{"http:\/\/dx.doi.org\/10.14288\/1.0427413":{"http:\/\/vivoweb.org\/ontology\/core#departmentOrSchool":[{"value":"Arts, Faculty of","type":"literal","lang":"en"},{"value":"Vancouver School of Economics","type":"literal","lang":"en"}],"http:\/\/www.europeana.eu\/schemas\/edm\/dataProvider":[{"value":"DSpace","type":"literal","lang":"en"}],"https:\/\/open.library.ubc.ca\/terms#degreeCampus":[{"value":"UBCV","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/creator":[{"value":"Pe\u00e7anha, Vinicius","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/issued":[{"value":"2023-03-09T22:42:36Z","type":"literal","lang":"en"},{"value":"2023","type":"literal","lang":"en"}],"http:\/\/vivoweb.org\/ontology\/core#relatedDegree":[{"value":"Doctor of Philosophy - PhD","type":"literal","lang":"en"}],"https:\/\/open.library.ubc.ca\/terms#degreeGrantor":[{"value":"University of British Columbia","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/description":[{"value":"Chapters 2 and 3 analyze a place-based policy that reduced the effects of lowering lethal violence at the neighborhood level for several years in some of the most violent neighborhoods on earth. Chapter 2 discusses how this reduction affects short-run learning gains, employment, and incarceration for treated individuals in their early adulthood. The policy increases human capital for students in the short run. Fewer disruptions in the school routine, less student absenteeism, and a safer environment \\textit{within} school drive these results. Moreover, younger individuals have a substantially lower likelihood of being incarcerated later.  \r\n\r\nChapter 3 evaluates the spatial spillover induced by the policy. I find that the program decreased homicides and police killings in treated areas and did not cause crime displacement to other places in Rio de Janeiro. There is suggestive evidence of crime migration to areas in Rio's metropolitan region and the state's countryside.\r\n\r\nIn Chapter 4, I investigate how localized heat stress affects vulnerable populations \\emph{within} the city of Rio de Janeiro. It is known that temperature shocks increase mortality, and the link is primarily via human physiology. However, most of this evidence comes from cross-city and epidemiological studies in developed countries. This chapter examines the heat-mortality relationship at a fine-grained level within Rio de Janeiro. We rely on novel satellite imagery sources on temperature and administrative health records at the individual level to build a neighborhood-by-month panel over 14 years. Heat stress increases all-cause mortality in individuals aged 60 years or older but does not affect other age groups. In particular, we find that hot days in a typical month in Rio account for 2\\% of cardiovascular deaths in the population 60+. Access to preventive health care can attenuate the marginal effect of temperature on these deaths. We conclude that temperature shocks are localized within cities, implying that remedial policies should also be localized.","type":"literal","lang":"en"}],"http:\/\/www.europeana.eu\/schemas\/edm\/aggregatedCHO":[{"value":"https:\/\/circle.library.ubc.ca\/rest\/handle\/2429\/83911?expand=metadata","type":"literal","lang":"en"}],"http:\/\/www.w3.org\/2009\/08\/skos-reference\/skos.html#note":[{"value":"Essays on Urban Violence and HealthbyVinicius Pec\u00b8anhaB.A., Federal University of Rio de Janeiro, 2014M.A., Getulio Vargas Foundation, 2015a 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)March 2023\u00a9 Vinicius Pec\u00b8anha, 2023The following individuals certify that they have read, and recommend to the Faculty ofGraduate and Postdoctoral Studies for acceptance, the thesis entitled:Essays on Urban Violence and Healthsubmitted by Vinicius Pec\u00b8anha in partial fulfillment of the requirements for the degree ofDoctor of Philosophy in Economics.Examining Committee:Claudio Ferraz, Professor, Vancouver School of Economics, UBCCo-SupervisorThomas Lemieux, Professor, Vancouver School of Economics, UBCCo-SupervisorJamie McCasland, Professor, Vancouver School of Economics, UBCSupervisory Committee MemberNathan Nunn, Professor, Vancouver School of Economics, UBCUniversity ExaminerSumeet Gulati, Professor, Faculty of Land and Food Services, UBCUniversity ExaminerAdditional Supervisory Committee Members:Siwan Anderson, Professor, Vancouver School of Economics, UBCSupervisory Committee MemberiiAbstractChapters 2 and 3 analyze a place-based policy that reduced the effects of lowering lethal vi-olence at the neighborhood level for several years in some of the most violent neighborhoodson earth. Chapter 2 discusses how this reduction affects short-run learning gains, employ-ment, and incarceration for treated individuals in their early adulthood. The policy increaseshuman capital for students in the short run. Fewer disruptions in the school routine, lessstudent absenteeism, and a safer environment within school drive these results. Moreover,younger individuals have a substantially lower likelihood of being incarcerated later.Chapter 3 evaluates the spatial spillover induced by the policy. I find that the programdecreased homicides and police killings in treated areas and did not cause crime displacementto other places in Rio de Janeiro. There is suggestive evidence of crime migration to areasin Rio\u2019s metropolitan region and the state\u2019s countryside.In Chapter 4, I investigate how localized heat stress affects vulnerable populations within thecity of Rio de Janeiro. It is known that temperature shocks increase mortality, and the linkis primarily via human physiology. However, most of this evidence comes from cross-city andepidemiological studies in developed countries. This chapter examines the heat-mortalityrelationship at a fine-grained level within Rio de Janeiro. We rely on novel satellite imagerysources on temperature and administrative health records at the individual level to builda neighborhood-by-month panel over 14 years. Heat stress increases all-cause mortality inindividuals aged 60 years or older but does not affect other age groups. In particular, wefind that hot days in a typical month in Rio account for 2% of cardiovascular deaths inthe population 60+. Access to preventive health care can attenuate the marginal effect oftemperature on these deaths. We conclude that temperature shocks are localized withincities, implying that remedial policies should also be localized.iiiLay SummaryThis thesis discusses development issues raised in urban contexts. In Chapter 2, I analyzethe effects of a public policy that decreased violence in poor neighborhoods in the city of Riode Janeiro on learning gains in the short-run, and on formal employment and incarcerationin the medium run. I evaluate the effects of this policy on crime displacement in Chapter3. Chapter 4 shows that localized heat stress within a city increases mortality, mainly forcauses of death that reflect underlying chronic conditions, on the elderly. We also show thatexpanding primary health care coverage can fully mitigate these adverse effects of heat stress.ivPrefaceThe research in Chapters 2 and 3 are original, unpublished and independent work by theauthor of this thesis, Vinicius Pec\u00b8anha. Chapter 4 is an original, unpublished, and joint workwith Rudi Rocha (Getulio Vargas Foundation) and Dimitri Szerman (Amazon). The otherco-authors contributed to the identification of the research question. Vinicius expanded theidea and mostly contributed to the design of the research project, review of the literature,cleaning and analysis of the data, and evaluation of the results. This chapter was writtencollaboratively.vTable of ContentsAbstract . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . iiiLay Summary . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . ivPreface . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . vTable of Contents . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . viList of Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . viiiList of Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xAcknowledgements . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xiiDedication . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xiv1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 12 The human capital effects of a neighborhood-level reduction in violence:Evidence from Rio\u2019s favelas . . . . . . . . . . . . . . . . . . . . . . . . . . . 42.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 42.2 Context and Policy Intervention . . . . . . . . . . . . . . . . . . . . . . . . . 92.2.1 Violence and Drug Gangs in Rio\u2019s Favelas . . . . . . . . . . . . . . . 92.2.2 UPP Program . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 112.2.3 Municipal School System in Rio . . . . . . . . . . . . . . . . . . . . . 132.3 Data and Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . . . 142.3.1 Violence . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 142.3.2 School outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 172.3.3 Medium-run outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . 202.4 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 242.4.1 Violence . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 242.4.2 School outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 25vi2.4.3 Medium-run outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . 292.5 Interpretation . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 302.6 Conclusion and Policy Takeaways . . . . . . . . . . . . . . . . . . . . . . . . 313 The Impacts of UPP on Violence . . . . . . . . . . . . . . . . . . . . . . . . 473.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 473.2 Context . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 503.2.1 Spatial Distribution of Drug Factions . . . . . . . . . . . . . . . . . . 503.2.2 Police structure in Rio . . . . . . . . . . . . . . . . . . . . . . . . . . 523.3 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 533.4 Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 553.5 Results and Discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 563.6 Conclusion and Further Steps . . . . . . . . . . . . . . . . . . . . . . . . . . 584 Heat and Health: A Tale of a Tropical City . . . . . . . . . . . . . . . . . 744.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 744.2 Background and Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 784.2.1 Rio de Janeiro: Geography, Climate and Inequality . . . . . . . . . . 784.2.2 Temperature . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 794.2.3 Health Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 834.2.4 Auxiliary Data and Controls . . . . . . . . . . . . . . . . . . . . . . . 844.3 Empirical Model . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 854.4 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 874.5 Access to Health Services . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 904.6 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 90Bibliography . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 100A Appendix to Chapter 2 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 111A.1 Linkage . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 123A.1.1 Conceptual Framework . . . . . . . . . . . . . . . . . . . . . . . . . . 123A.2 Panel student x year . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 125B Appendix to Chapter 3 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 126B.1 Corrections in police station information . . . . . . . . . . . . . . . . . . . . 126C Appendix to Chapter 4 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 128C.1 Dealing with Missing Values . . . . . . . . . . . . . . . . . . . . . . . . . . . 134C.2 Timing and expansion of health infra-structure . . . . . . . . . . . . . . . . . 135C.3 Neighborhoods\u2019 aggregation . . . . . . . . . . . . . . . . . . . . . . . . . . . 136viiList of TablesTable 2.1 Effects of the UPP treatment on violence rates . . . . . . . . . . . . . . . 33Table 2.2 Effects of the UPP treatment on standardized test scores . . . . . . . . . 35Table 2.3 Effects of the UPP treatment on school infrastructure and teachers\u2019 com-position . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 36Table 2.4 Effects of the UPP treatment on student composition . . . . . . . . . . . 37Table 2.5 Robustness for the effects of UPP treatment on standardized test scores:proxies for students\u2019 household income . . . . . . . . . . . . . . . . . . . . 38Table 2.6 Effects of the UPP treatment on educational indicators . . . . . . . . . . 40Table 2.7 Medium-run results for UPP treatment: years of exposure to treatmentwhile in primary school . . . . . . . . . . . . . . . . . . . . . . . . . . . . 42Table 2.8 Effects of UPP treatment on school environment . . . . . . . . . . . . . . 43Table 2.9 Effects of UPP treatment on expectations and violence within school . . . 44Table 2.10 Heterogeneity of the effects of UPP treatment on short- and medium-runoutcomes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 45Table 3.1 Summary statistics violence indicators per period of time . . . . . . . . . 65Table 3.2 Effects of the UPP on lethal violence . . . . . . . . . . . . . . . . . . . . . 66Table 3.3 Robustness for the effects of UPP on violence indicators . . . . . . . . . . 68Table 3.4 Effects of UPP on crime indicators \u2013 different control groups . . . . . . . 71Table 4.1 Summary Statistics of Neighborhood-Month Panel . . . . . . . . . . . . . 93Table 4.2 Effects of Hot Days on Mortality due to Cardiovascular Causes . . . . . . 95Table 4.3 Differential Effects of Temperature on Mortality due to CardiovascularCauses by Socioeconomic Measures . . . . . . . . . . . . . . . . . . . . . 97Table 4.4 Effects of Hot Days on Mortality due to Cardiovascular Causes by Educa-tion and Race . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 98Table 4.5 Mitigation Policies to Temperature shocks on Mortality due to Cardiovas-cular Causes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 99Table A.1 Summary statistics violence indicators - semester rates per 100,000 individuals113viiiTable A.2 Robustness for the effects of UPP treatment on violence rates . . . . . . . 114Table A.3 Socioeconomic characteristics form Census 2010 of Treated and UntreatedComplexes of favelas . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 116Table A.4 Summary statistics for Treated and Control schools from School Census 2007117Table A.5 Differences between whites and non-white boys for socioeconomic charac-teristics in Prova Brasil . . . . . . . . . . . . . . . . . . . . . . . . . . . . 118Table A.6 Heterogeneity of Treatment Effects of the UPP on standardized test scores- Early vs. Late treated . . . . . . . . . . . . . . . . . . . . . . . . . . . . 119Table A.7 Robustness of the effects of UPP treatment on standardized test scores:alternative definitions of treatment . . . . . . . . . . . . . . . . . . . . . . 120Table A.8 Robustness of the effects of UPP treatment on standardized test scores:alternative definitions of treatment . . . . . . . . . . . . . . . . . . . . . . 121Table C.1 Specific Causes - Age 60+ . . . . . . . . . . . . . . . . . . . . . . . . . . 132Table C.2 Effects of LST temperature on Cardiovascular outcomes (per 100,000 Indi-viduals aged 60+) - Alternative Imputations . . . . . . . . . . . . . . . . 132Table C.3 Effects of Hot Days on Mortality by Age and Cause of Death . . . . . . . 133ixList of FiguresFigure 2.1 Dynamic effects of UPP treatment on total homicides rates . . . . . . . . 34Figure 2.2 Robustness for the effects of UPP treatment on standardized test scores:difference-in-differences estimators . . . . . . . . . . . . . . . . . . . . . . 