evidence suggests that expected discrimination also affected the final interviewerrating in our experiment. If that is true, there is reason for policymakers and firms to considerpolicies such as \u201cblinding\u201d in interviews.diff p-val=0.200.17diff p-val=0.090.03Double-lasso ControlsNo ControlsOverall PerformanceOverall*High Exp. DiscOverall*Low Exp. DiscOverall*WhiteOverall.*Non-white-.5 -.4 -.3 -.2 -.1 0 .1 .2 .3 .4 .5 .6 .7 .8Effect of Name-Only on Final Interviewer Rating (SDs)95% CI90% CINote: The graph shows average and heterogeneous treatment effects on the final performance rating (used formaking recommendations) of being told that one\u2019s interviewer would only know their name (as opposed toname and address). Thicker error bars show 90% confidence intervals, and thinner bars show 95% intervals.Figure 4.8: Expected Discrimination May Also Affect Final Interviewer RatingBut our results have implications even if all the effects of expected stigma visibility wererestricted to the jobseekers\u2019 self-assessment. For instance, after a negative interview experi-ence, jobseekers might be reticent to apply again for other jobs that require formal interviews.Also, note that interviewers in our experiment had no way to discriminate against favela res-idents \u2013 because we focused on the effects of expected discrimination, we kept interviewersalways on script, and they did not know anything about the experimental design or ques-tion at the time of the interviews. But, in a regular interview, interviewers may actuallybehave differently towards a favela jobseeker, which can further change how the intervieweereacts and amplify the effects of expected discrimination on performance. Finally, even ifwe disregard performance completely, there is the question of jobseekers\u2019 self-confidence: ex-pected discrimination can undermine jobseeker\u2019s psychological welfare in general (Pascoe andSmart Richman, 2009; Schmitt et al., 2014), and we show that it leads to negative interviewexperiences.Blinding and Other PoliciesOur experiments have implications for policies that restrict the information recruiters mayaccess. First, consider policies that reduce stigma visibility at the callback stage, such asre\u00b4sume\u00b4 anonymization, or forbidding employers from requesting some specific information.Our results suggest we should not expect such policies to change applicant behavior substan-tially or across the board. Our analysis of the interaction between race and address visibilitysuggests that such policies might only encourage applications for groups who can keep on91hiding their stigmas later on, as was the case with white jobseekers in our sample. Sincethere is also evidence that such procedures can backfire when they lead recruiters to makedecisions with incomplete information (e.g., Behaghel et al. 2015; Doleac and Hansen 2020),our results suggest these policies should be treated with even more caution.On the other hand, there is reason to become more optimistic about \u201cblind\u201d auditions (asin Goldin and Rouse 2000) or interviews, since we show evidence that simply expecting ablinding procedure can improve performance. Our study highlights the importance of job-seekers\u2019 second-order beliefs, rather than whatever other damage discriminating interviewersmay impose. Hence, employers should make sure that jobseekers are fully aware of blindingpolicies. Furthermore, even if a policy hides one stigma, it may fail to have an effect becauseanother stigma may act as a substitute \u2013 as we show in Section 4.5.1. Hence, policies thathide all stigmas during interviews (e.g., audio-only, text, or metaverse interview rounds) coulddominate alternatives. AI-intermediated candidate selection is also a promising alternative,as shown in Avery et al. (2023).Understanding exactly what is different about face-to-face interviews that leads to largereffects of expected discrimination could help inform policy, too. At a face-to-face interview,application and show-up costs are sunk, but the immediate stakes are higher, and an inter-viewer explicitly judges the jobseeker. Our experiments cannot measure the importance ofeach of those components, but we have some hints that jobseekers might find it difficult to bestrategic at the office. For instance, if we look at jobseekers who went through a Status Quoapplication process and make it to the interview, we see the same jobseekers are 20% (5.7p.p.) less likely to obfuscate their addresses at the interview office (p < 0.01). Looking at theexperimental results, we see that the index component that is most affected by Name-Only isa self-perceived measure of professional behavior, suggesting that jobseekers can not (or willnot) self-regulate their behaviors as much when they believe their address stigma is visible.If the stress and difficulty in managing behavior are to blame, coaching programs could helpjobseekers to prepare for facing the pressure of an interview.Firms may also play a role in decreasing expected discrimination and creating an environmentwhere they can extract a better signal from interviews. For instance, making the candidate-selection process more transparent and credibly committing to non-discriminatory practices(such as diversity, equity, and inclusion). While firms need to consider the trade-offs involvedin adopting these policies, our evidence on interview performance suggests that such policiesmay help them extract more accurate signals during candidate selection.924.6 ConclusionThis chapter provides evidence that, in a context where favela jobseekers overestimate address-based discrimination, expected discrimination damages interview performance. When we ma-nipulate expected discrimination though expected address visibility at the interview, expectedvisibility leads to a significant decrease in interviewees\u2019 perceptions of their performance anda nonsignificant decrease in the interviewer-assessed performance. Nevertheless, there arestatistically significant decreases in interviewer-assessed performance for those who expecthigh discrimination and for white jobseekers. The effects on these subgroups are consistentwith i) expected discrimination leading to worse performance when a stigma is visible andii) the race and address stigmas acting as substitutes.Hence, expected discrimination can amplify the effects of whatever discrimination exists ininterviews. It can lead to self-fulfilling prophecies, at least in sense that if a jobseeker expectsa worse evaluation because of their address, they get one. As expected discrimination canmake favela residents look worse on average to interviewers, it has the potential to create aself-fulfilling prophecy: as many favela residents expect discrimination and perform worse,recruiters may form opinions about favela jobseekers that do not reflect their full capacities.While we do not see significant effects on average interviewer-assessed performance, futureresearch can test whether it is true with a higher-powered experiment and in other contextswhere expected discrimination may be more important. To close the loop, it would alsobe necessary to verify whether interviewers perceive the discriminated group as worse onexpectation.Regarding the application decision, we show evidence from two experiments indicating thatexpected anti-favela discrimination plays no role in most jobseeker\u2019s decision to apply. Weshow that i) manipulating expected stigma visibility at the moment of the application de-cision and ii) shifting beliefs about expected discrimination rates (by randomly revealing tojobseekers callback rate estimates for favela and non-favela neighborhoods) do not changeapplication rates. White jobseekers may be an exception to that rule since they apply moreoften when told that their addresses are unnecessary at the application stage \u2013 an effect ofstigma visibility that is again consistent with the visibility of race and address operating assubstitutes. The non-responsiveness of non-whites to their address visibility may be why wesee null effects on the experiment manipulating address visibility at the application stage.The possibility of making decisions