39Figure 2.3 Medium-run effects of the UPP treatment by age when treatment startedin the school . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 41Figure 2.4 Heterogeneity of UPP treatment effects on schooling by grades - Dynamiceffects . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 46Figure 3.1 Large favelas by treatment year . . . . . . . . . . . . . . . . . . . . . . . 60Figure 3.2 Temporal evolution for violence indicators for the city of Rio de Janeiro . 61Figure 3.3 Treated and Control police stations in Rio de Janeiro . . . . . . . . . . . 62Figure 3.4 Temporal evolution for violence indicators for treated and control stationsin the city of Rio de Janeiro . . . . . . . . . . . . . . . . . . . . . . . . . 63Figure 3.4 Temporal evolution for violence indicators for treated and control stationsin the city of Rio de Janeiro (cont.) . . . . . . . . . . . . . . . . . . . . . 64Figure 3.5 Dynamic effects of UPP on violence indicators . . . . . . . . . . . . . . . 67Figure 3.6 Temporal evolution of crime indicators for police stations in the state ofRio de Janeiro . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 69Figure 3.6 Temporal evolution of crime indicators for police stations in the state ofRio de Janeiro (cont.) . . . . . . . . . . . . . . . . . . . . . . . . . . . . 70Figure 3.7 Distribution of criminal groups in Rio de Janeiro . . . . . . . . . . . . . 72Figure 3.8 Distribution of drug gangs and militia in Rio de Janeiro - 2019 . . . . . . 73Figure 4.1 Rio de Janeiro: Land Use and Heat Map . . . . . . . . . . . . . . . . . . 92Figure 4.2 LST and Air temperature in Rio de Janeiro . . . . . . . . . . . . . . . . 92Figure 4.3 Neighborhood-Day Monthly Temperature Distribution . . . . . . . . . . 94Figure 4.4 The Effect of Daily Temperatures on Mortality due to CardiovascularCauses in Population 60+ . . . . . . . . . . . . . . . . . . . . . . . . . . 96xFigure 4.5 The Effect of contemporaneous and future (placebo) temperature exposureon Mortality . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 96Figure A.1 Spatial and Temporal Evolution of UPPs in the city of Rio de Janeiro . . 112Figure A.2 Dynamic effects of UPP treatment on police killings and other homicidesrates . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 114Figure A.3 Treated and Control clusters of favelas . . . . . . . . . . . . . . . . . . . 115Figure A.4 Age of the individual when treatment starts: variation by cohorts of birthand year of treatment in the school. . . . . . . . . . . . . . . . . . . . . . 122Figure A.5 Example for years of exposure to treatment in primary school . . . . . . 122Figure C.1 Time-Series and Cross-Sectional Residual Variation in Heat Stress . . . . 129Figure C.2 Time-series variation for the number of days above 40C as a fraction ofthe historical neighborhood-month average for selected neighborhoods . . 130Figure C.3 Robustness to different specifications . . . . . . . . . . . . . . . . . . . . 131Figure C.4 Expansion of health infrastructure over time and across neighborhoods inRio . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 135xiAcknowledgementsThere is a song (Cobra Rasteira, from the Brazilian group Meta\u00b4 Meta\u00b4) with two beautifulverses that describe my experience during the Ph.D.: \u201cNem todo trajeto e\u00b4 reto \/\/ Nem o mare\u00b4 regular\u201d. They mean that not every path is straight; not even the sea is linear. During thistrajectory over the years in graduate school, I faced several challenges that, while difficult,enriched my unique experience in life. And, most important, I was not alone.First, I would like to thank my wife, Amanda, for her patience and love. She shared theanxiety, frustrations, and joy throughout this long journey. This Ph.D. is yours as well. Ilove you. My family also deserves my gratitude. I\u2019ve been physically distant these years, butI do care. I missed many important moments, from deaths to births, for being abroad. Iwish I had been there at any of these events, and I am sorry that I couldn\u2019t.I am deeply grateful for the guidance and support of the committee members \u2013 Claudio,Thomas, Siwan, and Jamie. I am particularly in debt to Jamie. Her kindness, patience,intelligence, and mentorship were fundamental to this process.Vancouver brought me many friends who helped me with academic issues and the distanceto Brazil. Fernando and Ieda, thanks for listening to my complaints and showing me thatI could have fun in Vancouver. Brayan, even with the distance, our conversations inspiredme and helped me understand more about the limitations and the cynism of science \u2013 but,also its power. Pablo, Juan, Davide, Anand, Sev, and other members of my cohort: yourintelligence and research capacity pushed me further; you also taught me that I could havesome fun.I want to thank my friends from Rio\u2019s City Hall. Duda, Clara, and Rodrigo, from whom Ilearned about the technical part of policymaking and the politics of the process. Workingwith you made this research more credible to me. Ygor and Adriano, you showed me howcareful listening is a fundamental part of a policy. Paulo and Fernando: working with policyis also about managing crises. And good communication is an essential part of this process.I hope we can implement a public policy together again.xiiUBC 4YF partly funded the research in this thesis. I would only be able to do the researchwith this support. I also would like to thank NEREUS (The University of Sa\u02dco Paulo Regionaland Urban Economics Lab) for sharing relevant data to this research.xiiiDedication\u2013 A` Amanda e a` nossa ohana. A` minha fam\u0131\u00b4lia pelo amor incondicional.xivChapter 1IntroductionThe Thesis discusses development economics issues and policies to deal with some of themin an urban scenario. These are relevant questions because most citizens will live in a cityby 2030, and the majority will be in urban areas by 2050 (UN, 2018). Notably, cities faceseveral specific challenges, such as urban violence, the impacts of climate change, and howwe deal with inequality and spatial segregation (Glaeser and Cutler, 2021). These problemsdeserve our attention as development economists and demand responses tailored to citiesthat incorporate specific features of the urban context.In my Thesis, I analyze policies that deal with some of these concerns. Chapters 2 and 3examine a policy to reduce urban violence in some city areas. More specifically, in the secondchapter, I investigate the short impacts on learning gains and the medium-run effects onincarceration and formal employment of a policy that reduced violence in poor neighborhoodsin the city of Rio. In the third chapter, I analyze the spatial consequences in terms of crimein the city and metro area of Rio, and I discuss the crime dynamics after this policy. Andfinally, in the last chapter, I estimate the impacts of temperature shocks within the city andhow localized public policies can mitigate these effects.The second chapter evaluates a large place-based policy that sharply reduced violence for upto four years in poor neighborhoods (favelas) in the city of Rio. There are challenges to iso-lating the effects of urban violence decrease at the favela level on learning gains and outcomesin early adulthood. Notably, urban violence is ingrained in social contexts that are difficultto rapidly change (UN Habitat, 2007). To overcome this limitation, I evaluate a policy, thePacification Police Units Program (UPP), that altered policing strategy in treated favelas.Instead of intermittent police raids, the approach focused on the permanent occupation ofsome of these neighborhoods by community-oriented policing. The program was designedto reduce the territorial control of drug traffickers and to create a safe environment for the1mega-events that would happen in Rio, such as the 2014 World Cup and the summer 2016Olympic games. The program started in 2008, and as of 2014, it had treated 28 out of 53large favelas in the city, where more than 1.5 million citizens lived.I exploit the roll-out of this policy to show that it reduced total homicides by a fourth andpolice killings by almost 40% in treated areas. Moreover, this reduction lasts for six semestersafter the start of the program. Students in schools within treated areas have more significantstandardized test scores than those in similarly untreated large favelas. Due to the program,their test scores rise by 0.09 standard deviation for the Math exam and 0.07 for Reading.Fewer disruptions in the school routine, less student absenteeism, and a safer environmentwithin school drive these results. Observable changes in students\u2019 composition, teachers\u2019quality, infrastructure improvements, or increases in parental income do not conduct theseoutcomes. Moreover, individuals more exposed to the program while growing up have asubstantially lower likelihood of being incarcerated in their early adulthood. Each additionalyear in Primary school after the beginning of the UPP in a treated place reduces the pos-sibility of being imprisoned by 20%. Although there are data limitations, the evidence onthe medium-run mechanism is consistent with these effects being caused by changes in cog-nitive function associated with a less violent childhood and a change in drug-related careeropportunities for young men in favelas.In the third chapter, I discuss potential spatial spillovers caused by this place-based policy.Crime displacement is a primary concern for place-based policies. For example, negativespatial spillovers to areas in the control group violate the SUTVA assumption for causalinference and bias the results. I use data at the police station level (coarser than favelaunits) to evaluate the likelihood of crime displacement to untreated police stations. I showthat the violence indicators in untreated areas in the city of Rio also present a downwardtrend after the treatment. Given the size of the UPP policy, it is unlikely that a confounderdrives these trends. Thus, the results I found in the second chapter are not an econometricartifact caused by crime displacement to untreated areas. However, I also find suggestiveevidence of crime migration to regions outside the city of Rio, such as the metropolitan areaand the countryside of the state of Rio.Chapter 4 revisits the heat-mortality relationship by studying the role of localized temper-ature shocks within the city of Rio. A growing stream of causal evidence has shown thatchanges in environmental factors affect human health. The heat-mortality relationship hasattracted particular attention, as the potential risks of climate warming and average tem-perature changes are expected to be widespread across the globe. Detrimental effects ofexposure to heat waves and extremely high temperatures, considered one of the most dam-aging events, have been well documented in different contexts in developed and developing2countries. This has been made possible, to a great extent, by the utilization of plausiblyexogenous variation in weather indicators at the national and sub-national levels. A centralempirical question, however, is how localized these effects are. This is especially relevantshould damage be heterogeneous within regions. While much of the existing evidence comesfrom estimates of average treatment effects at the regional level, little is still known aboutthe extent to which the impacts and the distribution of damages are localized in general andhow effective localized policy responses can be in particular.We construct novel data from high-frequency satellite imagery on land surface temperature(LST) and health records to assemble a neighborhood-by-month panel over 14 years. Withthese data, we explore within-neighborhood variation in temperature to identify the effectsof heat stress on health outcomes. In particular, we investigate the effects of temperatureshocks on the mortality rates due to cardiovascular diseases of individuals aged 60 years andolder. We find that days above 40 degrees Celsius in a typical month in Rio account for2% of deaths due to cardiovascular conditions in the population 60+. However, we showthat access to preventive health care can mitigate these adverse effects. We contribute tothe literature with novel evidence on spatial heterogeneity in heat stress damages, whichhas implications for the optimal design of policies to attenuate the harmful consequences oftemperature shocks.3Chapter 2The human capital effects of aneighborhood-level reduction inviolence: Evidence from Rio\u2019s favelas2.1 IntroductionUrban violence is one of the main concerns for citizens in Low- and Middle-Income Countriesand imposes significant welfare and economic losses due to violence (Jaitman et al., 2015).Cerqueira et al. (2019) estimate that Brazil, for example, has economic losses as large as6% of its GDP. Moreover, shootings and chronic exposure to violence directly impact schooloutcomes (Monteiro and Rocha (2017); Ang (2021), Koppensteiner and Menezes (2021)) andhave long-term consequences in the labor market, health, and prison outcomes (Sviatschi(2022); Chetty et al. (2016); Damm and Dustmann (2014)). Nonetheless, little is knownabout the human capital effects of reducing urban violence at the neighborhood level andits consequences in the medium run. Most of the papers in the literature focus either onexposure to acute episodes of violence (Rossin-Slater et al. (2020); Bharadwaj et al. (2021);Cabral et al. (2021)), interventions at the individual level to cope with violence (Blattmanet al., 2017) or on programs that move individuals out of a violent neighborhood to a saferenvironment (Chyn, 2018).In this paper, I estimate the impact of a place-based policy that decreased lethal violence forup to four years in some of the most violent neighborhoods (also known as favelas) on earthon short- and medium-run outcomes. Initially, I focus on the human capital effects of thisneighborhood-level reduction in violence. I analyze students\u2019 performance in standardizedtest scores and show how the policy induces learning gains. Then, I explore the effect of4the policy on altering individuals\u2019 trajectories in the medium run by either increasing theirchances of formal employment or reducing their criminal involvement1. Finally, I discuss ifhuman capital improvement due to a less violent environment translates into medium-runoutcomes.There are several challenges to credibly estimating urban violence reduction at neighborhoodlevels on human capital effects and their impacts later in life. First, urban violence hasdeep-root causes that are hard to alter in the short run (UN Habitat, 2007). Thus, successfulpublic policies that decreased urban violence at the local level had either a longer timehorizon by focusing on social investments or institutional reforms (Hoelscher and Nussio,2016). Moreover, as in many other cities in Latin America, criminal groups control parts ofthe territory and display criminal governance in these neighborhoods, imposing difficultieson the government to implement public policies in there (Uribe et al., 2022). Second, thereis an empirical challenge. Data limitations restrict researchers\u2019 capacity to address certainquestions. Specifically, it is only possible to analyze the medium-run effects of a policy withidentified administrative data.To overcome the first challenge, I analyzed a large public policy that tackled urban violenceby changing the logic of policing strategy. Before the program, the Police relied on a \u2018logicof war\u2019 (Prado and Trebilcock, 2018) against drug traffickers focused on intermittent policeraids, which often caused shootings in