in private and in one\u2019s own time when crafting an appli-cation (but not at the interview) may be another reason why we see effects at the interviewbut not at the application stage. Address obfuscation may have also contributed to the nulleffects in the Information Experiment. At the moment of the interview, expected discrimi-nation might be more important for several reasons like stress, difference in stakes, or even93stereotype threat.Given the importance of the topic for firms and policymakers, we see an avenue for futureresearch aiming to understand precisely why expected discrimination is (more) relevant atthe interview stage. Moreover, since many institutions have become committed to diversity,equity, and inclusion (DEI) in recent years (Pew Research, 2021; Fath, 2023), an immedi-ate question is whether making such public commitments can indeed decrease jobseekers\u2019expected discrimination regarding those firms. These DEI commitments can be costly forfirms (e.g., a firm might need to hire staff to develop and implement such policies), whiletheir upsides are uncertain. If DEI commitments remove a handicap faced by jobseekers whoanticipate discrimination and help recruiters in talent identification, they could become moreattractive to a broader range of firms.94Chapter 5ConclusionThis thesis is composed of three chapters that tackle significant questions related to economichistory and development economics. Chapter 2 investigates the impact of private colonizationexposure on government size and public goods provision in Brazil. Exploiting the DonataryCaptaincy system, where Colonial Brazil was divided and allocated to private citizens, andthe fact that each captaincy was eventually returned to the Portuguese Crown, I create ameasure for years of private colonization. Our findings suggest that a longer exposure toprivate colonization led to fewer public employees, lower government expenditure, and fewerpublic goods by 1920. However, by 2010, there was evidence of convergence in governmentsize and educational outcomes, although disparities persisted in public health. The resultsare robust to various tests, such as a case study comparing captaincies with only 1 and 2years of private colonization to their neighbours that had approximately 180 years of privatecolonization, and adjustments for spatial correlation. Finally, results using placebo DonataryCaptaincies yielded null results, suggesting that the results are not driven by unobservablecharacteristics correlated with latitude.Chapter 3 contributes to the discussion on slavery\u2019s lasting effects by investigating how theshare of female slaves in 1872 impacted violence against black women in the 2010s. I addresspotential endogeneity concerns by exploiting the Brazilian Empire\u2019s drafting of male slavesduring the Paraguayan War as an instrument for the share of female slaves. The closer amunicipality was to the war front, the more male slaves were drafted, resulting in a largershare of female slaves. Using data from 2015 to 2017 on gender violence, I find that a highershare of female slaves in 1872 led to a significant increase in violence against black womentoday. More specifically, a 1 percentage point increase in the share of female slavery led toa 21.2% increase in cases of physical violence and a 65.2% increase in psychological violenceper 1,000 black inhabitants. Notably, this impact is absent when analyzing violence against95white women.Finally, in Chapter 4, we conduct three field experiments to analyze how jobseekers respondto expected discrimination in labour market interactions. We partner with a large cosmeticsfirm in Rio de Janeiro and invite favela residents to apply for their positions. Jobseekers\u2019application rates are largely unaffected by the randomly assigned requirement to disclosetheir addresses during the application stage. Similarly, we do not see an effect on applicationrates when we inform them about the lack of discrimination in callback rates in a previouslyconducted audit study. 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Discrimination againstworkers from slums: What is its extent, what explains it, and how do we tackle it?107Appendix AAppendix to Chapter 2A.1 Supplementary TablesVariable N Mean SD N Mean SDLow Exposure High ExposureYears of Private Colonization 1,273 68.08 80.55 1,347 192.12 19.341920 OutcomesGDP per capita (in 2010 R$) 1,128 702.90 444.62 1,235 537.08 308.60Land Gini Index 1,268 0.64 0.12 1,332 0.57 0.14Public Municipal Administrators (per 1,000 people) 1,273 0.44 0.47 1,347 0.36 0.37Education workers (per 1,000 people) 1,273 1.29 1.25 1,347 0.84 0.64Schools (per 1,000 people) 1,273 0.12 0.13 1,347 0.10 0.12Medical Doctors (per 1,000 people) 1,273 0.80 0.79 1,347 0.60 0.61Literacy Rate 1,273 0.19 0.08 1,347 0.17 0.07Public Expenditure per capita 1,123 4.85 8.58 1,220 2.39 3.14Public Expenditure in Education per capita 1,015 0.18 0.38 1,058 0.14 0.22Public Expenditure in Health per capita 1,015 0.24 0.50 1,058 0.10 0.232010 OutcomesGDP per capita (in 2010 R$) 1,273 13,053.91 19,477.73 1,347 9,752.85 12,062.06Gini Index 1,273 0.49 0.06 1,347 0.50 0.06Public Employees (per 1,000 people) 1,269 48.60 20.72 1,344 50.80 19.98Public Schools teachers (per 1,000 people) 1,273 12.35 3.59 1,347 12.67 3.38Public Schools (per 1,000 people) 1,273 0.12 0.13 1,347 0.10 0.12SUS Doctors (per 1,000 people) 1,273 1.70 1.07 1,347 1.38 0.84Non-SUS Doctors (per 1,000 people) 1,273 0.16 0.34 1,347 0.08 0.23Public Expenditure per capita 1,264 1,046.57 498.30 1,330 991.05 413.19Public Expenditure in Education per capita 1,264 417.59 223.64 1,330 390.89 193.13Public Expenditure in Health per capita 1,264 548.87 242.71 1,330 502.61 182.37Geographical CharacteristicsLatitude 1,273 -15.89 6.83 1,347 -15.28 4.56Longitude 1,273 -42.61 4.14 1,347 -41.96 3.62Altitude 1,273 477.52 305.79 1,347 498.05 286.78Distance to Coast (in kms) 1,273 189.81 185.94 1,347 282.29 223.08Distance to River (in kms) 1,273 33.65 31.42 1,347 44.51 38.68Coffee Suitability 1,273 28.57 15.43 1,347 28.98 11.66Sugar Suitability 1,273 26.58 14.97 1,347 22.91 10.22Corn Suitability 1,273 30.30 13.05 1,347 27.93 10.95Rice Suitability 1,273 40.12 15.59 1,347 39.38 10.83Soy Suitability 1,273 27.76 12.44 1,347 25.95 9.32Notes: Each observation is a 2010 municipality in Brazil. A municipality is classified as low exposure if they were exposedless than 179 years (the median) to private colonization. Otherwise, they are classified as high exposure. GDP per capitafor 1920 is measured in 2010 reais. Public expenditure data in 1926 is measured in contos de reis. GDP per capita, andpublic expenditure data in 2010 are measured in 2010 reais.Table A.1: Summary Statistics108ln(Sunlight) ln(Rainfall) Slope ln(Dist. River)(1) (2) (3) (4)Panel A: Whole SampleYears of Private Colonization (in 100 years) -0.00622*** -0.0282*** 0.182* -0.0419(0.00170) (0.0107) (0.105) (0.113)Observations 2,619 2,619 2,619 2,619R-squared 0.852 0.636 0.679 0.183State FE Yes Yes Yes YesGeographical Controls Yes Yes Yes Yes1920 Cluster Yes Yes Yes YesMean Dep. Var. 1.636 7.022 6.275 2.788Panel B: Up to 50km of the borderYears of Private Colonization (in 100 years) -0.00680*** -0.0403*** 0.0500 -0.0130(0.00202) (0.0117) (0.117) (0.109)Observations 1,495 1,495 1,495 1,495R-squared 0.865 0.680 0.669 0.256State FE Yes Yes Yes YesGeographical Controls Yes Yes Yes Yes1920 Cluster Yes Yes Yes YesMean Dep. Var. 1.645 6.994 5.774 2.757Notes: Years of Private Colonization is defined as the difference between the year the captaincy was trans-ferred to the Crown and the year of the first settlements. Geographical controls are distance to the closestcaptaincy border, longitude, latitude, altitude, distance to the coast, sunlight intensity, and annual rainfall,except for the case where one of the controls is used as an outcome. Robust standard errors in parentheses. If*** p<0.01, ** p<0.05, * p<0.1.Table A.2: Geographical Variables109Dependent Variable: Land SuitabilityCoffee Sugar Corn Rice SoyPanel A: Whole SampleYears of Private Colonization (in 100 years) -0.513 -1.972*** 0.291 0.550 0.264(0.653) (0.682) (0.517) (0.655) (0.462)Observations 2,619 2,619 2,619 