the favelas (Lessing, 2017), disrupting citizens\u2019 livesand increasing the risk of these individuals getting caught in the crossfire. With the beginningof this new policy, the strategy shifted to installing permanent police stations in the favelasand operating in the logic of policing closer to citizens\u2019 needs. The Pacification Police UnitsProgram (UPP) was established in some poor neighborhoods to end armed control of theterritory by drug gangs and introduce community-oriented police in the favelas. The programwas designed to curb criminal power in Rio\u2019s favelas and to prepare the city for the mega-events (2014World Cup and 2016 Summer Olympics) happening a few years ahead (Willadinoet al., 2018). The UPP program rapidly expanded over time. From the end of 2008 until2014, 38 UPP units were installed in 28 out of 53 large favelas in Rio, reaching almost 1.5million citizens \u2018treated\u2019.Regarding the empirical challenge, I use several data pieces in this work, such as violenceoutcomes geocoded at the treated favela level, national standardized test scores from ProvaBrasil, School Censuses, and administrative datasets linked by name and date of birth. Inparticular, I employ the school records data for the universe of students enrolled in municipalpublic Elementary and Middle schools from 2000 to 2014, the Brazilian Employer-Employee1These two medium-run outcomes can be understood as the extreme points of a spectrum of job quality(Musumeci, 2016; Willadino et al., 2018). While drug-related jobs are risky and do not require many years ofeducation, formal labor market positions are stable and correlate with (more) human capital-intensive jobs.5matched dataset (RAIS) that displays information about all formal labor market connectionsin the state of Rio de Janeiro, and the universe of individuals incarcerated in 2018 for thestate of Rio de Janeiro. The administrative datasets allow me to link students in schoolsin large favelas before the beginning of the program to the labor market and incarcerationoutcomes later in their lives.I rely on the staggered introduction of the UPP program, which is unanticipated by the agentsand generates a temporal and spatial variation of exposure to the treatment to identify thecausal effects. I perform three empirical exercises that shed light on the policy\u2019s short- andmedium-run effects. First, I use the geocoded violence data for ever-treated favelas to testin a difference-in-differences framework if violence decreased in treated areas relative to not-yet-treated places. Second, I use individual test scores for students in schools located in largefavelas to estimate the effects of the policy on learning and human capital. I complement thisdata with a rich set of information from Students\u2019, Teachers\u2019, and Principals\u2019 socioeconomicsurveys to explore the channels for these effects. Finally, I employ the administrative schoolrecords data to find the individuals who were enrolled in schools in treated or untreatedfavelas before the beginning of the UPP program. I link these students with the otheradministrative datasets \u2013 formal labor market and incarceration data \u2013 that encompass theuniverse of individuals with a formal job and incarcerated in 2018. I analyze how the policychanges the likelihood of being present in these medium-run data and how the effects varydepending on the age of individuals when treatment started in their school. I adopt a cohort-place fixed effects strategy (Hoynes et al., 2016) that estimates the Intend-to-Treat effect ofbeing exposed to the treatment at a certain age.I show that UPP decreases total homicides in treated favelas by almost 25%. Moreover, dueto the change in policing strategy in treated favelas, police killings reduce by 38%. The policyinduces a level-shift decrease in total homicides until six semesters after the beginning of thetreatment. Thus, the results show that UPP significantly reduced exposure to lethal violencein treated favelas. Crime displacement is a primary concern for place-based policies. Thesenegative spatial spillovers violate the SUTVA assumption for causal inference and bias theresults. In the Second Chapter of the Thesis, I provide a more detailed discussion of crimedisplacement by using data at the police station level (coarser than favela units). With thisdata, I test the likelihood of crime displacement to untreated police stations2. I show in thenext chapter that the violence indicators in untreated areas also present a downward trendafter the treatment. Given the relevance and magnitude of the UPP policy, it is unlikely thata confounder drives these results. Thus, relevant to this paper, there is no evidence of crimedisplacement to untreated favelas.2I define a police station as untreated if there are large untreated favelas within its catchment area. Iwill provide a more profound discussion in the next chapter.6For the short-run results, I test whether treated students in Primary school (5th and 9thgrades) perform better on national standardized exams than individuals in schools locatedin untreated favelas. Test scores increase by 0.09 standard deviation for the Math exam and0.07 for Reading. The results last for (at least) three exam waves after the treatment. Thesefindings are not driven by observable changes in students\u2019 composition, teachers\u2019 quality,infrastructure improvements, or increases in parental income. Moreover, I do not find theeffects of the UPP treatment on other educational outcomes at the school level, such asdropout or age-grade distortion rates. I observe, however, that the significant decrease inviolence in treated places translates to less violence within school, fewer disruptions in theschool routine, and less student absenteeism. These results are consistent with the effectsdriven by reducing the violence burden and creating a more stable learning routine at school.In the medium-run, the estimates indicate that the younger the citizen was when treatmentstarted in their school, the lower the probability of being incarcerated in early adulthood.These results hold up to individuals aged 14 years old or less when UPP treatment began.In a similar empirical exercise, I calculate the number of predicted years of exposure totreatment while in Primary school (grades 1 to 9), and I find that each additional year inthis educational stage reduces the likelihood of being incarcerated by 20% of the samplemean.Can human capital impacts captured in the short-run test scores explain medium-run incar-ceration effects? Short-run test score gains and medium-run reductions in incarceration areboth concentrated among boys, suggesting human capital gains may play some role in laterlife outcomes. Alternatively, short- and medium-run effects could be driven by a third per-sistent mediating variable unobserved by the econometrician that arises from a reduction inexposure to violence or to criminal gang members. Some plausible examples include improve-ments in cognitive or psychosocial function that are concentrated among boys or reductionsin remunerative employment opportunities in the drug trade (for students in primary schoolbut also in early adulthood).Although it is difficult to disentangle these mechanisms with the available data, there isevidence that the effects are not driven by a strictly human capital mechanism. First, thereare no medium-run effects on participation in the formal labor market. Second, learningeffects dissipate over time. I observe two cohorts in both grade 5 and grade 9 (in a repeatedcross-section). Large test score gains for exposed cohorts in grade 5 do not persist to grade9, where there are no learning improvements for these early exposure cohorts.Closer to this paper, Prem et al. (2021) study the impacts of FARC\u2019s conflict terminationon educational outcomes in Colombia. They find that the decrease of violence exposure inplaces with previous FARC presence reduces dropout and modestly improves test scores. I7expand their research by discussing the medium-run impacts of violence reduction and byfocusing on a context plagued by urban violence. Furthermore, Ang (2021) provides evidencethat police killings have detrimental short and medium-run consequences for Hispanic andblack individuals. I show that reducing lethal violence, especially police violence, increasestest scores, but these effects are suggestively higher for white citizens. The results in thispaper suggest that only decreasing police killings and lethal violence at the neighborhoodlevel may not close the race gap in test scores.This work contributes to the growing literature on the impacts of exposure to violence onseveral outcomes. Monteiro and Rocha (2017), Duque et al. (2019), Koppensteiner andMenezes (2021), and Sviatschi (2022) discuss how acute violent episodes impact schools,health, and labor market results. I expand this literature by analyzing a relatively persistentlevel shift in violence exposure and not only single episodes. Ferraz et al. (2015), Magaloniet al. (2020), Lautharte (2021), and Ribeiro (2020) evaluate the impact of UPP on violenceand criminal governance, infant outcomes, and school routine3, respectively. I add to thisliterature by analyzing the effects of the policy on learning outcomes and discussing thepolicy\u2019s medium-run effects.I also add to the literature on neighborhood effects and policies that alleviate the consequencesof growing up in a poor neighborhood (Chetty et al., 2016; Chetty and Hendren, 2018; Chyn,2018). I contribute to this stream of literature by showing the results of a policy that changeda critical feature of these neighborhoods by reducing homicides and police killings whilearguably holding other unobservables such as social networks and interactions, and informalinstitutions constant. I report the effects on individuals who lived in the same neighborhoodas before but, after the policy, in a less violent environment. The results suggest that it ispossible to change the opportunity of citizens without moving them to places further away.Besides this introduction, the paper contains six more sections. In section 2, I analyze theinstitutional context of Rio\u2019s criminal market and the importance of the UPPs in this market.In section 3, I discuss the data and the empirical strategy of the paper. I show the results insection 4 and debate how the short- and medium-run results connect in section 5. Finally,in section 6, I conclude the analysis and discuss future work.3Ribeiro (2020) estimates the effects of the UPP on the number of days a school was closed due toshootings in its surroundings. In this paper, I improve his identification strategy by employing a Difference-in-Differences empirical strategy and by incorporating plausible treatment heterogeneity effects of the UPPpolicy.82.2 Context and Policy Intervention2.2.1 Violence and Drug Gangs in Rio\u2019s FavelasRio de Janeiro is one of the largest cities in the world, displays endemic violence levels,and has a complex criminal environment in which most of the city\u2019s poor neighborhoodsare ruled by drug factions (Magaloni et al., 2020). In 2007, a year before the beginning ofthe Pacification Police Units, the homicide rate in Rio was almost 53 homicides per 100,000citizens. On top of that, Rio has a violent Police force: in that year, the Police itself killed902 citizens, with a police killings rate of 14.6 deaths per 100,000 citizens.These numbers are higher than in other contexts with criminal presence, such as Colombia(37 deaths per 100,000 individuals)4 and Mexico (8 per 100,000)5, and are similar to placesthat display criminals gangs with substantial territorial control such as El Salvador (57 per100,000)6. Barcellos and Zaluar (2014) suggest that criminal groups\u2019 turf wars over territorialcontrol and the modus operandi of the Police in Rio explain this high homicide rate.The presence of criminal organizations that control parts of the territory and impose theirrule in these areas is widespread in Low- and Middle-Income Countries. For example, Uribeet al. (2022) estimate that more than 70 million citizens in Latin America live under thegovernance of criminal groups. These organizations negatively impact the socioeconomicdevelopment of the neighborhoods where they operate (Melnikov et al., 2020). In Rio deJaneiro and in parts of the state of Rio de Janeiro drug gangs started to operate in areas ofthe territory in the 1980s. These criminal groups locate in favelas (slums) in the hills of thecity of Rio de Janeiro and poor neighborhoods in the metropolitan region of the city. Coutoand Hirata (2022a) estimate that more than 1.5 million citizens (more than a fifth of thecity\u2019s population) were under criminal governance in the city of Rio before the beginning ofthe UPP program.The drug traffickers control these communities\u2019 social and economic activities, impose theirlaws and judge conflicting cases (Dowdney, 2003). Due to the adverse geography of theseplaces, police incursions are at a disadvantage in clashes with criminals, fortifying the com-mand of the drug gangs over the slums (Serrano-Berthet et al., 2012).There are three significant drug gangs - Red Command (CV), Friends of Friends (ADA),and Pure Third Command (TCP) \u2013 that started acting as prison gangs and, then becamecriminal enterprises displaying a high degree of criminal governance in the favelas (Hirata and4https:\/\/data.worldbank.org\/indicator\/VC.IHR.PSRC.P5?locations=CO. Accessed in July 2022.5https:\/\/smallwarsjournal.com\/jrnl\/art\/homicide-mexico-2007-march-2018-continuing-epidemic-militarized-hyper-violence. Accessed in July 2022.6https:\/\/data.worldbank.org\/indicator\/VC.IHR.PSRC.P5?locations=SV. Accessed in July 2022.9Grillo, 2017b; Blattman et al., 2022). The other major groups in Rio\u2019s criminal market arethe militias. Initially, the militia groups were formed by off-duty state officers, such as policeofficers and firefighters, to supposedly protect neighborhoods from drug traffickers. Once theycontrol the place, they sell private protection and other utilities in these poor neighborhoods(Cano and Duarte, 2012). Different from the drug factions, their actions are similar to amafia as described in Gambetta (1993), involving racketeering, rent-seeking activities, andinfiltration into the political system. Recently, there is anecdotal evidence that the militiaformed a partnership with drug traffickers and started selling drugs7.Within the favela, each leader promotes a vertical, hierarchical structure in the drug tradeorganization. Also, gang leaders improved upon former institutions in these neighborhoodsand developed relatively stable institutions in local governance, acting as local political agents(Arias, 2006, 2009). Unlike terrorists or insurgent groups, the gangs\u2019 leaders\u2019 objective func-tion is mainly an economic one (Lessing, 2008). Violence is instrumentally used to maintainorder (guarantee contracts or enforce their \u2018laws\u2019) or expand their business areas and not toincrease de jure political power or to destabilize social order by terror acts.The locus of the economic power of these groups are the favelas and poor neighborhoods,which shows how territoriality plays a role in the distribution of power of these factions. Thecompetition among the gangs and the militia, the profitability of these disadvantaged places,and the logic of territorial control engendered an arms race and turf wars over the favelas(Souza e Silva et al., 2008; Wolff, 2017).The criminal workers that are employed in drug factions are young (more than half of themare below 18 years old), non-white (more than 70%), boys (more than 90%), who were