2,619 2,619R-squared 0.331 0.338 0.487 0.236 0.504State FE Yes Yes Yes Yes YesGeographical Controls Yes Yes Yes Yes Yes1920 Cluster Yes Yes Yes Yes YesMean Dep. Var. 28.78 24.70 29.09 39.75 26.84Panel B: Up to 50km of the borderYears of Private Colonization (in 100 years) -0.202 -0.947 0.391 0.743 0.417(0.717) (0.696) (0.575) (0.702) (0.517)Observations 1,495 1,495 1,495 1,495 1,495R-squared 0.327 0.337 0.523 0.203 0.554State FE Yes Yes Yes Yes YesGeographical Controls Yes Yes Yes Yes Yes1920 Cluster Yes Yes Yes Yes YesMean Dep. Var. 28.73 24.80 30.64 40.97 28.38Notes: Years of Private Colonization is defined as the difference between the year the captaincy wastransferred to the Crown and the year of the first settlements. Geographical controls are distance tothe closest captaincy border, longitude, latitude, altitude, distance to the coast, sunlight intensity,and annual rainfall, except for the case where one of the controls is used as an outcome. Robust stan-dard errors in parentheses. If *** p<0.01, ** p<0.05, * p<0.1.Table A.3: Balance Test: Suitability110(1) (2) (3) (4) (5) (6)Panel A: Whole SampleLn(Population in 1920) Ln(Population in 2010)Years of Private 0.0858* 0.0748* 0.0540 -0.0954*** 0.0731*** 0.129***Colonization (in 100 years) (0.0472) (0.0400) (0.0398) (0.0268) (0.0277) (0.0288)Observations 2,620 2,619 2,619 2,620 2,619 2,619R-squared 0.008 0.179 0.332 0.005 0.114 0.248Geographical Controls No Yes Yes No Yes YesState FE No No Yes No No YesPanel B: Up to 50km of the borderLn(Population in 1920) Ln(Population in 2010)Years of Private 0.0550 0.0651 0.0136 -0.0469 0.140*** 0.133***Colonization (in 100 years) (0.0585) (0.0528) (0.0518) (0.0366) (0.0380) (0.0388)Observations 1,496 1,495 1,495 1,496 1,495 1,495R-squared 0.003 0.178 0.335 0.001 0.130 0.277Geographical Controls No Yes Yes No Yes YesState FE No No Yes No No YesNotes: Years of Private Colonization is defined as the difference between the year the captaincy was trans-ferred to the Crown and the year of the first settlements. Geographical controls are distance to the closestcaptaincy border, longitude, latitude, altitude, distance to the coast, sunlight intensity, and annual rainfall.Robust standard errors in parentheses. If *** p<0.01, ** p<0.05, * p<0.1.Table A.4: Population 1920 and 2010111Dependent Variable: Non-SUS Doctors per 1,000 inhabitants in 2010(1) (2) (3) (4)Panel A: Whole SampleYears of Private Colonization (in 100 years) -0.0560*** -0.0281*** -0.00680 -0.0111(0.00739) (0.00747) (0.00723) (0.00768)Observations 2,620 2,620 2,619 2,619R-squared 0.027 0.166 0.153 0.184State FE No Yes No YesGeographical Controls No No Yes YesMean Dep. Var. 0.122 0.122 0.121 0.121Panel B: Up to 50km of the borderYears of Private Colonization (in 100 years) -0.0550*** -0.0281*** -0.00797 -0.0151(0.0107) (0.0106) (0.00999) (0.0115)Observations 1,496 1,496 1,495 1,495R-squared 0.025 0.180 0.166 0.199State FE No Yes No YesGeographical Controls No No Yes YesMean Dep. Var. 0.120 0.120 0.120 0.120Notes: Years of Private Colonization is defined as the difference between the year the captaincy was trans-ferred to the Crown and the year of the first settlements. Geographical controls are distance to th closestcaptaincy border, longitude, latitude, altitude, distance to the coast, sunlight intensity, and annual rainfall.Robust standard errors in parentheses. If *** p<0.01, ** p<0.05, * p<0.1.Table A.5: Non-SUS Medical Doctors in 2010112(1) (2) (3) (4)Dependent Variable:Municipal PublicEmployees per 1,000ln(Public Expenditureper capita)Education Workersper 1,000 inhabitansMedical Doctorsper 1,000 inhabitantsPanel A: Whole SampleYears of Private -0.0590 -0.0869 -0.160 -0.142Colonization (in 100 years)25 km (0.0165)*** (0.0376)** (0.0377)*** (0.0257)***50 km (0.0229)*** (0.0569) (0.0467)*** (0.0334)***75 km (0.0248)** (0.0689) (0.0465)*** (0.0363)***100 km (0.0267)** (0.0764) (0.0429)*** (0.0380)***150 km (0.0280)** (0.0822) (0.0377)*** (0.0387)***200 km (0.0272)** (0.0797) (0.0306)*** (0.0361)***Observations 2,619 2,342 2,619 2,619R-squared 0.279 0.523 0.405 0.461Mean Dep. Var. 0.398 0.636 1.060 0.700Panel B: Up to 50km of the borderYears of Private -0.0499 -0.128 -0.153 -0.148Colonization (in 100 years)25 km (0.0209)** (0.0458)*** (0.0566)*** (0.0343)***50 km (0.0245)** (0.0622)** (0.0675)** (0.0423)***75 km (0.0232)** (0.0688)* (0.0665)** (0.0434)***100 km (0.0249)** (0.0700)* (0.0578)*** (0.0424)***150 km (0.0239)** (0.0709)* (0.0586)*** (0.0442)***200 km (0.0240)** (0.0652)** (0.0453)*** (0.0426)***Observations 1,495 1,327 1,495 1,495R-squared 0.355 0.535 0.403 0.488Mean Dep. Var. 0.391 0.689 1.077 0.696Notes: All specifications include state fixed effects and control for the distance to the border and a set ofgeographical variables including longitude, latitude, altitude, distance to the coast, sunlight incidence, andrainfall. Clustered standard errors at the 1920 municipality level are reported in parentheses. ***, **, and *indicate significance at the 1, 5, and 10 percent levels.Table A.6: Conley SD - 1920113(1) (2) (3) (4) (5) (6)Dependent Variable:Municipal PublicEmployees per 1,000ln(Current Expenditureper capita)Public School Teachersper 1,000 inhabitansSUS Medical Doctorsper 1,000 inhabitantsHealth Centersper 10,000 inhabitantsChild Mortalityper 10,000 inhabitantsPanel A: Whole SampleYears of Private -0.316 -0.0189 0.0976 -0.113 -0.256 0.0672Colonization (in 100 years)25 km (0.634) (0.0108)* (0.102) (0.0266)*** (0.108)** (0.0523)50 km (0.743) (0.0131) (0.123) (0.0351)*** (0.151)* (0.0577)75 km (0.819) (0.0144) (0.136) (0.0412)*** (0.179) (0.0577)100 km (0.882) (0.0156) (0.150) (0.0449)** (0.201) (0.0553)150 km (0.869) (0.0159) (0.154) (0.0428)*** (0.210) (0.0478)200 km (0.873) (0.0162) (0.160) (0.0427)*** (0.220) (0.0536)Observations 2,612 2,590 2,619 2,619 2,609 2,618R-squared 0.101 0.150 0.243 0.273 0.180 0.074Mean Dep. Var. 49.73 6.856 12.52 1.533 5.253 2.147Panel B: Up to 50km of the borderYears of Private -0.487 -0.0249 0.134 -0.0882 -0.257 0.136Colonization (in 100 years)25 km (0.793) (0.0138)* (0.126) (0.0342)*** (0.133)* (0.0618)**50 km (0.774) (0.0143)* (0.127) (0.0413)** (0.171) (0.0712)*75 km (0.697) (0.0137)* (0.0976) (0.0442)** (0.192) (0.0699)*100 km (0.655) (0.0143)* (0.104) (0.0446)** (0.209) (0.0623)**150 km (0.695) (0.0169) (0.103) (0.0436)** (0.219) (0.0438)***200 km (0.613) (0.0153) (0.106) (0.0426)** (0.223) (0.0451)***Observations 1,490 1,482 1,495 1,495 1,492 1,494R-squared 0.156 0.188 0.302 0.253 0.232 0.053Mean Dep. Var. 49.66 6.845 12.71 1.531 5.363 2.128Notes: All specifications include state fixed effects, and control for the distance to the border and a set ofgeographical variables including longitude, latitude, altitude, distance to the coast, sunlight incidence, andrainfall. Robust standard errors are reported in parentheses. ***, **, and * indicate significance at the 1, 5,and 10 percent levels.Table A.7: Conley SD - 2010114(1) (2) (3) (4)Dependent Variable:Municipal PublicEmployees per 1,000ln(Public Expenditureper capita)Education Workersper 1,000 inhabitansMedical Doctorsper 1,000 inhabitantsPanel A: Whole SamplePrivate Colonization -0.120*** -0.0173 -0.233*** -0.170***(0.0373) (0.0848) (0.0650) (0.0499)Observations 2,619 2,342 2,619 2,619R-squared 0.280 0.520 0.400 0.449Mean Dep. Var. 0.398 0.636 1.059 0.700Panel B: Up to 50km of the borderPrivate Colonization -0.0954** -0.0459 -0.236*** -0.142**(0.0414) (0.0879) (0.0785) (0.0570)Observations 1,495 1,327 1,495 1,495R-squared 0.356 0.529 0.400 0.472Mean Dep. Var. 0.391 0.689 1.076 0.696Notes: All specifications include state fixed effects, and control for the distance to the border and a set ofgeographical variables including longitude, latitude, altitude, distance to the coast, sunlight incidence, andrainfall. Clustered standard errors at the 1920 municipality level are reported in parentheses. ***, **, and *indicate significance at the 1, 5, and 10 percent levels.Table A.8: Non-Linear Measure - 1920115(1) (2) (3) (4) (5) (6)Dependent Variable:Municipal PublicEmployees per 1,000ln(Current Expenditureper capita)Public School Teachersper 1,000 inhabitansSUS Medical Doctorsper 1,000 inhabitantsHealth Centersper 10,000 inhabitantsChild