bornand live in the favelas they work (more than 70%) and more than half of them were raisedby their mothers alone (Willadino et al., 2018). In this survey, Willadino et al. (2018) showsthat these workers usually start in the drug business at ages below 15 years old (more than2\\3), don\u2019t attend school (78%), dropped out of school before high school, and earn between1 to 3 times the minimum wage. They mainly enter the drug business for economic reasons,either to help their family or to \u201cearn a lot of money\u201d, and most of them, more than 70%,were caught by the Police at least once.Before the UPP policy, the actions of Police in the status quo were based on a \u2018logic ofwar\u2019 (Prado and Trebilcock, 2018) with a strategy of intermittent police raids in the favelas,without a clear rationale for its actions (Lessing, 2017). Several reports stated that policecorruption was widespread in the Police (Misse, 2010; Soares, 2006). Before the program,7https:\/\/odia.ig.com.br\/rio-de-janeiro\/2018\/04\/5529467-milicianos-e-traficantes-se-aliam-para-a-venda-de-drogas-e-roubo-de-cargas.html#foto=1 and https:\/\/g1.globo.com\/rj\/rio-de-janeiro\/noticia\/milicia-controla-o-trafico-de-drogas-e-transporte-publico-em-regioes-da-zona-oeste-do-rio-segundo-investigacao-do-mp.ghtml.Accessed in June 2022.10there were no police stations within the favelas and little law enforcement from the Police inthese neighborhoods.2.2.2 UPP ProgramThe Pacification Police Units program (UPPs) was launched in December 2008 and had asits primary goals to end the armed control of the territory by drug gangs and to introducea community-oriented police8. The program was not focused on eradicating drug traffickingper se but on restoring State control through the monopoly of force in some selected favelas.The program\u2019s original design was intended to improve a suite of public services in favelas.This social arm of the program was called UPP Social. This arm would be responsible formapping communities\u2019 demands and proposing policies to address these concerns. Impor-tantly, UPP Social would have the political support to implement the social interventionsin treated favelas. However, due to political reasons9, UPP Social never worked as initiallyplanned10 and very few social policies were implemented in treated areas (Magaloni et al.,2018; Dias, 2017; Couto et al., 2016).Then, the UPP policy ultimately only included three key components: (1) the hiring of newpolice officers without a history of bribery or connection to the gang (Beltrame and Iaquinto,2014), (2) the territorial overrun of the space, and (3) the establishment of community policingstations inside favelas with an ongoing presence of police in the streets11. This increase inlaw enforcement in treated favelas caused a rise in the cost of doing drug business in theselocalities (Felbab-Brown, 2011).Given the focus on restoring territorial control from drug traffickers in favelas, the UPPintervention has an inherent place-based component. Moreover, decreasing the criminal gov-ernance in these places potentially impacts several dimensions of people\u2019s lives, and therefore,one might consider UPP as a bundled treatment. For example, the UPP program can increaselabor mobility and parental income or improve public and private investments in these areas.Although it may be challenging to disentangle all the treatment prospects, I will address8Policymakers also call the policing strategy as proximate policing (Magaloni et al., 2020). The conceptrelates to introducing police agents in that favela understand citizens\u2019 needs and respect their rights.9In meeting a former coordinator of UPP Social, she mentioned that UPP created a substantial politicalsurplus and that several political actors were fighting over this. If policymakers concentrated the socialpolicies in one technical area, it would be harder for other political actors to claim part of the surplus.Then, political actors did not give political support to implement these social policies. More in https:\/\/www.wola.org\/analysis\/what-can-be-learned-from-brazils-pacification-police-model\/. Accessed in July 2022.10https:\/\/rioonwatch.org\/?p=17660. Accessed in June 2022.11Cano et al. (2012) suggest the program was a paradigm shift in Rio\u2019s policing strategies against drugcriminals. Rather than performing episodic armed incursions in the favelas seeking drugs, guns, and criminals,the Pacification Police Unit program focused on establishing a permanent base of operations in the communityand breaking the territorial domination of the drug gangs.11some of these possibilities later in the empirical exercises. Notably, the UPP program didnot induce significant emigration of individuals since most of the citizens living in treatedfavelas were born or lived for more than ten years there (Musumeci, 2016). Thus, the policyarguably did not disrupt previous social interactions among neighbors in the favela.The Public Security Secretary used two loose criteria to establish a UPP in a slum: (i) thefavela had to be a poor community, and (ii) dominated by ostensibly armed criminal groups.Several researchers argue that the program was created as Rio\u2019s strategy for the mega eventsthat happen in the city, especially the World Cup 2014 and the Summer Olympics 2016(Frischtak and Mandel, 2012; Burgos et al., 2011; Magaloni et al., 2018; Silva, 2017; Felbab-Brown, 2011). They argue that the goal of UPP policy was to protect World Cup andOlympics areas, and, therefore, not systematically correlated to crime dynamics in Rio\u2019sfavelas12.Moreover, the project targeted large favelas composed of a cluster of small favelas13. These\u201cclusters of favelas\u201d were explicitly defined by the Rio de Janeiro District Attorney (MPRJ)in 2019 based on official information from Rio\u2019s City Hall14. They have a sizeable population,have been plagued by the presence of drug traffickers since the 1980s, and, importantly, theywere the spatial planning unit in which Rio\u2019s City Hall historically developed and imple-mented public policies, which engendered a shared sense of belonging to the neighborhood(Matiolli, 2016). Thus, these large favelas are defined as places that create a unique urbancluster and that share historical bonds among themselves15.The program gradually expanded over time. Between 2008 and 2014, 37 Pacification PoliceUnits were installed in the city of Rio de Janeiro, and 28 of 53 large favelas were treated.Figure A.1 displays the spatial and temporal evolution of the favelas treated by the UPPprogram. In terms of expansion over time, three large favelas were pacified in 2008, three in2009, thirteen in 2010, seven in 2011, five in 2012, five in 2013, and one in 2014.In figure A.3, I show that the treated units overlap with these large favelas. I will use theremaining ones as controls16. Table A.3 presents the descriptive statistics for the favelas intreated and control areas. Treated and control favelas are similar in almost all dimensions.There are two main differences: i) distance to Olympic venues, as I discussed above17 and12See also https:\/\/www.economist.com\/the-americas\/2013\/09\/14\/from-hero-to-villain-in-rio. Accessed inJune 2021.13Throughout the paper, I will refer to these neighborhoods simply as favelas or large favelas, althoughcolloquially in Rio, people would refer to them as \u201cclusters of favelas\u201d.14http:\/\/apps.mprj.mp.br\/sistema\/inloco\/. Accessed in July 2022.15https:\/\/wikifavelas.com.br\/index.php\/Sistema de Assentamentos de Baixa Renda (SABREN)#GrandesFavelas16This definition of treated and control units is similar to the one used in Ribeiro (2020).17Most the Olympic venues are pre-existing structures\/sites, so we would not expect construction to be aconfounding variable.12ii) the number of residents who earn more than ten times the minimum wage. Although theshare is small (less than 2%), treated favelas have almost four times more citizens earningmore than ten times the minimum wage than untreated favelas. This happens because someof the treated favelas are located in the wealthiest zone of the city. This area\u2019s average incomein favelas is higher than in other city zones.The policy was popular with residents in the early years. In two separate extensive surveys,Magaloni et al. (2018) and Ribeiro and Vilarouca (2018) show how individuals in different lo-calities have divergent responses about their general beliefs about the UPP program. Ribeiroand Vilarouca (2018) show that citizens in early-treated favelas (2008 to 2010) are more likelyto approve the program, while individuals in late-treated places have more concerns. Thesepapers suggest that recruiting enough new police officers, funding, and institutional supportfrom the police department became increasingly difficult during the scale-up of the policy,weakening the program\u2019s efficacy in later years. Therefore, I take this treatment heterogene-ity into account in the empirical strategy and use a DD estimator that explicitly allows fortreatment effect heterogeneity over the staggered introduction.2.2.3 Municipal School System in RioPublic schooling provision is constitutionally divided in Brazil in the following way: (i) Mu-nicipalities (cities) provide preschool, elementary (grades 1 to 5), and middle school (grades6 to 9) education and Youth and Adult Education; (ii) States supply high school educa-tion. Rio de Janeiro has the largest municipal school system in Brazil (Bartholo and Costa,2016) with around 1500 municipal public schools spread all over its territory, almost 40,000teachers, and attending more than 600,000 individuals from pre-school to Youth and AdultEducation18.The system has an open enrollment policy in which parents can choose any school for theirchildren19 (Bartholo, 2014). Thus, there are no school districts for Municipal schools inRio. Although this rule can create more heterogeneity among students, da Costa andde Souza Almeida (2019) suggests most students attend a school close to where they live.Indeed, most of the students in the data walk to school and live up to a 15-minute walkdistance of their school20.Most students in Rio are enrolled in municipal public schools. Lemgruber et al. (2022) show18More information in https:\/\/educacao.prefeitura.rio\/educacao-em-numeros\/. Accessed in June 2022.19Parents or individuals responsible for the students can use an online option or go directly to a school.In both cases, they are shown the schools with vacancies, and they can choose their preferred school. Moreinformation in https:\/\/carioca.rio\/servicos\/matricula-nas-escolas-e-creches-municipais\/. Accessed in June 2022.20In the main sample, more than 75% of students live up to a 15-minute walk distance, and 84% go toschool on foot13that almost 70% of total individuals in primary school years are enrolled in public schools.They also argue that there is a strong stratification between private and public schools:individuals with higher socioeconomic status tend to attend private schools.There are 409 out of 1540 municipal schools within a 100-meter buffer of large favelas. Thetypical favela has, on average, 7.7 units, and the typical school in a favela has more than600 enrollments per year. These suggest that schools are present in large favelas and have aconsiderable number of students enrolled.There is evidence that episodes of violence disrupt the school routine. Monteiro and Rocha(2017) and Lemgruber et al. (2022) analyze how drug battles and police incursions in thefavelas increase the number of days a school closes for external reasons and raise studentabsenteeism. Moreover, they show that the status quo policing and the presence of drugcriminals in these favelas also affect students\u2019 learning. Thus, it is expected that the UPPprogram could positively affect school outcomes by decreasing exposure to criminal gover-nance and episodes of violence.2.3 Data and Empirical Strategy2.3.1 ViolenceThe impact of the UPP program on violence levels in treated places can be seen as the \u2018firststage\u2019 of the estimation. Had the program not reduced violence exposure, I couldn\u2019t hypoth-esize that the policy\u2019s short- or medium-run impacts would be through violence reduction. Iutilize monthly official crime rates from the Institute of Public Security (ISP-RJ) from 2007to 2016 to test if the UPP policy reduces exposure to lethal violence. ISP-RJ defines totalhomicides as the sum of police killings21 and homicides committed by individuals, which Ilabel as other homicides in the following tables and graphs.The Institute of Public Security (ISP-RJ) does not provide geocoded information for allhomicides. In fact, I only have data for a limited but spatially more precise dataset of favela-level homicides and police killings encompassing only treated favelas. Thus, I could not usehomicides in untreated large favelas in this exercise. I provide a detailed control-group-basedanalysis of violence using police station-level data in the dissertation\u2019s second chapter22. Ialso discuss concerns about potential spatial spillovers of the treatment to control units thatmay bias the estimates in this chapter.21Police killings refer to homicides committed by police agents while on duty.22Police stations\u2019 catchment areas, which are the maximum spatial disaggregation with consistent officialstatistics, are larger than favelas. So, I define a police station as treated if there is at least one treated favelain its domain, and a control police station has a large untreated favela in its boundaries.14I show the summary statics for the main violence indicators in table A.1. Before the beginningof the UPP program (2007 and 2008), the mean semester homicide rate for ever-treated favelaswas 25.4 per 100,000 individuals23. In this period, police agents were responsible for most ofthe homicides committed in these large favelas. The bulk of these deaths happened in policeoperations within the favelas, which caused armed conflicts between the police and criminals(Monteiro et al., 2020). After the treatment, all violence indicators display a considerablereduction.The empirical specification is a difference-in-differences setup in which I control for semesterand favela fixed effects. The identification assumption is that treated, and not-yet-treatedunits would follow the same trend over time if the program had not happened. To identifythe UPP treatment effects on homicides, I exploit the staggered introduction nature of thepolicy and the fact that the timing of treatment was arguably exogenous once controlled byunobserved fixed favelas\u2019 characteristics. First, there was no official disclosure of informationabout potentially treated areas. Second, the occupation date was released to the public onlya week before the beginning of the treatment. I estimate the following equation:Yit = \u03bbi + \u03b4t + \u03b2Dit + \u03f5it (2.1)where Di\u03c4 is a dummy that turns one for periods after the beginning of the policy in favela i,\u03bbi and \u03b4t control for favela and semester fixed effects, respectively. The parameter of interestis \u03b2 which captures the impact of treatment on violence rates. The dependent variables aretotal homicides, police killings, and other homicides.To reduce concerns related to the skewness of the dependent variables, I collapse the data atthe semester level and use the inverse hyperbolic sine transformation of the dependent vari-able. I also show that the results are robust to Negative Binomial and Poisson specifications.As I discussed, there is enough qualitative evidence to be concerned about heterogeneoustreatment effects a priori. Thus, the preferred estimation incorporates this feature of thepolicy. I evaluate the impact of the program using the estimator proposed by Borusyak et al.23The yearly mean homicide rate for ever-treated favelas was 50.8 homicides per 100,000 citizens between2007 and 2008, which it is eight times bigger than US homicides rate in 2008 (Cooper et al., 2011)15(2022)24.I estimate a dynamic difference-in-differences specification to discuss how the effects of thepolicy evolve:Yit = \u03bbi + \u03b4t +\u22122\u2211\u03c4=\u22127\u03b3\u03c4Di\u03c4 +7\u2211\u03c4=0\u03b2\u03c4Di\u03c4 + \u03f5it (2.2)where, Di\u03c4 is dummy that turns one if t = T\u2217i + \u03c4 and T\u2217i is the semester that UPP startedin favela i. I collapse the data at the semester level to increase each estimate\u2019s precision.The parameters of interest, in this case, are the lags, {\u03b2\u03c4}\u03c4\u22650, and the leads, {\u03b3\u03c4}\u03c4<0. Thelags display the impact of the policy in \u03c4 periods of the program\u2019s implementation. I binnedperiods after 7 semesters and before 7 semesters of treatment to 7 and -7, respectively. Ifthe program could reduce violence in treated places, I would expect the lag coefficients tobe negative. The leads show the program\u2019s effects \u03c4 periods before it started. Assuming noanticipation effects, after controlling for place and time fixed effects, I shouldn\u2019t expect anydifference in pre-trends. Then, I expect that lead coefficients are not statistically differentfrom zero.For this dynamic specification, there is not enough power to estimate treatment effects inthe estimator proposed by Borusyak et al. (2022)25. Therefore, I show the OLS estimates forthe dynamic regression.There are two main concerns for the identification of the treatment effect. First, the violationof SUTVA (Rubin, 1986) due to spatial spillovers to not-yet treated units, which could occurif, for example, drug traffickers migrate from treated areas to not-yet-treated neighborhoodsand violence levels increase in their new location. In this case of crime displacement, the esti-mates would be overestimated. Or, if criminals in untreated favelas adapt to avoid treatmentin their areas, which would be a crime deterrence effect of the police. However, I considerthat crime deterrence in this setting is a minor concern because the estimates would be alower bound to the actual effect. I discuss these effects in more detail in the Second Chapter.24Borusyak et al. (2022) DD imputation estimator rely on the potential outcomes model E[Yit(0)] = \u03bbi+\u03b4t,where E[Yit(0)] is the potential outcome for unit i in period t if unit i were not treated. Then, they estimateunit and time fixed effects only on non-treated observations. The next step is to extrapolate the estimatesto treated observations by imputing Yit(0) = \u03bb\u02c6i + \u03b4\u02c6t. The authors calculate the treatment effect for unit iand period t as \u03c4it = Yit\u2212Yit(0). Finally, they aggregate \u03c4it using weights related to the estimand of interestto provide the estimate of the causal impact: \u03c4 =\u2211i,t \u03c9it\u03c4it. Under some common assumptions, they showthat their estimator is more efficient than other competing DD estimators. Moreover, they provide conditionsto test if pre-trend estimates differ from zero, while other estimators rely on placebos to shed some light onpre-trends.25Technically, the minimum effective number of observations is below the minimum recommended by theauthors. They argue that estimates with insufficient observations may be \u201cunreliable and their SE may bedownward biased\u201d (Borusyak et al., 2022).16Second, another concern may be raised if treatment is correlated with a contemporaneousviolence shock. That is, if treatment time is associated with increased violence before treat-ment caused by a temporary shock. Given the focus on pacifying areas close to Olympicvenues, I shouldn\u2019t expect this to be a concern a priori. If the introduction of a UPP in aplace correlates with an increase in violence, the pre-treatment estimates in an \u2018event study\u2019estimation strategy would be significant, a hypothesis that I test and reject.2.3.2 School outcomesI use individual grades from national standardized exams on Reading (Portuguese Language)and Mathematics from Prova Brasil that happen every two years for all students in the5th and 9th grades studying in public schools with more than 20 students enrolled in thatschool-grade. The National Institute of Educational Research from the Ministry of Education(INEP-MEC) designed the exams. Their main goal is to evaluate nationwide the educationalperformance of schools and design actions to improve learning26. Prova Brasil also containssocioeconomic surveys filled by students, teachers, and principals. These surveys providedemographic information about these groups and describe the learning environment at school.In particular, I use the variables in the surveys as covariates in the main regressions and I alsotest the impact of Pacification on changes in the school environment, teachers\u2019 expectations,and student composition after the treatment.The primary sample contains Prova Brasil exams from 2007 to 2015. There are two reasonsfor this time range. First, data is not consistent at the individual level for the 2005 wave of theexam. There are fewer observations at the student level than in other exam wave27. Second, asFerraz et al. (2015) and Willadino et al. (2018) argue, the UPP program decreased violencesuccessfully until after the 2014 World Cup and the 2016 Summer Olympics. However,violence levels returned to pre-treatment in treated areas after 2016. By including examyears after 2015, the treatment effects could be contaminated by the increase in violence;therefore, I do not include more recent years in the main analysis.I utilize geocoded schools\u2019 locations from Institute Pereira Passos (IPP), Rio\u2019s City HallResearch Institute, to restrict the sample to schools within 100 meters of distance to atreated or an untreated complex of favelas. I select this threshold of 100 meters because thepaper focuses on exploring the local effects of Pacification on school outcomes. Then, I wantto restrict schools located within treated or control favelas. I allow a 100-meter buffer to deal26The scores are used to build the Index of Basic Education Development (IDEB), which is an input forFederal transfers to States and Cities in Brazil.27For example, 41,783 observations for all students in Brazil who took the exam in grade 5 in 2005, whilethere are 2,310,302 observations in 2007. Moreover, no variable allows me to identify the school attended bythe student in 2005. Then, I chose not to incorporate this year into the primary sample.17with any geocoding issue that may arise in the spatial organization of the data28. Moreover,I keep only schools that appear in all waves of the Prova Brasil exam. With these criteria,there are 60 schools and 23,291 students in treated areas and 78 schools and 38,760 studentsin control areas.I aggregate School Census information, annually updated by the National Institute of Ed-ucational Research from the Ministry of Education (INEP-MEC) to the Prova Brasil data.They contain information about the universe of schools in Brazil. The variables encompassschool characteristics such as the number of enrollments, employees, infrastructure, and stu-dent and teacher characteristics. Moreover, the School Census provides information aboutother educational indicators at the school level, such as pass rate, grade retention, age-gradedistortion, and dropout rates. I employ this data to test if educational attainment changesin treated schools relative to schools in the control group. A priori, the UPP program mayimpact these indicators either positively or negatively. On the one hand, if students at themargin of dropping out stay at school longer because of the program, pass rate, grade re-tention, and even age-grade distortion may be negatively affected. On the other hand, ifstudents of lower (higher) quality move into treated schools, I could observe the program\u2019snegative (positive) effect on these educational indicators.I define a school as treated in a specific exam wave if the school is located in a favela pacifiedat least three months before the exam29. The exams usually happen in November. So, aschool is treated if the favela was pacified by June of the exam year. Since the exam happensin odd years, if a UPP treats a school in an even year, the treated year for that school is theyear after the occupation. For example, if UPP occupied a favela in 2010, I consider the firsttreated exam wave to be 2011.The primary outcomes of interest are the test scores for Math and Reading. To interpret theestimates below, I standardized the test scores by the topic of the exam (Math or Reading),the year of the exam, and the student\u2019s grade (5th or 9th grade), using only treated or controlschools.I exploit the staggered introduction of the program to estimate the impacts of the PacificationPolice Units on test scores. The identifying assumption is that educational outcomes intreated places would have followed the same common trend as never-treated and not-yet-treated units if these treated units had not been treated. The empirical specification is:Yisjt = \u03bbs + \u03b4t + \u03b2Disjt + \u03d5\u2032Xisjt + \u03f5isjt (2.3)28I also use a 250m-buffer as a robustness exercise.29I test alternative definitions for treatment in the robustness section.18where i denotes the student and t the year (wave) when the student takes the standardizedtest; \u03bbs and \u03b4t are the school and wave of exam fixed effect, respectively. Disjt is a dummythat turns one for schools in treated favelas j and waves of the standardized test after theyear of the beginning of the UPP\u2019s occupation in favela j; Xisjt are students\u2019 and schools\u2019characteristics and \u03f5isjt is the error term. In this specification, \u03b2 is the parameter of interest,and I test the hypothesis that \u03b2 \u0338= 0. The standard error \u03f5isjt is robust to correlations withinthe same favela, j; therefore, they are clustered at the favela level.Some of the educational outcomes are available only at the school level. For these cases, Irun the regressions at the school level, controlling for school and time fixed effects, weightingby the number of students who take the exam or are enrolled at the school (in the SchoolCensuses data, for example), and clustering the standard errors at the favela level.I also estimate a Dynamic Difference-in-Differences specification:Yisjt = \u03bbs + \u03b4t +\u22122\u2211\u03c4=\u22124\u03b3\u03c4Disj\u03c4 +3\u2211\u03c4=0\u03b2\u03c4Disj\u03c4 + \u03d5\u2032Xisjt + \u03f5isjt (2.4)where, Disj\u03c4 is dummy that turns one if t = T\u2217isj+\u03c4 and T\u2217isj is the first wave of the exam afterthe UPP started in favela j. The omitted category is the exam wave before the beginning oftreatment.The UPP program achieved better results in early treated from 2008 to 2010 Magaloniet al. (2018); Ribeiro and Vilarouca (2018). Thus, there are important concerns of treatmentheterogeneity and possible biases that I can cause to TWFE estimation in this setting. Thus,I calculate the program\u2019s impact using the Borusyak et al. (2022) imputation estimator. Thisschool sample size is large enough that I can estimate the preferred estimator in the dynamicspecification. I also show the results are robust to using other estimators that deal withtreatment heterogeneity issues such as De Chaisemartin and d\u2019Haultfoeuille (2020), Callawayand Sant\u2019Anna (2021) and Sun and Abraham (2021).There are two key weaknesses of this data. The data does not have unique individual iden-tifiers, so I cannot match students over exam waves. Thus, the sample is a repeated cross-section of students30. Moreover, the data is not identified, and I cannot link it to otheradministrative datasets.30I accommodate the repeated cross-section nature of the data in the estimation strategy proposed byBorusyak et al. (2022), by analyzing the potential outcomes model: E[Yi(s)t(0)] = \u03bb(s)i + \u03b4t, where s standsfor the school attended by individual i in period t. The main difference from panel data estimation is thatthe fixed effect is at the school level, \u03b1(s)i.192.3.3 Medium-run outcomesEnrollment records I analyze identified administrative enrollment records from Rio\u2019s Mu-nicipal Secretary of Education. The data encompass the universe of students enrolled inmunicipal public schools (from pre-school to 9th grade) from 1997 to 2014. I observe in-formation about the students\u2019 and parents\u2019 names and dates of birth, which allows me tocreate a unique identifier and link this data with other administrative data. There is alsoinformation about students\u2019 socioeconomic characteristics such as age, gender, race, parentaleducation, if the students or the responsible receive cash transfers, the parents\u2019 occupation,if the student attended pre-school, and if the students live with their parents. There were ap-proximately 2.2 million students that passed through the Municipal School System between1997 and 2014.Moreover, I observe the history of students\u2019 moves in the Municipal Schooling System. Itis an unbalanced panel data at student and academic year levels in which any change instudents\u2019 status is recorded in the data. For example, suppose a student changes classrooms,goes to another municipal or private school, drops out, or enrolls in the same school for a newacademic year. In that case, the data records the movement as a new observation. From thisdata, I construct the information that contains unique entries at the student x academic yearx school levels and, thus, show the school attended by the student in each academic year.I discuss how I construct the data in Appendix A.2. For now, I exploit the cross-sectionalvariable of students enrolled in 2008 to define students in treated or control schools31.RAIS \u2013 Brazilian Matched Employer-Employee The RAIS data captures the universeof formal labor market relationships in a year. This data is organized by the BrazilianMinistry of Labor from mandatory forms filled by firms that operate in the formal labormarket (Dix-Carneiro, 2014). I have access to RAIS for the State of Rio de Janeiro in 2018.There are more than 4.7 million identified workers in the data. The data also have additionalinformation about occupation, wage, working hours, and job length. For now, I am onlyinterested in the extensive margin of formal labor market relationships, i.e., the presence inthe formal labor market; I use only the name and date of birth of individuals with formaljobs.Incarceration I use confidential administrative data from Rio de Janeiro\u2019s District Attorneywith the universe of individuals incarcerated between 2018 and 2020 in the State of Rio deJaneiro. There are almost 200k citizens that have passed through Rio\u2019s Prison System duringthese years. The data contain identified information for inmates\u2019 names and dates of birth.31I will expand the analysis to incorporate the time-series dimension of the panel data in later research.Then, I would be able to analyze how the UPP program affects the changes in schools, grade failure, anddropouts in treated students relative to students in the control schools.20Also, other variables are related to the felony, such as the crime committed or prison length.However, there are many missing observations, and they are not consistently filled in. Then,as the formal labor market data, I consider only the extensive margin of being incarcerated.SampleFor the linkage