Mortalityper 10,000 inhabitantsPanel A: Whole SamplePrivate Colonization -0.578 -0.00708 -0.156 -0.142*** -0.873*** 0.113(1.077) (0.0184) (0.169) (0.0463) (0.175) (0.1000)Observations 2,612 2,590 2,619 2,619 2,609 2,618R-squared 0.101 0.149 0.243 0.269 0.186 0.074Mean Dep. Var. 49.73 6.855 12.52 1.532 5.254 2.148Panel B: Up to 50km of the borderPrivate Colonization -0.894 -0.0100 -0.126 -0.0744 -0.778*** 0.158(1.327) (0.0233) (0.215) (0.0610) (0.219) (0.119)Observations 1,490 1,482 1,495 1,495 1,492 1,494R-squared 0.156 0.186 0.302 0.250 0.236 0.052Mean Dep. Var. 49.65 6.844 12.71 1.530 5.363 2.128Notes: All specifications include state fixed effects, and control for the distance to the border and a set ofgeographical variables including longitude, latitude, altitude, distance to the coast, sunlight incidence, andrainfall. Robust standard errors are reported in parentheses. ***, **, and * indicate significance at the 1, 5,and 10 percent levels.Table A.9: Non-Linear Measure - 2010116A.2 Supplementary Figures(a) 1920 State Boundaries(b) 2010 State BoundariesNotes: The maps present the Donatary Captaincies\u2019 historical boundaries and Brazil\u2019s state boundaries in(a) 1920 and (b) 2010.Figure A.1: State and Donatary Captaincies Boundaries117Notes: The number next to each Donatary Captaincy represents the number of years under private coloniza-tion.Figure A.2: Years of Private Colonization118Appendix BAppendix to Chapter 3B.1 Supplementary Tables(1) (2) (3) (4)VARIABLESln(distance to Uruguaiana) -5.295*** -3.745*** -4.859*** -4.203***(1.214) (1.020) (0.981) (1.059)Latitude -0.197 0.140 -0.0786 -0.412**(0.161) (0.117) (0.149) (0.172)Longitude 0.290 0.195 0.0920 -0.102(0.184) (0.134) (0.144) (0.161)Total of Slaves (in 10,000 habs) 0.606 -0.00347 1.047(0.716) (0.689) (0.822)Population in 1872 (in 100,000 habs) 1.388 2.682** 0.550(1.542) (1.355) (1.670)Share of Female in 1872 108.6*** 103.2*** 104.1***(13.34) (14.37) (14.49)Share of White in 1872 -0.768 -0.256 0.639(1.976) (2.140) (2.164)Share of Foreign in 1872 7.267 6.169 8.193(4.423) (5.875) (6.011)Share of Married in 1872 11.15*** 8.186* 9.507**(4.078) (4.487) (4.597)Share of Catholic in 1872 19.39*** 16.03* 16.75**(6.654) (8.456) (8.404)GDP (in R$ billions) -0.239(0.159)Population in 2010 (in 1,000,000 habs) 0.799(0.589)Share of Urban pop. in 2010 1.163(1.949)Share of Female in 2010 -1.397(1.764)Share of Black in 2010 -3.099(7.397)Share of Brown in 2010 6.519***(2.096)Share of Indigenous in 2010 -35.45(48.18)Literacy Rate in 2010 -14.27(9.630)Observations 259 259 259 259R-squared 0.134 0.477 0.499 0.533Province FE Yes No Yes YesMean Dep. Var. 46.16 46.16 46.16 46.16F-Stat 19.01 13.47 24.53 15.76Notes: The dependent variable is the share of female slaves, ranging from 0 to 100, in each1872 municipality. The main independent variable is the log distance to Uruguaiana in kms.1872 controls: total number of slaves, population, share of women, share of whites, share offoreign, share of married people, share of catholic. 2010 controls: municipal GDP, population,share of urban population, share of females, share of blacks, share of brown, share of indigenouspeople and literacy rate. Additional controls: latitude and longitude. Robust standard errorsin parentheses. When *** p<0.01, ** p<0.05, * p<0.1.Table B.1: First Stage Results119(1) (2) (3) (4)VARIABLES White Brown Blacks IndigenousShare of Female Slaves (x100) 0.128 -0.0189 0.408** 0.489*(0.0894) (0.0629) (0.169) (0.295)Latitude 0.0167 -0.0265 0.131 0.421*(0.0667) (0.0478) (0.140) (0.240)Longitude 0.0508 -0.0230 0.175 0.405*(0.0539) (0.0442) (0.108) (0.234)Total of Slaves (in 10,000 habs) -0.0942 -0.0498 -0.280 0.414(0.217) (0.280) (0.488) (1.073)Population in 1872 (in 100,000 habs) -0.0220 0.535 -0.120 -0.896(0.420) (0.479) (1.010) (2.210)Share of Female in 1872 -13.96 1.617 -41.39** -42.84(9.431) (7.272) (18.20) (29.79)Share of White in 1872 0.229 -0.171 0.157 3.578*(0.378) (0.612) (1.055) (1.854)Share of Foreign in 1872 -1.509 -0.250 -4.312 1.089(1.459) (1.458) (3.183) (6.984)Share of Married in 1872 -0.709 1.321 -1.986 1.249(1.179) (1.053) (2.652) (4.643)Share of Catholic in 1872 -3.149 -0.829 -9.352** 0.0481(2.106) (1.965) (4.480) (9.296)GDP (in R$ billions) 0.0604 0.0835** 0.131 -0.0132(0.0413) (0.0374) (0.0896) (0.151)Population in 2010 (in 1,000,000 habs) -0.218 -0.309** -0.438 0.168(0.151) (0.141) (0.329) (0.558)Share of Urban pop. in 2010 0.0859 0.431 0.411 -2.062(0.496) (0.380) (1.092) (2.203)Share of Female in 2010 0.794** 0.687* 1.003 2.054(0.360) (0.390) (0.802) (1.513)Share of Black in 2010 -3.135 -1.667 -7.327 -15.36(1.948) (2.352) (4.759) (10.06)Share of Brown in 2010 -1.331 1.062 -4.859*** -2.374(0.822) (0.855) (1.742) (3.485)Share of Indigenous in 2010 10.50 25.96* 31.92** 12.59(6.845) (15.69) (15.29) (51.20)Literacy Rate in 2010 3.485 2.146 0.134 7.326(2.642) (2.572) (5.767) (10.14)Observations 259 259 259 258R-squared 0.091 0.342 -0.283 -0.004Province FE Yes Yes Yes YesMean Dep. Var. 0.853 0.892 1.454 1.375Robust standard errors in parentheses*** p<0.01, ** p<0.05, * p<0.1Notes: The dependent variable is the number of cases of violence against women per 1,000inhabitants of that race. 1872 controls: total number of slaves, population, share of women,share of whites, share of foreign, share of married people, share of catholic. 2010 controls: mu-nicipal GDP, population, share of urban population, share of females, share of blacks, share ofbrown, share of indigenous people and literacy rate. Additional controls: latitude and longi-tude. Robust standard errors in parentheses. When *** p<0.01, ** p<0.05, * p<0.1.Table B.2: Second Stage - All types of Violence120(1) (2) (3) (4)VARIABLES White Brown Blacks IndigenousShare of Female Slaves (x100) 0.0929* -0.00788 0.249*** 0.541*(0.0478) (0.0509) (0.0863) (0.293)Latitude 0.00543 -0.0214 0.0438 0.469**(0.0397) (0.0387) (0.0831) (0.237)Longitude 0.0318 -0.0286 0.0930 0.421*(0.0364) (0.0364) (0.0695) (0.234)Total of Slaves (in 10,000 habs) -0.126 -0.121 -0.339 0.368(0.159) (0.234) (0.348) (1.055)Population in 1872 (in 100,000 habs) 0.0959 0.563 0.343 -0.969(0.299) (0.419) (0.686) (2.155)Share of Female in 1872 -10.21* 0.570 -25.79*** -47.02(5.208) (5.902) (9.787) (29.83)Share of White in 1872 0.0965 -0.253 -0.256 3.086*(0.287) (0.556) (0.661) (1.847)Share of Foreign in 1872 -1.044 -0.112 -2.949 1.637(1.058) (1.161) (2.201) (7.075)Share of Married in 1872 -0.750 0.821 -1.228 1.283(0.820) (0.855) (1.740) (4.701)Share of Catholic in 1872 -2.089 -0.439 -6.295** 0.965(1.378) (1.462) (2.946) (9.587)GDP (in R$ billions) 0.0493* 0.0778** 0.104* -0.00313(0.0282) (0.0313) (0.0579) (0.151)Population in 2010 (in 1,000,000 habs) -0.185* -0.290** -0.368* 0.111(0.105) (0.119) (0.215) (0.562)Share of Urban pop. in 2010 -0.00865 0.392 0.547 -1.149(0.422) (0.337) (0.785) (2.252)Share of Female in 2010 0.770*** 0.715** 1.057* 2.373(0.292) (0.324) (0.554) (1.556)Share of Black in 2010 -2.156 -1.162 -5.563 -16.10*(1.407) (1.919) (3.504) (9.768)Share of Brown in 2010 -1.111* 0.773 -3.381*** -3.608(0.571) (0.720) (1.168) (3.433)Share of Indigenous in 2010 10.09** 26.02* 31.47*** 4.449(4.366) (13.32) (9.484) (46.27)Literacy Rate in 2010 2.359 1.031 -0.137 2.190(1.987) (2.197) (3.819) (10.15)Observations 259 259 259 258R-squared 0.117 0.337 0.021 -0.036Province FE Yes Yes Yes YesMean Dep. Var. 0.666 0.722 1.175 1.188Robust standard errors in parentheses*** p<0.01, ** p<0.05, * p<0.1Notes: The dependent variable is the number of cases of physical violence against women per1,000 inhabitants of that race. 1872 controls: total number of slaves, population, share ofwomen, share of whites, share of foreign, share of married people, share of catholic. 2010 con-trols: municipal GDP, population, share of urban population, share of females, share of blacks,share of brown, share of indigenous people and literacy rate. Additional controls: latitude andlongitude. Robust standard errors in parentheses. When *** p<0.01, ** p<0.05, * p<0.1.Table B.3: Second Stage - Physical Violence121(1) (2) (3) (4)VARIABLES White Brown Blacks IndigenousShare of Female Slaves (x100) 0.160* 0.0636 0.364** 0.391(0.0872) (0.0409) (0.182) (0.308)Latitude 0.0585 0.0218 0.167 0.256(0.0642) (0.0309) (0.136) (0.215)Longitude 0.0702 0.0327 0.167* 0.267**(0.0438) (0.0272) (0.0913) (0.131)Total of Slaves (in 10,000 habs) -0.0973 -0.0797 -0.336 -0.264(0.169) (0.140) (0.359) (0.537)Population in 1872 (in 100,000 habs) -0.164 0.122 -0.0944 -0.280(0.331) (0.241) (0.735) (0.974)Share of Female in 1872 -16.13* -6.401 -36.34* -38.98(9.203) (4.648) (19.19) (31.57)Share of White in 1872 -0.0423 -0.107 -0.268 0.532(0.358) (0.335) (0.796) (0.958)Share of Foreign in 1872 -1.069 -0.436 -3.230 -4.615(1.302) (0.985) (2.641) (3.116)Share of Married in 1872 -1.114 -0.273 -2.677 -3.687(1.076) (0.617) (2.305) (3.430)Share of Catholic in 1872 -2.578 -1.231 -6.902* -8.187(1.987) (1.379) (4.016) (5.387)GDP (in R$ billions) 0.0448 0.0446** 0.0964 0.0761(0.0364) (0.0209) (0.0753) (0.101)Population in 2010 (in 1,000,000 habs) -0.157 -0.162** -0.327 -0.218(0.131) (0.0765) (0.271) (0.357)Share of Urban pop. in 2010 0.000137 0.243 0.146 0.260(0.372) (0.229) (0.758) (0.983)Share of Female in 2010 0.562* 0.474** 1.072 1.445*(0.331) (0.185) (0.682) (0.879)Share of Black in 2010 -1.607 -0.968 -2.245 -5.359(1.491) (1.265) (3.251) (4.557)Share of Brown in 2010 -1.023 0.00383 -2.971** -1.319(0.707) (0.470) (1.452) (2.336)Share of Indigenous in 2010 6.697 10.47** 23.84* 40.45(8.732) (5.258) (14.12) (34.12)Literacy Rate in 2010 2.725 1.063 4.066 10.73(2.225) (1.455) (4.745) (6.656)Observations 259 259 259 258R-squared -0.941 0.085 -1.443 -0.470Province FE Yes Yes Yes YesMean Dep. Var. 0.323 0.330 0.558 0.473Robust standard errors in parentheses*** p<0.01, ** p<0.05, * p<0.1Notes: The dependent variable is the number of cases of psychological violence against womenper 1,000 inhabitants of that race. 1872 controls: total number of slaves, population, share ofwomen, share of whites, share of foreign, share of married people, share of catholic. 2010 con-trols: municipal GDP, population, share of urban population, share of females, share of blacks,share of brown, share of indigenous people and literacy rate. Additional controls: latitude andlongitude. Robust standard errors in parentheses. When *** p<0.01, ** p<0.05, * p<0.1.Table B.4: Second Stage - Psychological Violence122(1) (2) (3) (4)VARIABLES White Brown Blacks IndigenousShare of Female Slaves (x100) 0.00116 0.00714 0.00584 0.0410(0.00854) (0.0133) (0.0180) (0.0706)Latitude -0.00568 -0.000989 -0.0114 -0.0938(0.00585) (0.00911) (0.0174) (0.0791)Longitude 0.00293 0.0120* 0.0104 0.120(0.00496) (0.00670) (0.0129) (0.0728)Total of Slaves (in 10,000 habs) -0.0164 -0.0459 -0.0427 -0.507(0.0263) (0.0317) (0.0508) (0.411)Population in 1872 (in 100,000 habs) 0.0482 0.106* 0.0987 0.773(0.0460) (0.0579) (0.114) (0.705)Share of Female in 1872 -0.0445 -0.864 -0.913 -5.890(0.939) (1.386) (1.916) (8.925)Share of White in 1872 -0.0154 -0.0162 0.0625 -0.490(0.0444) (0.0523) (0.113) (0.545)Share of Foreign in 1872 0.00501 -0.311 -0.507 -1.414(0.139) (0.189) (0.321) (2.004)Share of Married in 1872 -0.0124 -0.199 -0.00777 0.497(0.137) (0.157) (0.277) (1.205)Share of Catholic in 1872 -0.0151 -0.428 -0.797* -2.877(0.223) (0.334) (0.480) (2.990)GDP (in R$ billions) 0.00523 0.00665 -0.00174 -0.0381(0.00331) (0.00451) (0.00753) (0.0346)Population in 2010 (in 1,000,000 habs) -0.0202* -0.0233 0.00409 0.188(0.0117) (0.0158) (0.0287) (0.127)Share of Urban pop. in 2010 0.0739 0.140** 0.286*** -1.532(0.0537) (0.0582) (0.107) (1.876)Share of Female in 2010 0.0196 0.0839* -0.208 0.768(0.0356) (0.0495) (0.250) (0.608)Share of Black in 2010 -0.226 0.109 -0.671 5.101(0.227) (0.324) (0.541) (5.759)Share of Brown in 2010 0.113 0.0399 -0.0253 0.931(0.0863) (0.113) (0.244) (1.280)Share of Indigenous in 2010 1.793** 2.981*** 0.381 -1.947(0.825) (0.896) (2.080) (10.80)Literacy Rate in 2010 0.287 0.558* -0.187 6.032(0.256) (0.324) (0.625) (4.609)Observations 259 259 259 258R-squared 0.212 0.227 0.122 0.057Province FE Yes Yes Yes YesMean Dep. Var. 0.0894 0.105 0.166 0.232Robust standard errors in parentheses*** p<0.01, ** p<0.05, * p<0.1Notes: The dependent variable is the number of cases of sexual violence against women per 1,000inhabitants of that race. 1872 controls: total number of slaves, population, share of women, shareof whites, share of foreign, share of married people, share of catholic. 2010 controls: municipalGDP, population, share of urban population, share of females, share of blacks, share of brown,share of indigenous people and literacy rate. Additional controls: latitude and longitude. Ro-bust standard errors in parentheses. When *** p<0.01, ** p<0.05, * p<0.1.Table B.5: Second Stage - Sexual Violence123(1) (2) (3) (4)VARIABLES White Brown Blacks IndigenousShare of Female Slaves (x100) -7.72e-05 0.00157 -0.00272 0.00449(0.00210) (0.00567) (0.00650) (0.0165)Latitude -0.00138 -0.000614 -0.00534 0.0172(0.00185) (0.00453) (0.00664) (0.0152)Longitude -0.000846 0.000231 0.000652 0.0343**(0.00203) (0.00337) (0.00460) (0.0150)Total of Slaves (in 10,000 habs) 0.00635 0.00922 0.0251 -0.0327(0.0137) (0.0145) (0.0271) (0.126)Population in 1872 (in 100,000 habs) 0.00406 -0.00868 -0.0208 0.0852(0.0197) (0.0226) (0.0439) (0.264)Share of Female in 1872 0.0170 -0.121 0.405 0.809(0.231) (0.624) (0.724) (1.794)Share of White in 1872 -0.0181 -0.0665 -0.0683 -0.0199(0.0153) (0.0599) (0.0470) (0.180)Share of Foreign in 1872 -0.0178 -0.0517 -0.0528 0.615(0.0539) (0.113) (0.129) (0.510)Share of Married in 1872 0.00178 0.00798 0.109 0.0393(0.0457) (0.0860) (0.128) (0.336)Share of Catholic in 1872 -0.0845 -0.153 -0.132 0.626(0.0811) (0.140) (0.172) (0.721)GDP (in R$ billions) 0.00187 0.00474* 0.00352 -0.00764(0.00137) (0.00244) (0.00334) (0.0105)Population in 2010 (in 1,000,000 habs) -0.00792 -0.0179** -0.0150 0.0288(0.00514) (0.00901) (0.0126) (0.0409)Share of Urban pop. in 2010 0.0146 0.0910*** 0.130*** 0.0351(0.0224) (0.0327) (0.0478) (0.110)Share of Female in 2010 0.0366** 0.0535** -0.0395 0.226(0.0175) (0.0227) (0.0945) (0.142)Share of Black in 2010 -0.268*** -0.365** -0.698*** -1.059(0.0942) (0.174) (0.249) (0.782)Share of Brown in 2010 0.0171 0.0725 -0.00555 0.148(0.0357) (0.0658) (0.0982) (0.217)Share of Indigenous in 2010 0.778 5.384 5.623 3.778*(0.483) (3.929) (4.387) (2.208)Literacy Rate in 2010 0.00792 -0.0554 -0.335 0.254(0.116) (0.176) (0.330) (0.792)Observations 259 259 259 258R-squared 0.215 0.286 0.211 0.076Province FE Yes Yes Yes YesMean Dep. Var. 0.0289 0.0338 0.0492 0.0473Robust standard errors in parentheses*** p<0.01, ** p<0.05, * p<0.1Notes: The dependent variable is the number of cases of violence with signs of torture againstwomen per 1,000 inhabitants of that race. All regressions are controlled for: 1872 controls (totalnumber of slaves, population, share of women, share of whites, share of foreign, share of marriedpeople, share of catholic), 2010 characteristics (municipal GDP, population, share of urban pop-ulation, share of females, share of blacks, share of brown, share of indigenous people and literacyrate), latitude and longitude and province FE. Robust standard errors in parentheses. When ***p<0.01, ** p<0.05, * p<0.1.Table B.6: Second Stage - Violence with signs of Torture124(1) (2) (3) (4)White Brown Blacks IndigenousPanel A: Total cases of Violence (per 1,000)Share of Female Slaves (x100) 0.128 -0.0189 0.408 0.489Robust SE (0.0894) (0.0629) (0.169)** (0.295)*Spatial SE: cutoff = 100 km (0.0837) (0.0763) (0.176)** (0.325)Spatial SE: cutoff = 200 km (0.0399)*** (0.0546) (0.0970)*** (0.125)***Spatial SE: cutoff = 250 km (0.0463)*** (0.0322) (0.116)*** (0.131)***Observations 259 259 259 258Mean Dep. Var. 0.853 0.892 1.454 1.375Panel B: Physical Violence (per 1,000)Share of Female Slaves (x100) 0.0929 -0.00788 0.249 0.541*Robust SE (0.0478)* (0.0509) (0.0863)*** (0.293)*Spatial SE: cutoff = 100 km (0.0420)** (0.0624) (0.0904)*** (0.331)Spatial SE: cutoff = 200 km (0.0342)*** (0.0449) (0.0793)*** (0.123)***Spatial SE: cutoff = 250 km (0.0352)*** (0.0336) (0.0747)*** (0.134)***Observations 259 259 259 258Mean Dep. Var. 0.666 0.722 1.175 1.188Panel C: Psychological Violence (per 1,000)Share of Female Slaves (x100) 0.160 0.0636 0.364 0.391Robust SE (0.0872)* (0.0409) (0.182)** (0.308)Spatial SE: cutoff = 100 km (0.0815)* (0.0381)* (0.187)* (0.348)Spatial