among the different administrative datasets, I use students\u2019 names and datesof birth and apply the algorithm described in Appendix A.1. In a nutshell, I block theindividuals using the first letter of their names and year of birth, calculate the Jaro-Winklerdistance for students\u2019 names and conservatively define that two names are a match if theJaro-Winkler distance is above 0.95 and the dates of birth are the same.This linkage strategy aims to reduce the likelihood of a false positive while accepting a higherprobability false negative. That is, I define as a match only individuals who have highlysimilar names32 and were born on the same date. So, I expect the number of matches I findto be smaller than the actual number of matches. The primary assumption for estimatingtreatment effects is that the true positive rate stays relatively constant over time and acrosstreated and untreated places. If this is the case, the linkage procedure would only introducemeasurement error in the dependent variable, reducing the power of the statistical tests Iperform.The medium-run empirical strategy aims to estimate the effects of studying in a treated placeon outcomes later in adulthood compared to students who attended a school in an untreatedfavela. So, I use the linked administrative data to test if students who attended a treatedschool have a higher likelihood of being in the formal labor market or are less likely to beincarcerated later in their lives compared to students who were enrolled in control schools.I keep the same schools as the short-run sample to achieve this objective. To avoid concernsrelated to movement across schools caused by decreasing violence levels in treated favelas,I employ an intent-to-treat empirical strategy similar to Hoynes et al. (2016). I use pre-enrollment information; thus, I define a student as treated if she was enrolled in a treatedschool before the beginning of the program in 2008. Likewise, I represent the set of individualsin the control group as students in a control school in 2008.I analyze the cohorts born between 1992 and 2000. I chose this range to capture individualswith ages compatible with being in primary school at the beginning of treatment and oldenough to be in the formal labor market or incarcerated in 2018. This implies that at thebeginning of treatment at the end of 2008, the student has at least eight years old and she is32Names in Brazil have, on average, two or more family names, which reduces the chances of observingprevalent small names such as \u2018John Smith\u2019. In the administrative enrollment records, for example, 76% ofunique names have three surnames; 33% have four surnames.21at or above 3rd grade. Thus, disaggregated cohort level analysis is bounded from below atage 8 and grade 3.With these restrictions, 61,635 students appeared in treated or untreated schools after thebeginning of the UPP program: 23,982 attended one of the 60 treated schools, and 37,653attended one of the 78 untreated schools. With the linkage algorithm, I find that 17,965(29.15%)33 individuals are present in the formal labor market, and 1,825 (2.96%)are incar-cerated.Empirical specificationI exploit the variation induced by the staggered introduction of the program and by year ofbirth to estimate the impact of the exposure to the policy on the probability of being in theformal labor market or incarcerated in early adulthood. The identifying assumption is thatthe timing of individual exposure is plausibly exogenous after controlling cohort and schoolfixed effects.There are some reasons to a priori expect that the program may positively impact youngerindividuals more. There is an extensive literature of place-based effects (Sviatschi, 2022;Chetty et al., 2016; Hoynes et al., 2016) that show that younger citizens are more affectedby these policies and, also, Willadino et al. (2018) show that most of the teenagers involvedwith drug trafficking entered the business with 13 and 15 years old. So, policies that couldchange opportunities in life may have higher impacts later. I employ two main empiricalspecifications to shed light on the timing of exposure to treatment.First, I analyze how treatment impacts vary by the age that the individual was when treat-ment commenced in her school. I employ a cohort-place fixed effects strategy (Bailey et al.,2021; Hoynes et al., 2016; Duflo, 2001), in which the individual is treated at age \u03c4 if she was\u03c4 years old when treatment started. The empirical specification for this exercise is:Yibsj = \u03b4s + \u03bbb +15\u2211\u03c4=8\u03b4\u03c41{s is treated}1{age = \u03c4}+ . . .+19+\u2211\u03c4=17\u03b2\u03c41{s is treated}1{age = \u03c4}+ \u0393\u2032Xibsj + \u03f5ibsj(2.5)where, i indexes the individual, b cohort (year of birth), s is the school individual attendedin 2008, and j the favela where the school is located; age refers to the individual\u2019s age when33Reassuringly, in a survey with more than 2,000 residents at favelas treated by the UPP program,Musumeci (2016) finds that 26.6% of respondents were in the formal labor market in 2016, a statistic that issimilar to the one I find.22treatment started in that favela, \u03b4s is school fixed effect and \u03bbb is a cohort fixed effect. Thestandard errors are clustered at the favela level. The coefficients of interest are {\u03b4\u03c4 , \u03b2\u03c4}\u03c4 thatshows the effects of being exposed to treatment at age \u03c4 relative to the omitted category of16 years old.The parameters of interest ({\u03b4\u03c4 , \u03b2\u03c4}\u03c4 ) are identified from variation within schools (or favelas)across birth cohorts. Figure A.4 shows the variation in treatment age when treatment startedin the individual\u2019s favela. In these figures, the timeline (horizontal dimension) displays theyear of birth, and the vertical dimension shows the year of treatment. So, for example, if aperson were born in 1998 and lives in a favela treated in 2010, this person would be in thefourth vertical line and under 1998 in the horizontal dimension. The red numbers refer to theage individual was when treatment began. The never-treated units allow for the estimationof unrestricted cohort fixed effects.The second estimation follows the empirical strategy discussed in Hoynes et al. (2016)34.Similar to their paper, the UPP program, as a place-based policy, \u2018does not turn off\u2019. Allindividuals who live in a treated favela are \u2018eligible\u2019 to receive the treatment. Thus, com-parisons to estimate treatment effects should be made \u2018from above\u2019, i.e., relative to other(possibly) treated categories.Given that individuals enter the drug trafficking business at ages 13 to 15 on average andthat most of them drop out of school in Middle school (Willadino et al., 2018), I estimate thepredicted number of years a student is exposed to treatment while in primary school relativeto be treated after this period. The testable conjecture is that individuals more exposed totreatment before the period in which they make critical decisions in their lives will be moreimpacted by the UPP program.To calculate the predicted years of exposure to treatment while in primary school, I em-ploy the institutional fact that students enter primary school in grade 1 at age 6 and thatprimary school lengths for nine years. So, the predicted grade a student is when treat-ment arrives is defined by: Predicted grade = Treatment year\u2212 (Year of birth + 6) + 1, and(Calendar) years of exposure to primary = 9\u2212 Predicted grade. For example, an individualborn in 1998 enters primary school in 2004 at age 6. Suppose that she studies in a place thatwas treated in 2010. Then, she would be predicted to be in grade 7 when treatment started,and, therefore, she would be exposed to treatment for two years while in primary school. Igraphically show this example in Figure A.5.34Hoynes et al. (2016) study the effects of being exposed to Food Stamps during childhood on lateroutcomes in life.23The empirical specification is:Yibsj = \u03b4s + \u03bbb + \u03b2EUPPbsj + \u0393\u2032Xibsj + \u03f5ibsj (2.6)where, i, s, j and b index for individual, school, and favela and, the cohort of birth, \u03b4s is aschool FE, \u03bbb is a cohort of birth FE, EUPPsjb is the number of (calendar) years an individualwas treated while in primary school, Xisjb captures individual controls and standard errorsare clustered at favela level.The parameter of interest is \u03b2, which captures the marginal impact of an additional treatmentwhile in primary school. The parameter is identified from the variation of age and grade fromdifferent cohorts in the same school when the UPP policy commenced in that locality.In these estimations, the exposure to UPP treatment while in primary school or the agethe individual was when treatment started already captures the intensity of treatment. Theestimates pick any treatment heterogeneity caused by early treated units. Thus, I run TwoWay Fixed Effect regressions for the medium-run specifications.2.4 Results2.4.1 ViolenceTable 2.1 presents the reduced-form estimation for the UPP treatment. The main indepen-dent variable is a dummy that turns one for semesters after the beginning of the treatmentin a favela. The results show that UPP significantly reduced exposure to violence in treatedfavelas. The program cut Total homicides, police killings, and other homicides rates by morethan 20%. Significantly, the police killings rate in treated favelas reduces by 38% (p < 0.05).Figure 2.1 shows the dynamic impacts of the Pacification program on violence reduction intreated places. The policy induces a level-shift decrease in total homicides until six semestersafter the beginning of the treatment. Figure A.2 displays the effects of police killings and otherhomicides committed by citizens over time. The pre-trend coefficients suggest no differentialpre-treatment trends between treated and not-yet-treated favelas for all the crime indicators.This can be seen as evidence that the UPP did not target favelas hit by contemporaneousshocks in its criminal market.I discuss the robustness of the results in table A.2. First, I use a negative binomial specifica-tion to deal with possible concerns about the right skewness of the dependent variable. Theincidence ratio results suggest that treatment reduces total homicide levels by 40% (p < 0.01)and police killings by more than 60% (p < 0.01). The results do not indicate a statistically24significant reduction in other homicides.The results indicate that the reduction in total homicides was primarily driven by the decreasein police killings in treated favelas, which is consistent with the change in the police modusoperandi induced by the UPP policy (Lessing, 2017). The police replaced the former strategyof intermittent police raids inside the favelas that increased the likelihood of a crossfire withpermanent community-oriented policing that dislodged drug traffickers from the favelas. Thenew policing strategy developed by the UPP decreased the clashes between the police andcriminals and reduced the number of deaths caused by the police.In the second chapter of the thesis, I provide a more detailed discussion about the robustnessof these results using never-treated units. I use coarser data at the police station levelto construct violence indicators for police stations with a large untreated favelas in theircatchment areas. With this data, I can address the spatial spillover concerns that may affectthe identification of the effects. I show in the next chapter that the violence indicators inuntreated areas also present a downward trend after the treatment. Given the relevance andmagnitude of the UPP policy, it is unlikely that a confounder drives these results. Thus,relevant to this paper, there is no evidence of crime displacement to untreated favelas.2.4.2 School outcomesTable 2.2 presents the main results for the impact of UPP treatment on Math and Readingtest scores. The Pacification program in the preferred specification35 causes an increase of0.09 standard deviation for the Math exam and 0.07 standard deviation for the Reading. Thepoint estimates are robust to the introduction of students and school covariates. Notably, thepoint estimates for level shift violence reduction in Rio\u2019s favelas are almost two times largerin absolute value than the impact of episodes of violence on school outcomes. Monteiro andRocha (2017) estimate that drug battles in Rio reduce standardized test scores by 0.05sd for5th graders in the Math exam. At the same time, I find an increase of 0.1sd in Math testscores for Elementary students when homicides and police killings consistently decrease inthe favelas.I show how these effects differ by subsamples in panel A of table 2.10: boys perform better35The preferred specification is column (1), in which I do not control for any covariates. There are twomain reasons: (i) treated and untreated favelas and schools in treated or untreated places are already similarin almost all of the covariates before the beginning of the program, as shown in tables A.3 and A.4, and (ii)a priori, the composition of students or teachers and, investments at school level can change due to the UPPprogram. For example, better students may move to treated schools after the pacification, or schools mightreceive more investment following the UPP entry. In this plausible scenario, composition variables wouldbe mediators of the treatment on the effects, and the estimates would suffer from overcontrol bias (Cinelliet al., 2021). Given that UPP is a bundled treatment, I prefer to estimate its total effect on school outcomes,focusing on column (1), and then estimate the impacts of the policy on mediators in separate regressions.25than girls in both exams, and there is suggestive evidence that white boys respond morepositively to the UPP treatment than non-white boys for both Math and Reading tests.Since boys are more exposed to drug-related violence in the favelas (Barcellos and Zaluar,2014), the differential gender effects of the policy are consistent with a more intense reductionin exposure to lethal violence and the presence of drug traffickers (Zaluar, 2011) in treatedareas.To explore the suggestive differences between white and non-white boys, I test in table A.5how these subgroups vary in several socioeconomic characteristics: white boys perform betteron math and reading exams on average, they live more with both parents, display a lowerlikelihood of having failed a grade or having dropped out before, and work less outside thehome than non-white students. Besides, there is evidence that white students are wealthier(measured by income proxies). Monteiro and Rocha (2017) indicate that high-performingstudents are more affected by episodes of violence in their neighborhoods. I show that myresults are consistent with the idea that the same type of students \u2013 high(er)-performingindividuals \u2013 benefit more from the decrease in violence caused by the UPP program.Figure 2.4 exhibits how the consequences of UPP treatment change by the schooling grade(5th or 9th grade). The effects for the 5th grade appear in the first wave after the beginningof the treatment and persist until cohorts that take the exam up to three waves after thetreatment. In contrast, the impacts for students in the 9th grade are contemporaneous(Math) and last for one cohort after the treatment. Although I cannot track individuals overtime, students who take the exam in the 5th grade should retake the exam in the 9th gradefour years (two waves) after the first test. For example, students who took the 5th-gradeexam in a school treated in 2009 would retake the exam in 9th grade four years later. Byanalyzing the dynamic effects for 9th grade, I observed that treated places don\u2019t presentdifferential results for exams that happen two or more waves after the treatment. Studentswho show a positive treatment effect in the 5th grade seem to have a null impact four yearslater, in the 9th grade. I consider this empirical fact as suggestive evidence that the effect ofUPP on school outcomes is dissipating over time.One possible reason for these dissipating effects over time is that the constant interactionwith the police may impose more psychological costs for teenagers in Middle School. Ang(2021) suggests that even low-risk contact with the police can be detrimental to adolescents.Since the UPP police introduced permanent settlements in treated favelas and adopted astop-and-frisk strategy that targeted teenagers more (Willadino et al., 2018), these negativeeffects of police behavior may offset the positive consequences of a less violent environment.Despite the positive effect on test scores, I do not find impacts of the UPP treatment on othereducational outcomes at the school level, such as dropout rates or age-grade distortion. Table262.6 exhibits these results. These findings suggest that better performance at standardizedtest scores does not translate into changes in the extensive margin decision of staying or not atschool, on average. Monteiro and Rocha (2017) find that drug battles nearby schools do notimpact the dropout rate in these schools. Taken together, these results suggest that dropoutis relatively inelastic to exposure to violence in Rio\u2019s favelas. A possible explanation for thisinelastic behavior is that primary schooling (grades 1 to 9) is mandatory in Brazil (Bartholoand Costa, 2016) and school attendance is a criterion for social benefits such as conditionalcash transfers (Neri and Camillo Osorio, 2019), which increases to legal and financial costsof dropping out of primary school.ChannelsI explore plausible channels that may explain the increase in standardized test scores afterthe UPP program below:School Routine Table 2.8 describes school problems reported by Principals. School routineis less interrupted after the UPP program, in line with Ribeiro (2020) that shows that UPPreduces the number of days in which a school was closed due to gunfights in its surroundingscompared to schools located in other untreated favelas. Besides, principals report that stu-dents\u2019 absenteeism decreases after the treatment. Thus, students are less disrupted in theirschool routine and, therefore, more present in schools after the slums are pacified.Expectations and violence within the school I exploit the fact that there are questions aboutfuture students\u2019 expectations and exposure to violence in the Teachers Survey from ProvaBrasil. Teachers\u2019 beliefs about future high school graduation for children in both elementaryand middle school increased by more than 16%. However, the UPP program did not changethe expectation of college attendance. That is, teachers believe that the program can helpstudents graduate more in high school, but the effects of the policy on school would not alterthe likelihood of college enrollment. Exposure to violence within the school also decreases.Teachers report that aggression from teenagers in middle school reduces by more than 17%and aggression among teenagers by 30%. These results suggest that teachers had a posi-tive expectation about the effect of the UPP policy on learning and the treatment reducedteenagers\u2019 violent behavior within school.Students\u2019 composition Another possibility is that different types of students move to treatareas after the beginning of the treatment. The composition of students can shed light onwhy school outcomes improved in treated places. Conceptually, the composition of studentsmay improve in areas with UPP due to the enrollment of better students who were studyingoutside the favela, or it may deteriorate because good students previously studying in favelascould exploit educational opportunities outside the favela.27I investigate these hypotheses in table 2.4. Indeed, there is an increase in students enrolledin treated favelas. However, there is no change in observable variables that correlate withstudents\u2019 performance. Thus, there is no evidence of changes in student composition intreated favelas caused by the UPP policy.Teachers\u2019 composition and Infrastructure Given that the UPP policy may have induced otherinvestments in treated favelas and that these areas are less violent, school and teacher qualitycould have increased in treated places. I show in table 2.3 that these results are not drivenby changes in school infrastructure or the quality of teachers36.Household income I show that the school results are robust to the inclusion of proxies tohousehold income in table 2.5. Students in the treated sample could have higher householdincome due to the treatment because the UPP policy may have increased labor opportunitiesfor their parents. Nevertheless, the estimates suggest that the effects of the UPP programon test scores are not driven primarily by changes in household income.RobustnessI show in table A.6 that students in early-treated favelas (2009-2011) perform better in ProvaBrasil for both Math and Reading exams. Due to the plausibility of treatment heterogeneity,I perform a robustness exercise with other recent difference-in-difference estimators thataddress the concerns this sort of heterogeneity raises. Figure 2.2 exhibits the estimation ofthe leads and lags coefficients for the periods before and after treatment, respectively, forthese estimators. I also include the standard TWFE estimator for comparison reasons. Thepoint estimates stay at the same level, around 0.15 standard deviation for Math and 0.1 forReading, after the first treated wave of the exam. Then, the results are robust to the choiceof different recently designed estimators that deal with issues that may arise with treatmentheterogeneity.Since Prova Brasil, the national standardized exam, happens every two years, some schoolsmay be treated in the same wave of the exam, but one school receives the treatment beforethe other. I provide evidence that the UPP program impacts more schools treated for a moreextended period. I show in Table A.7 that the results are robust and, indeed, greater thanan alternative definition of the treatment: schools are treated in a specific wave if the UPPstarted in their favelas at least six months before the exam day.Table A.8 provides robustness estimation for a different buffer around favelas. A school istreated if it is placed up to 250 meters from treated favelas. Analogously, I define that a schoolis in the control group if it locates up to 250 meters from an untreated favela. Since the UPP36This result is in line with Ribeiro (2013) which shows that UPP did not have an impact on the flow ofteachers from or to treated schools.28policy targets favelas ruled by drug traffickers and the criminal governance of these actors arerestricted to the favelas they operate, the UPP effects should decrease with distance. That iswhat happens when I increase the buffer. The UPP program still positively impacts treatedschools, but the point estimate is almost 0.02sd lower than the main specification.2.4.3 Medium-run outcomesFigure 2.3 presents the point estimates for each age the individual was when treatment startedin her school\/favela. There is a concave relationship between the incarceration outcomes: theyounger the individual is, the lower the likelihood he ends up in prison in his early adulthood.These effects start to be statistically zero at a 90% confidence interval when the individualis aged 14 or more. Concerning the presence in the formal labor market in 2018, the UPPprogram did not alter the probability of having a formal job later in treated individualsregardless the how old the individual was when treatment commenced.In table 2.7, I provide a similar piece of evidence but with a reduced-form estimation. Ianalyze the predicted years of exposure to treatment while in primary school37. I find thatan additional year of exposure to treatment in primary school reduces the probability of beingincarcerated by 0.006 percentage points (p-value < 0.01), which represents a 20% decreaserelative to the sample mean (0.0296). As expected from the results above, there are noimpacts of the UPP program on the probability of being in the formal labor market.The UPP program, thus, could reduce incarceration for treated individuals who stay undertreatment in primary school for five years or more. To glimpse the effects, I perform aback-of-the-envelope calculation to estimate the amount saved by the program in the costs ofhaving a person incarcerated. There were 9,842 individuals in treated areas in 2008 eligiblefor this intensity of treatment. On average, without the treatment, 295 of these individuals(9, 842\u22170.0296) would be in jail later in life. Relying on estimates of the yearly cost ofincarceration of 4320 US dollars 38, in a back-of-the-envelope calculation, the UPP programcould save more than 1.2 million US dollars a year. These estimates are a lower bound sincethey do not contain the social cost of crime or defensive investments.Although the human capital gains related to the UPP program could not increase participa-tion in the formal labor market, the results indicate that the treatment strongly reduced theincarceration of individuals treated at a younger age. In terms of the formal labor marketresults, there are some alternatives. First, if the UPP treatment deferentially increases theprobability of college enrollment, treated individuals could appear later in the formal labor37This analysis is similar because years of exposure in primary school strongly correlate with the age whentreatment started.38https:\/\/www.cnnbrasil.com.br\/nacional\/custo-medio-de-pessoa-presa-no-brasil-e-de-r-18-mil-por-mes-aponta-cnj\/. Accessed in November 2022.29market. Although there is suggestive evidence that the learning gains dissipate over time,I intend to investigate this possibility in future research. Second, the UPP program mayhave increased cognitive abilities in the short run but not other abilities necessary to theformal labor market. This could also explain the null results for the formal labor marketoutcomes. For the incarceration outcomes, younger treated individuals are less exposed toviolence and the presence of drug traffickers (Willadino et al., 2018), suggesting that theeffects can be driven both by a reduced burden of violence and by fewer opportunities in thecriminal market.2.5 InterpretationI have shown that the UPP policy caused (at least) short-term learning gains and a con-siderable reduction in the likelihood of being incarcerated later in life but no effects on theprobability of having a job in the formal sector. Given that the UPP program focused onspecific neighborhoods (place-based policy), many elements of these places\u2019 environments canexplain the results above. Children and teenagers in treated areas (the focus of this paper)grow up in different socioeconomic contexts and social networks than individuals in controlfavelas, which could justify these outcomes.I present evidence that some of these environmental channels did not occur. Concerning thetest scores results, there is no evidence that neither peer cohorts and student compositionwithin schools nor school infrastructure and teachers\u2019 quality are changing (tables 2.3, 2.4and 2.5). Moreover, parental income does not explain these results. I do find, however, alarge decrease of violence in treated places (figure 2.1) which translates to teachers observingless violence within the school and to principals reporting fewer disruptions in school routineand students absenteeism (tables 2.8 and 2.9). Taken together, these findings are consistentwith effects being driven by a reduction in student cognitive burden from violence and alsoconsistent with a reduction in learning disruptions at school. Given the existing data, it isdifficult to differentiate between these explanations.What can cause the medium-run results, and how these results possibly link to the learninggains in the short run? I partly address this question by performing heterogeneous analysisfor sample subgroups. I show these comparisons in table 2.10. The subgroup analysis suggestsno simple linear relationship exists between test score gains and later outcomes in life. Iftest scores proxy improvements in cognitive skills, boys should be expected to perform betterin the formal labor market later in life, which does not seem to be the case. In fact, someevidence suggests that any human capital effects may dissipate over time (figure 2.4).However, I observe that boys are differently more impacted by the policy. They display abigger improvement in learning in the short run and a sizeable reduction in the likelihood30of incarceration later in their lives (results for white and non-white boys in Panel B of table2.10). Taken together, the evidence on medium-run mechanisms is most consistent with theseeffects being driven by a change in drug-related career opportunities for young men in favelas.The findings would also be consistent with incarceration effects being driven by changes incognitive function associated with a less violent childhood. However, data constraints limitmy ability to differentiate between these outcomes.2.6 Conclusion and Policy TakeawaysIn this paper, I analyze the short- and medium-run consequences of a place-based publicpolicy that reduced criminal governance and exposure to violence in treated places. I exploitthe fact that UPP did not induce criminal migration to control neighborhoods to estimateits impact on school outcomes, formal labor market presence, and incarceration probability.I find that the policy caused an increase of more than 0.08 sd in standardized test scores,a significant decrease in the likelihood of being incarcerated, and no impact on presence inthe formal labor market. I provide evidence that this place-based policy may be a plausibleinstrument to improve life prospects at the neighborhood level.The results of this paper show that the UPP program is an alternative to the status quopolicing strategy of intermittent police raids that display high human and financial costs(Lessing, 2017). In these raids, police agents perform occasional tactical operations in thefavelas to apprehend drugs or arrest drug traffickers. When these operations happen, itis frequent that citizens will be caught in the crossfire, and several public services will bedisrupted. UPP policy changed this logic of police intervention, reduced homicides, andintroduced a permanent community policing strategy in these favelas. Although it can becostly to implement this strategy, the results suggest it pays off.There are some caveats and directions to expand this research. First, I cannot directly linkstudents\u2019 grades in standardized test scores to medium-run outcomes. Thus, I do not observean individual trajectory in life that passes through education until early adulthood. Instead, Iexploit treatment heterogeneity to shed light on different groups that benefit from the policy.In future research, I intend to incorporate information about high-school attendance andgrades, college admissions, and teenagers in contact with the Juvenile Justice system. Thisinformation would allow me to provide a complete view of schooling outcomes and exploreother mechanisms related to criminal involvement.Second, in the medium-run results, I define a treated person as she attends a treated school.Although most of the students indeed live within a 15-minute walking distance of schools,I could capture in this definition students who live outside of a treated favela as treatedindividuals. Since criminal governance is more prevalent within favelas\u2019 boundaries and31UPP is a place-based policy, I expect that exposure to treatment decreases with distanceto a treated area. So, there may be a downward bias in the medium-run estimates. Futureresearch needs to disentangle if these results are driven by students who live or attend a schoolin the treated areas but live outside the treated areas. After geocoding all the addresses inthe administrative enrollment data, I will be able to shed light on this issue.Third, an exciting extension is understanding how the drug trafficking criminal workforcechanged after the UPP and then discussing how this change may alter peer effects within theclassroom. After organizing the Juvenile Justice System data, I will link these individualswith administrative enrollment data, and I will be able to test some of the mechanisms Idiscuss in this paper.Finally, the UPP program creates a general equilibrium shock in Rio\u2019s metropolitan regionthat changes this criminal market. Although I do not observe crime displacement to untreatedfavelas in the city of Rio de Janeiro, other areas in the metropolitan region might have sufferedfrom crime migration. Therefore, future research must incorporate these externalities andcosts while evaluating UPP\u2019s impact.32Figures and TablesTable 2.1: Effects of the UPP treatment on violence ratesTotal homicides Police killings Other homicidesPanel A: Borusyak et al. (2022)Treat -0.64 -0.68 -0.37(0.17)*** (0.32)** (0.17)**Obs. 518 518 518Panel B: TWFE-0.60 -0.75 -0.26(0.20)*** (0.28)** (0.15)*Obs. 740 740 740Semester FE Yes Yes YesFavela FE Yes Yes YesMean before treat. 