SE: cutoff = 200 km (0.0266)*** (0.0311)** (0.0556)*** (0.114)***Spatial SE: cutoff = 250 km (0.0479)*** (0.0192)*** (0.111)*** (0.121)***Observations 259 259 259 258Mean Dep. Var. 0.323 0.330 0.558 0.473Panel D: Sexual Violence (per 1,000)Share of Female Slaves (x100) 0.00116 0.00714 0.00584 0.0410Robust SE (0.00854) (0.0133) (0.0180) (0.0706)Spatial SE: cutoff = 100 km (0.00641) (0.0106) (0.0167) (0.0786)Spatial SE: cutoff = 200 km (0.00223) (0.00709) (0.00121)*** (0.0645)Spatial SE: cutoff = 250 km (0.00223) (0.00709) (0.00121)*** (0.0645)Observations 259 259 259 258Mean Dep. Var. 0.0894 0.105 0.166 0.232Panel E: Violence with signs of Torture (per 1,000)Share of Female Slaves (x100) -0.000077 0.00157 -0.00272 0.00449Robust SE (0.00210) (0.00567) (0.00650) (0.0165)Spatial SE: cutoff = 100 km (0.00229) (0.00605) (0.00634) (0.0115)Spatial SE: cutoff = 200 km (0.00163) (0.00545) (0.00251) (0.00882)Spatial SE: cutoff = 250 km (0.00138) (0.00480) (0.00396) (0.00949)Observations 259 259 259 258Mean Dep. Var. 0.0289 0.0338 0.0492 0.0473Notes: The dependent variable is the number of cases of violence against women per 1,000 in-habitants of that race. All regressions are controlled for 1872 characteristics (total number ofslaves, population, share of women, share of whites, share of foreign, share of married people,share of catholic), 2010 characteristics (municipal GDP, population, share of urban population,share of females, share of blacks, share of brown, share of indigenous people and literacy rate),latitude, longitude and province FE. Robust standard errors in parentheses. When *** p<0.01,** p<0.05, * p<0.1.Table B.7: IV Results - Spatial Standard Errors125(1) (2) (3) (4)White Brown Blacks IndigenousPanel A: Total cases of Violence (per 1,000)Share of Female Slaves (x100) 0.0802 0.0117 0.180*** 0.124(0.0516) (0.0386) (0.0654) (0.108)Observations 259 259 259 258Mean Dep. Var. 0.713 0.723 1.016 0.673Panel B: Physical Violence (per 1,000)Share of Female Slaves (x100) 0.0733** 0.0129 0.153*** 0.171(0.0358) (0.0360) (0.0516) (0.109)Observations 259 259 259 258Mean Dep. Var. 0.584 0.609 0.875 0.569Panel C: Psychological Violence (per 1,000)Share of Female Slaves (x100) 0.112** 0.0607* 0.185** 0.141(0.0562) (0.0314) (0.0765) (0.116)Observations 259 259 259 258Mean Dep. Var. 0.299 0.305 0.469 0.298Panel D: Sexual Violence (per 1,000)Share of Female Slaves (x100) -0.00007 0.00164 -0.00274 0.00290(0.00209) (0.00561) (0.00644) (0.0134)Observations 259 259 259 258Mean Dep. Var. 0.0889 0.104 0.163 0.122Panel E: Violence with signs of Torture (per 1,000)Share of Female Slaves (x100) 0.000841 0.000042 -0.00834 0.0112(0.00170) (0.00538) (0.00674) (0.0127)Observations 257 257 257 256Mean Dep. Var. 0.0288 0.0336 0.0488 0.0389Notes: The dependent variable is the inverse hyperbolic sine transformation of thenumber of cases of violence against women per 1,000 inhabitants of that race. All re-gressions are controlled for 1872 characteristics (total number of slaves, population,share of women, share of whites, share of foreign, share of married people, share ofcatholic), 2010 characteristics (municipal GDP, population, share of urban popula-tion, share of females, share of blacks, share of brown, share of indigenous people andliteracy rate), latitude, longitude and province FE. Robust standard errors in paren-theses. When *** p<0.01, ** p<0.05, * p<0.1.Table B.8: IV Results using IHS Transformation on Cases of Violence126B.2 Supplementary FiguresNotes: The text on the cartoon says: \u201cDear, we need people. If the singles are running away to the woods,the only solution is to come to the bed of the married\u201d.Figure B.1: Cartoon published in the Brazilian newspaper Cabria\u02dco in December 12thof 1866.127Notes: The text on the cartoon says: \u201cComission to find volunteers for the war\u201d.Figure B.2: Cartoon published in the Brazilian newspaper Cabria\u02dco in September 22thof 1867.128Figure B.3: Cartoon published in the Paraguayan newspaper Cabichu\u00b4\u0131 in October 7thof 1867, portraying, in a racist manner, the Triple Alliance soldiers as monkeys.129Figure B.4: Another racist characterization of the Triple alliance army published inthe Paraguayan newspaper Cabichu\u00b4\u0131 in August 5th of 1867.130The highlighted areas are Paraguay (in red), Brazil (in white) and Argentina (in blue). The black area inthe southern part of Brazil is Uruguaiana.Figure B.5: Map of South America and the Location of Uruguaiana131Notes: The highlighted areas are Paraguay (in red), Brazil (in green) and Argentina (in blue). The hatchedarea in the northern part of Argentina indicates Corrientes.Figure B.6: Map of South America and the Location of Corrientes132Appendix CAppendix to Chapter 4C.1 Supporting Tables And FiguresC.1.1 Baseline SurveyMean SD Min Max NMare\u00b4 resident (0\/1) 0.62 0.48 0 1 2,167Jacarezinho resident (0\/1) 0.19 0.39 0 1 2,167Manguinhos resident (0\/1) 0.19 0.39 0 1 2,167Age 25.73 6.24 17 41 2,167Male (0\/1) 0.30 0.46 0 1 2,167White jobseeker (0\/1) 0.22 0.42 0 1 2,167Some college (0\/1) 0.08 0.27 0 1 2,167Completed regular high-school (0\/1) 0.80 0.40 0 1 2,167Working now (0\/1) 0.32 0.47 0 1 2,167Holds a formal job (0\/1) 0.13 0.34 0 1 2,167Ever worked (0\/1) 0.75 0.43 0 1 2,167Actively search last week (0\/1) 0.49 0.50 0 1 2,167Microsoft Office Experience (0\/1) 0.80 0.40 0 1 1,984Surveyor-assessed comm skills (Likert scale, 0-5) 2.79 1.10 0 4 2,167Math test score 6.96 2.50 0 17 2,167Heard of people refused job\/fired due to address (0\/1) 0.32 0.47 0 1 2,167Believes has been refused job\/fired due to address (0\/1) 0.28 0.45 0 1 2,167Own-favela expected Audit Study callback rate (%) 30.30 20.23 0 100 2,167Adjacent non-favela expected Audit Study callback rate (%) 63.24 24.54 0 100 2,167Racism (is reason, 0\/1) 0.68 0.47 0 1 1,497Having a different culture\/speech (is reason, 0\/1) 0.66 0.47 0 1 1,497Dislike of favela residents (is reason, 0\/1) 0.65 0.48 0 1 1,497Distance to work (is reason, 0\/1) 0.45 0.50 0 1 1,497Missing days because of police raids (is reason, 0\/1) 0.75 0.44 0 1 1,497Lower skill (is reason, 0\/1) 0.50 0.50 0 1 1,497Difficulty adapting to work (is reason, 0\/1) 0.47 0.50 0 1 1,497Fear or violence (is reason, 0\/1) 0.60 0.49 0 1 1,497Note: This table presents descriptive statistics for the door-to-door baseline survey. Differences in samplesizes occur because we dropped them after introducing the Information Experiment.Table C.1: Baseline Statistics133Location Population Literate Share White Population Share Income per Capita in R$ (2010)All non-favela neighborhoods in Rio 4,888,663 0.92 0.57 1376.35All favela neighborhoods in Rio 1,391,953 0.84 0.33 382.87Jacarezinho (favela) 37,792 0.87 0.33 349.63Manguinhos (favela) 36,151 0.83 0.34 346.86Mare\u00b4 (favela) 129,715 0.83 0.38 395.38Bonsucesso (non-favela) 18,341 0.93 0.60 897.97Maria da Grac\u00b8a (non-favela) 7,967 0.93 0.67 1126.26Note: This table presents summary statistics from the 2010 Census.Table C.2: Census (2010) Summary Statistics134(1) (2) (3) (4) (5) (6) (7) (8) (9)Expects > 25%disc in auditWhitejobseeker (0\/1)Male (0\/1)SkillIndexMare\u00b4resident (0\/1)Completehigh schoolWorkingnow (0\/1)Ever worked(0\/1)AgeAddress Omission 0.020 0.015 0.081\u2217\u2217\u2217 0.092 -0.017 0.027 -0.005 0.053\u2217 0.533(0.025) (0.029) (0.031) (0.059) (0.028) (0.029) (0.032) (0.031) (0.425)Known Address 0.016 -0.026 -0.004 -0.025 -0.009 0.024 -0.011 0.039 0.693(0.025) (0.028) (0.030) (0.058) (0.028) (0.029) (0.032) (0.031) (0.426)Observations 1302 1302 1302 1302 1302 1302 1302 1302 1302Status Quo Mean 0.83 0.23 0.27 -0.07 0.80 0.76 0.33 0.69 25.19Favela=Full p 0.89 0.15 0.01 0.05 0.76 0.91 0.83 0.63 0.71* p\u00a10.1, ** p\u00a10.05, *** p\u00a10.01.Table C.3: Address Omission Experiment: Randomization Balance135(1) (2) (3) (4) (5) (6) (7) (8) (9)Expects > 25%disc in auditWhitejobseeker (0\/1)Male (0\/1)SkillIndexMare\u00b4resident (0\/1)Completehigh schoolWorkingnow (0\/1)Ever worked(0\/1)AgeFavela Info 0.025 0.003 0.021 -0.020 0.036 -0.001 0.017 0.057 1.041\u2217(0.047) (0.038) (0.043) (0.078) (0.044) (0.034) (0.043) (0.038) (0.586)Full Info -0.030 0.017 0.026 -0.166\u2217\u2217 0.037 -0.072\u2217 -0.027 -0.011 -0.306(0.047) (0.039) (0.044) (0.082) (0.045) (0.037) (0.043) (0.041) (0.572)Observations 690 690 690 690 690 690 690 690 690No Info Mean 0.44 0.20 0.29 0.09 0.33 0.85 0.29 0.77 25.58Favela=Full p 0.23 0.72 0.91 0.07 0.98 0.05 0.29 0.07 0.02* p\u00a10.1, ** p\u00a10.05, *** p\u00a10.01.Table C.4: Information Experiment: Randomization Balance136(1) (2) (3) (4) (5) (6) (7) (8) (9)Expects > 25% disc in audit White jobseeker (0\/1) Male (0\/1) Skill Index Mare\u00b4 resident (0\/1) Complete high school Working now (0\/1) Ever worked (0\/1) AgeName-Only 0.020 -0.001 0.006 0.051 -0.095\u2217\u2217 0.019 0.060\u2217 0.056 -0.090(0.048) (0.042) (0.043) (0.085) (0.047) (0.041) (0.033) (0.043) (0.564)Observations 422 422 422 422 422 422 422 422 422Control Mean 0.59 0.24 0.26 -0.01 0.66 0.77 0.10 0.71 24.71* p\u00a10.1, ** p\u00a10.05, *** p\u00a10.01.Table C.5: Interview Experiment : Randomization Balance137(1) (2) (3) (1)-(2) (1)-(3) (2)-(3)Address Omission Experiment Information Experiment Interview Experiment Pairwise t-testVariable N Mean\/(SE) N Mean\/(SE) N Mean\/(SE) N Mean difference N Mean difference N Mean differenceMare\u00b4 resident (0\/1) 1302 0.790 690 0.354 422 0.614 1992 0.436*** 1724 0.176*** 1112 -0.260***(0.011) (0.018) (0.024)Jacarezinho resident (0\/1) 1302 0.184 690 0.193 422 0.204 1992 -0.009 1724 -0.020 1112 -0.011(0.011) (0.015) (0.020)Manguinhos resident (0\/1) 1302 0.027 690 0.454 422 0.182 1992 -0.427*** 1724 -0.156*** 1112 0.271***(0.004) (0.019) (0.019)Age 1302 25.610 690 25.851 422 24.661 1992 -0.241 1724 0.949*** 1112 1.190***(0.174) (0.236) (0.282)Male (0\/1) 1302 0.295 690 0.303 422 0.265 1992 -0.008 1724 0.030 1112 0.037(0.013) (0.018) (0.022)White jobseeker (0\/1) 1302 0.228 690 0.210 422 0.237 1992 0.018 1724 -0.009 1112 -0.027(0.012) (0.016) (0.021)Some college (0\/1) 1302 0.064 690 0.080 422 0.071 1992 -0.016 1724 -0.007 1112 0.009(0.007) (0.010) (0.013)Completed regular high-school (0\/1) 1302 0.776 690 0.823 422 0.777 1992 -0.047** 1724 -0.002 1112 0.046*(0.012) (0.015) (0.020)Working now (0\/1) 1302 0.326 690 0.284 422 0.135 1992 0.042* 1724 0.191*** 1112 0.149***(0.013) (0.017) (0.017)Holds a formal job (0\/1) 1302 0.118 690 0.135 422 0.047 1992 -0.017 1724 0.071*** 1112 0.087***(0.009) (0.013) (0.010)Ever worked (0\/1) 1302 0.722 690 0.786 422 0.737 1992 -0.064*** 1724 -0.015 1112 0.049*(0.012) (0.016) (0.021)Actively search last week (0\/1) 1302 0.531 690 0.425 422 0.649 1992 0.106*** 1724 -0.119*** 1112 -0.225***(0.014) (0.019) (0.023)Surveyor-assessed comm skills (Likert scale, 0-5) 1302 2.795 690 2.797 422 3.001 1992 -0.002 1724 -0.206*** 1112 -0.204***(0.029) (0.045) (0.051)Math test score 1302 6.960 690 6.945 422 6.919 1992 0.015 1724 0.041 1112 0.026(0.072) (0.091) (0.115)Reservation wage (USD) 1301 253.155 690 246.173 422 231.962 1991 6.983 1723 21.193*** 1112 14.211***(3.016) (3.215) (2.736)* p\u00a10.1, ** p\u00a10.05, *** p\u00a10.01.Table C.6: Comparison of Samples Across the Three Experiments138(1) (2) (3) (4) (5) (6) (7)Disc (%) Cb. Own Neigh (%) Cb. Own Neigh (%) Cb. Own Neigh (%) Cb. Other Neigh (%) Cb. Other Neigh (%) Cb. Other Neigh (%)Favela Info -7.288\u2217\u2217 -2.419 -3.344\u2217 2.995 -8.049\u2217\u2217\u2217 -8.521\u2217\u2217\u2217 3.337(3.487) (1.886) (1.961) (3.925) (2.149) (2.116) (9.814)Full Info -20.371\u2217\u2217\u2217 -1.428 -3.962\u2217 11.417\u2217\u2217 -13.923\u2217\u2217\u2217 -14.918\u2217\u2217\u2217 12.625(3.692) (1.973) (2.055) (4.541) (2.217) (2.193) (12.195)Observations 690 690 554 136 690 637 53Sample All All Overestimators Underestimators All Overestimators UnderestimatorsControl Mean 35.46 36.60 40.62 18.36 59.29 61.34 29.71Favela=Full p 0.00 0.60 0.76 0.05 0.01 0.00 0.40* p\u00a10.1, ** p\u00a10.05, *** p\u00a10.01.Table C.7: Effects of Information on Beliefs for Under- and Overestimators139Figure C.1: Figure 4.4 with Lasso-selected Controls140Figure C.2: Figure 4.5 with Lasso-selected Controls141Figure C.3: Effects of Information Treatments on Beliefs and Applications by WhetherJobseekers Initially Under- or Overestimated the Favela Callback Rate142Figure C.4: Heterogeneous Effects in the Address Omission Experiment \u2013 No Controls143Figure C.5: Heterogeneous Effects in the Address Omission Experiment \u2013 Double-lassoControls144Figure C.6: Heterogeneous Effects of Information Treatments \u2013 No Controls145Figure C.7: Heterogeneous Effects of Information Treatments \u2013 Double-lasso Controls146diff p-val=0.040.04diff p-val=0.220.24diff p-val=0.050.04Double-lasso ControlsNo ControlsAgg.*High Exp. DiscAgg.*Low Exp. DiscSelf*High Exp. DiscSelf*Low Exp. DiscInterv.*High Exp. DiscInterv.*Low Exp. Disc-.5 -.4 -.3 -.2 -.1 0 .1 .2 .3 .4 .5Effect of Name-Only on Interview Performance (SDs)95% CI90% CIdiff p-val=0.090.03diff p-val=0.200.12diff p-val=0.140.04Double-lasso ControlsNo ControlsAgg.*WhiteAgg.*Non-whiteSelf*WhiteSelf*Non-whiteInterv.*WhiteInterv.*Non-white-.5 -.4 -.3 -.2 -.1 0 .1 .2 .3 .4 .5Effect of Name-Only on Interview Performance (SDs)95% CI90% CIdiff p-val=0.490.49diff p-val=0.990.83diff p-val=0.310.35Double-lasso ControlsNo ControlsAgg.*Lower-SkillAgg.*Higher-SkillSelf*Lower-SkillSelf*Higher-SkillInterv.*Lower-SkillInterv.*Higher-Skill-.5 -.4 -.3 -.2 -.1 0 .1 .2 .3 .4 .5Effect of Name-Only on Interview Performance (SDs)95% CI90% CIdiff p-val=0.610.45diff p-val=0.440.25diff p-val=0.900.70Double-lasso ControlsNo ControlsAgg.*MaleAgg.*Non-maleSelf*MaleSelf*Non-waleInterv.*MaleInterv.*Non-male-.5 -.4 -.3 -.2 -.1 0 .1 .2 .3 .4 .5Effect of Name-Only on Interview Performance (SDs)95% CI90% CIFigure C.8: Heterogeneous Effects of Name-Only147Audit Estimates0100200300400Number of Respondents0 10 20 30 40 50 60 70 80 90 100Predicted callback rate  (%)Mar\u00e9 r\u00e9sum\u00e9 Bonsucesso r\u00e9sum\u00e9Audit Estimate0100200300400Number of Respondents-50 -25 0 25 50 75 100Predicted callback decrease if resum\u00e9 is from Mar\u00e9 vs. Bonsucesso (%)Outside audit's 95% CIWithin audit's 95% CIFigure C.9: Predicted vs. Actual Discrimination Rates148354045505560Discrimination Predicted in Audit Study (%)0 1 2 3Net Likert Discrimination (Favela - Non-favela)406080100Discrimination Predicted in Audit Study (%)0 20 40 60 80 100Discrimination Implied by Non-favela Counterfactual for Self (%)Note: Negative values of discrimination are pooled with zero discrimination \u2013 since there are few observationwith negative discrimination, which make estimates noisy. We construct the Likert discrimination measure bytaking the Liker-scale answers of how much employers discriminate against individuals in each neighborhood(from no discrimination to a lot), converting them into ordered integers, and and taking the difference.We calculate the discrimination for the counterfactual self by comparing the beliefs about one\u2019s job-findingprobability over the next six months to \u201csomebody just like you, but from [adjacent non-favela]\u201d.Figure C.10: Predicted Audit Study Discrimination Correlates with Other Measuresof Expected Discrimination149Figure C.11: Belief Update in Information Experiment Occurs for Mare\u00b4 and Non-Mare\u00b4Residents150C.2 Deviations from the Pre-Analysis Plan\u2022 We initially planned to stratify the randomization in the Interview Experiment bypredicted discrimination level and previous treatment assignments. On implementationwe kept only stratification by the discrimination level. That is because, given thelogistical constraints and lower-than-expected interview show-up rates, the batch sizesfor the interview stage would generate a very small number of observation per strata.\u2022 We pre-registered our in-survey math test as the main skill measure, but we later judgedit was too narrow with respect to a sales job. Hence, we also included education and ameasure of communication skills.\u2022 The receptionist randomized the treatment of ten participants at the office, and resultsdo not change by excluding them. She conducted the on-the-spot randomization wheneither i) she could not locate the jobseeker\u2019s treatment status (e.g., due to internetconnection issues), or ii) a candidate was mistakenly invited to the interview beforebeing assigned a randomization batch, or iii) the number of candidates schedules for aperiod was too low for make up a single strata.\u2022 We also updated our experimental design after completing half of our fieldwork. Seehttps:\/\/www.socialscienceregistry.org\/trials\/11041 for details.151C.3 Audit StudyPicking Re\u00b4sume\u00b4 Addresses. For addresses in each neighborhood, we picked streets thatwere i) entirely contained in the neighborhood, ii) in the postal office list, and iii) up to a15-minute walk from a bus stop in the avenue between Mare\u00b4 and Bonsucesso. These choicesguaranteed that employers could back out neighborhood unambiguously, and keep commutingtime to any job as constant as possible.C.3.1 Audit Study NeighborhoodsNote: This image shows the geographic location of the two neighborhoods for the audit study: Bonsucesso(Non-Favela) and Mare\u00b4 (Favela). The large avenue in the picture is the divide between each region.Figure C.12: Bonsucesso (Non-Favela) vs. Mare\u00b4 (Favela)152C.3.2 Re\u00b4sume\u00b4sNote: This image shows one of the re\u00b4sume\u00b4s used in the audit study. We drew the red box around the addressin this picture for emphasis. It was not present in the original re\u00b4sume\u00b4.Figure C.13: Example Re\u00b4sume\u00b4 \u2013 Mare\u00b4 home address153Note: Image shows one of the re\u00b4sume\u00b4s used in the audit study. We drew the red box around the address inthis picture for emphasis. It was not present in the original re\u00b4sume\u00b4.Figure C.14: Example Re\u00b4sume\u00b4 \u2013 Bonsucesso Address154C.3.3 Job PostingsNote: This is a job posting for one salesperson position in a dental clinic posted in Infojobs. It required amiddle school degree and no previous work experience.Figure C.15: Examples of Job Posting155C.3.4 Results(1) (2) (3)Callback (%) Callback (%) Callback (%)Mare\u00b4 re\u00b4sume\u00b4 -0.34 -0.40 -1.04(1.28) (1.29) (1.18)Observations 1400 1400 1400No Info Mean 16.96 16.96 16.96Controls No Yes NoJob FEs No No YesNote: Outcome variable evaluates to 100 if the application received a positive response and zero otherwise.Mare\u00b4 re\u00b4sume\u00b4 is a dummy for the fictitious applicant being from Mare\u00b4. Controls include the job\u2019s city region,and the website in which we found it. The callback level here is about 3% lower than than the numbers usedin the Information Experiment because for the regressions we only consider callbacks we could link to uniquepostings. Standard errors clustered at the posting level shown between parenthesis.Table C.8: Audit Study Results156C.4 Materials Used in ExperimentsNotes: This Figure shows surveyors interviewing research participants in Mare\u00b4.Figure C.16: Door-to-Door Baseline Survey157Note: This Figure displays how we elicited prior beliefs about discrimination against favela dwellers.Figure C.17: Predicted Discrimination Baseline Script158Figure C.18: Partner\u2019s Job Descriptions159(a) Status Quo (b) Address Omission(c) Known AddressFigure C.19: Second Screen of the Application Form of Each Experimental Conditionin the Address Omission Experiment160C.4.1 Interview Experiment Details(a) Co-Working Reception (b) Interview RoomFigure C.20: Interview Co-Working SpaceC.4.2 Interview ScriptIntroductionsYou [the interviewer] must treat all candidates equally and as uniformly as possible. Ideally,your tone will be friendly and reserved.Introduce yourself and confirm the candidate\u2019s name. Let the candidate know that the inter-view will be recorded, for quality control and training of future interviewers.Stick to the script as much as possible. Then you should say that you are going to start theinterview. If you have questions, you should wait until the end.161Interview\u2019s QuestionsQ1. How comfortable do you feel working with laptops\/computers?(1) Very comfortable, (2) A little comfortable, (3) Indifferent, (4) A little uncomfortable, (5)Very uncomfortableQ2. Do you typically send emails or type more complex texts? Can you tell me the last timeyou did something like this? OPEN ANSWERQ3. Have you ever used Word, Excel, or similar programs? If so, can you give me an exampleof something you have done with this program? OPEN ANSWERQ3. Have you ever used Word, Excel, or similar programs? If so, can you give me an exampleof something you have done with this program? OPEN ANSWERInterviewer evaluates how well the candidate did on this question, from 0 to 10Q4. Now I will also you to do an activity. Think of a product you like and know well. Itcould be a type of clothing, a cell phone, a car, anything, but preferably something that youknow how to describe and sell well, ok?Can you try to convince me that I should buy this product from you or your store, insteadof buying from a competitor? As if you were the seller of that product. OPEN ANSWERInterviewer evaluates how well the candidate did on this question, from 0 to 10, and alsowrites down: (i) the product sold, (ii) the main argument, and (iii) whether it was convinc-ing.Q5. What would you say are your top 3 skills for a sales job, and why do you think you aregood at them? It could be an example showing why you are good too. OPEN ANSWERInterviewer evaluates how well the candidate did on this question, from 0 to 10Q6. And your main disadvantages? Can you explain or give examples of how they affectyou? OPEN ANSWERInterviewer evaluates how well the candidate did on this question, from 0 to 10Q7. What do you think makes you the best fit for this position, compared to your competi-tors? OPEN ANSWER162Interviewer evaluates how well the candidate did on this question, from 0 to 10Q8. Thinking about your background and your day-to-day life, how would you say yourexperiences would help you to be a good fit for this position? You don\u2019t just need to giveprofessional experiences. It could be academic, school, some leadership position, participa-tion in social projects, volunteer work, or something else. OPEN ANSWERInterviewer evaluates how well the candidate did on this question, from 0 to 10Q9. Would you like to add any other information? OPEN ANSWERQ10. [Interviewees self-administer this question on a tablet]I see myself as a person that...1. Does a meticulous job2. It\u2019s a little careless sometimes3. It\u2019s trustworthy4. Tends to be disorganized5. Tends to be lazy6. Perseveres until tasks are completed7. Works efficiently8. Make and follow plans9. Is easily distractedOptions are: (1) Totally disagree, (2) Partially disagree, (3) Neither agree nor disagree, (4)Partially agree, (5) Totally agree.End of the Interview and Interviewer\u2019s AssessmentAsk if the candidate has any questions, and instruct the candidate to return to the receptionfor payment and final orientation.Immediately after saying goodbye to the candidate, the interviewer responds, on a scale from0 to 10 to each of the questions below. 0 means \u201cExtremely bad\u201d and 10 means \u201cExtremelywell\u201d.1631. Overall, how well did the candidate perform?2. How nervous did the candidate seem?3. How focused did the candidate seem?4. How professional was the candidate throughout the interview?164","@language":"en"}],"Genre":[{"@value":"Thesis\/Dissertation","@language":"en"}],"GraduationDate":[{"@value":"2024-05","@language":"en"}],"IsShownAt":[{"@value":"10.14288\/1.0441537","@language":"en"}],"Language":[{"@value":"eng","@language":"en"}],"Program":[{"@value":"Economics","@language":"en"}],"Provider":[{"@value":"Vancouver : University of British Columbia Library","@language":"en"}],"Publisher":[{"@value":"University of British Columbia","@language":"en"}],"Rights":[{"@value":"Attribution-NonCommercial-NoDerivatives 4.0 International","@language":"*"}],"RightsURI":[{"@value":"http:\/\/creativecommons.org\/licenses\/by-nc-nd\/4.0\/","@language":"*"}],"ScholarlyLevel":[{"@value":"Graduate","@language":"en"}],"Supervisor":[{"@value":"Valencia Caicedo, Felipe","@language":"en"}],"Title":[{"@value":"Essays in economic history and development","@language":"en"}],"Type":[{"@value":"Text","@language":"en"}],"URI":[{"@value":"http:\/\/hdl.handle.net\/2429\/87994","@language":"en"}],"SortDate":[{"@value":"2024-12-31 AD","@language":"en"}],"@id":"doi:10.14288\/1.0441537"}