2.84 1.80 1.99Notes: Table shows the results for regression equation (1) using Borusyak et al. (2022) imputationand TWFE estimators. The dependent variables are inverse hyperbolic sine of semesters\u2019 rates per100,000 citizens. Both regressions control for Semester and UPP (favela) fixed effects, have standarderrors clustered at the favela level, and use population as analytical weights. Total homicides is de-fined by the sum of police killings and other homicides. Borusyak et al. (2022) estimator uses fewerobservations because it drops observations in which all units are treated. * significant at 10%; ** sig-nificant at 5%; *** significant at 1%.33Figure 2.1: Dynamic effects of UPP treatment on total homicides rates(a) Total homicidesNotes: Figure shows the estimates for equation (2) using the TWFE estimator. I do not use Borusyaket al. (2022) estimator in these figures because the minimum effective number of observations is below theminimum recommended by the authors and the estimates may be unreliable. The dependent variable is theinverse hyperbolic sine of semesters\u2019 rates per 100,000 citizens. I control for Semester and Favela fixed effects,cluster standard errors clustered at the favela level, and use population as analytical weights. Confidenceintervals are at 95%.34Table 2.2: Effects of the UPP treatment on standardized testscores(1) (2) (3) (4)Panel A: MathTreat 0.095 0.099 0.098 0.085(0.042)** (0.038)*** (0.041)** (0.037)**Panel B: LanguageTreat 0.065 0.070 0.067 0.058(0.039)* (0.036)** (0.038)* (0.035)*Obs. 54,879 54,879 54,879 54,879Year FE Yes Yes Yes YesSchool FE Yes Yes Yes YesControls No Students Schools AllNotes: Table shows the results of regression for Borusyak et al.(2022) imputation estimator. Students\u2019 controls include students\u2019characteristics such as gender, race, mother\u2019s education, if lives withthe mother, if the student has failed a grade or dropped out of schoolbefore and if works outside home. Schools\u2019 controls are the numberof enrollments, the number of employees, the number of computersand an infrastructure index composed by the presence of a computerlab, science lab, library and sports court. Standard errors are clus-tered at favela level and dependent variable is standardized for eachyear and grade. * significant at 10%; ** significant at 5%; *** signif-icant at 1%.35Table 2.3: Effects of the UPP treatment on school infrastructure and teachers\u2019 compositionInfra-structure Teachers\u2019 Composition# Employees # Classrooms # Computers Infra index # Teachers Fem. Non-white College degree Graduate degree AgeTreat 1.106 0.308 -0.094 -0.029 1.140 -0.001 -0.029 0.032 0.014 0.025(2.001) (0.215) (1.650) (0.103) (0.749) (0.015) (0.032) (0.023) (0.014) (0.394)Obs. 690 690 690 690 690 690 665 690 689 690Year FE Yes Yes Yes Yes Yes Yes Yes Yes Yes YesSchool Yes Yes Yes Yes Yes Yes Yes Yes Yes YesMean Dep. Var 50.01 13.94 15.40 2.109 29.10 0.803 0.404 0.696 0.287 41.98Notes: Table shows the results of regression for Borusyak et al. (2022) imputation estimator. Outcomes come from School Census. The sample is re-stricted to years 2007, 2009, 20011, 2013 and 2015 in order to be relatable to the main regressions. Columns that refer to Infra-structure show the numberof employees and classrooms at school in a year and a Infra Index that is the sum of Computer Lab, Science Lab, Sports Court and Library. Columns\u201c# Teachers\u201d to \u201cAge\u201d are at school level and are weighted by the number of teachers at the school. Columns reflect the number of teachers at schoolin a year, the share of female, non-white, with a college degree, if any graduate degree (specialization, master or PhD), and their mean age, respectively.These variables reflect schools\u2019 and teachers\u2019 characteristics that may influence the time a student spends at school and the quality of learning a studentreceives. Standard errors are clusters at favela level. * significant at 10%; ** significant at 5%; *** significant at 1%.36Table 2.4: Effects of the UPP treatment on student composition(1) (2) (3) (4) (5) (6) (7) (8) (9)# Enrollment Fem. Non-white Lives parents Mother\u2019s lit. Mother above Primary Educ. Ever Failed Ever Truant Inc. indexTreat 13.399 -0.015 0.010 0.000 -0.002 -0.013 0.023 0.011 -0.049(3.634)*** (0.011) (0.006)* (0.010) (0.007) (0.013) (0.017) (0.009) (0.038)Obs. 690 54,879 54,879 54,257 54,879 34,182 54,879 54,879 50,538Year FE Yes Yes Yes Yes Yes Yes Yes Yes YesSchool Yes Yes Yes Yes Yes Yes Yes Yes YesMean Dep. Var. 83.43 0.499 0.758 0.489 0.944 0.587 0.291 0.0848 0.003Notes: Table shows the results of regression for Borusyak et al. (2022) imputation estimator. Outcomes come from a survey answered by students who take the national exam Prova Brasil. Students\u2019characteristics were regressed on treatment variables. The dependent variables are: female, non-white, if the student lives with both parents, if the mother is literate, if the mother has education abovePrimary education, if the student has ever failed a grade before, or if the student has ever been truant from a grade before. I construct an income index for column (9) based on the variables discussedabove and the variable if the student doesn\u2019t work outside the home. I apply a principal component analysis by each wave (year) of exam and predict its results. Standard errors are clustered at favelalevel. * significant at 10%; ** significant at 5%; *** significant at 1%.37Table 2.5: Robustness for the effects of UPP treatment on stan-dardized test scores: proxies for students\u2019 household in-come(1) (2) (3) (4)Panel A: MathTreat 0.095 0.085 0.107 0.105(0.042)** (0.037)** (0.038)*** (0.039)***Panel B: ReadingTreat 0.065 0.058 0.077 0.075(0.039)* (0.035)* (0.034)** (0.036)**Obs. 54,879 54,879 50,538 50,538Year FE Yes Yes Yes YesSchool FE Yes Yes Yes YesStudents controls No Yes Yes YesSchools controls No Yes Yes YesIncome controls No No Yes Yes - IndexNotes: Table shows the results for DD imputation (Borusyak et al., 2022) regressionswith different proxies for income. First, I control for several variables that might indicatehigher income such as, if the student studied in a private school at some point in his orher life, the number of bathrooms, bedrooms, televisions at home, if there is a freezer,a laundry machining, car or computer at home and if a maid works in his or her house.Second, I construct an income index based on the variables discussed above and the vari-able if the student doesn\u2019t work outside home. I apply a principal component analysis byeach wave (year) of exam and predict its results. The other students\u2019 controls include stu-dents\u2019 characteristics such as gender, race, mother\u2019s education, if lives with the mother, ifthe student has failed a grade or dropped out of school before and if works outside home.Schools\u2019 controls are the number of enrollments, the number of employees, the number ofcomputers and an infrastructure index composed by the presence of a computer lab, sci-ence lab, library and sports court. In the first and second columns, I present the resultsfor the main specification: initially controlling only for year and school fixed effects and,then, for all covariates in the main specification; in the third column results, I control forall students and school controls, and I include variables that are the proxies for income;in the forth column, I control for all students\u2019 and schools\u2019 covariates and, I replace thevariables that are proxies for income to the income index I discuss above. Standard er-rors are clustered at favela level and dependent variable is standardized for each year andgrade. * significant at 10%; ** significant at 5%; *** significant at 1%.38Figure 2.2: Robustness for the effects of UPP treatment on standardized test scores:difference-in-differences estimators(a) Dynamic effects - Math(b) Dynamic effects - ReadingNotes: Figure shows the impact of UPPs on school outcomes by using different DD estimators, controlling for wave ofexam and school fixed effects. A priori, the composition of students or teachers and, investments at school level can change dueto the UPP program. For example, better students may move to treated schools after the pacification or schools might receivemore investment following the UPP entry. In this plausible scenario, composition variables would be mediators of the treatmenton the effects and the estimates would suffer from overcontrol bias (Cinelli et al., 2021). Given that UPP is a bundled treatment,I estimate its total effect on school outcomes in the regressions above. Confidence intervals are at 95% level.39Table 2.6: Effects of the UPP treatment on educational indicators(1) (2) (3) (4)Pass rate Fail rate Dropout rate Age-grade dist. rateTreat 0.23 -0.80 0.56 -0.10(0.61) (0.69) (0.47) (1.18)Observations 690 690 690 690Year FE Yes Yes Yes YesSchool Yes Yes Yes YesMean Dep. Var (%) 87.93 9.85 2.23 25.06Notes: Table shows the results of regression for Borusyak et al. (2022) imputation estimator. Outcomescome from annual School Census data. Columns (1) to (4) are weighted by the number of students en-rolled at the school. Dependent variables are the approval (pass rate), failed, drop out and age-gradedistortion rates for elementary and middle school. Age-grade distortion is defined by the number ofstudents who are more than two years behind the grade she should be. Standard errors are clusters atfavela level. * significant at 10%; ** significant at 5%; *** significant at 1%.40Figure 2.3: Medium-run effects of the UPP treatment by age when treatment startedin the school(a) Incarceration(b) Formal Labor marketNotes: The figure displays the estimates from equation (4). It shows that how the effects of UPP program vary dependingon the age the individual was when treatment started in her school. The dots represent the point estimates and the lines the 95%confidence interval.41Table 2.7: Medium-run results for UPP treatment: years of exposure to treatmentwhile in primary schoolIncarceration RAIS(1) (2)EUPP -0.006 -0.002(0.002)*** (0.005)Observations 61,635 61,635Year FE Yes YesSchool Yes YesControls Yes YesMean Dep. Var 0.0296 0.291Notes: Table shows the results for the empiricalspecification shown in equation 5. The dependentvariable is a dummy that turns one if the student ap-pears in the formal labor market (RAIS) or it is in-carcerated in 2018. Exposure to UPP is measuredby the predicted number of years a student stays inprimary school during the UPP program. Controlsinclude gender, race, mother education, father regis-tered, father deceased, lives with mother, enrolled inSocial Service. Standard errors are clustered at favelalevel. * significant at 10%; ** significant at 5%; ***significant at 1%.42Table 2.8: Effects of UPP treatment on school environmentDid the school suffer from Did the school suffer from lack Did the school suffer from Did the school suffer from Did the school suffer from Does the school regularly offer Does the school regularly offerdisruption of scholar activities this year? financial resources this year? teachers\u2019 absenteeism this year? students\u2019 absenteeism this year? teachers\u2019 turnover this year? sports classes in extracurricular activities? arts classes in extracurricular activities?Treat -0.43 -0.00 0.04 -0.10 0.05 0.03 0.04(0.09)*** (0.05) (0.05) (0.05)** (0.05) (0.06) (0.05)Obs. 666 664 667 668 667 670 670Year FE Yes Yes Yes Yes Yes Yes YesSchool Yes Yes Yes Yes Yes Yes YesMean Dep. Var 0.348 0.295 0.148 0.445 0.172 0.870 0.842Notes: Table shows the results of DD imputation (Borusyak et al., 2022) regressions for outcomes related to principals\u2019 perceptions about school problems. The answers come from the Principals\u2019 Surveys from Prova Brasil and indicate if problemhappened in that academic year. Standard errors are clustered at the favela level. * significant at 10%; ** significant at 5%; *** significant at 1%.43Table 2.9: Effects of UPP treatment on expectations and violence within schoolDo you believe that more than half of your students Do you believe that more than half of your students Did an event of verbal or physical aggression happen Did an event of verbal or physical aggression happenwill graduate from high school? will attend college? against teachers or employees this last year? against students this last year?Panel A: Elementary SchoolTreat 0.155 0.052 0.049 0.071(0.053)*** (0.057) (0.045) (0.046)Obs. 1,589 1,584 1,598 1,575Mean Dep. Var 0.735 0.268 0.638 0.680Panel B: Middle SchoolTreat 0.121 -0.089 -0.144 -0.241(0.071)* (0.056) (0.066)** (0.063)***Obs. 748 749 778 766Mean Dep. Var 0.731 0.119 0.842 0.805Year FE Y es Y es Y esSchool FE Y es Y es Y esNotes: Table shows the results of DD imputation (Borusyak et al., 2022) regressions for outcomes related to teachers\u2019 expectations of students and exposure to violence within school. Answers come from the Teachers\u2019 Survey from Prova Brasil.Standard errors are clustered at the favela level. * significant at 10%; ** significant at 5%; *** significant at 1%.44Table 2.10: Heterogeneity of the effects of UPP treatment on short- and medium-run outcomesGirls Boys White boys Non-white boysPanel A: Test ScoresMathTreat 0.06 0.13 0.20 0.10(0.04) (0.04)*** (0.06)*** (0.05)**Mean Dep. Var 0.00 0.00 0.00 0.00ReadingTreat 0.06 0.08 0.14 0.06(0.04) (0.04)* (0.05)*** (0.05)Mean Dep. Var 0.00 0.00 0.00 0.00Obs. 27,360 27,519 6,670 20,840Panel B: IncarcerationEUPP -0.001 -0.010 -0.007 -0.012(0.001) (0.003)*** (0.004)* (0.003)***Obs. 29,938 31,697 9,859 21,838Mean Dep. Var 0.002 0.056 0.040 0.062Panel C: Formal Labor MarketEUPP -0.003 -0.002 -0.001 -0.003(0.006) (0.006) (0.010) (0.007)Obs. 29,938 31,697 9,859 21,838Mean Dep. Var 0.279 0.303 0.315 0.297Year FE Y es Y es Y es Y esSchool FE Y es Y es Y es Y esControls Y es Y es Y es Y esNotes: Table shows the results of regression for Borusyak et al. (2022) imputation estima-tor. I re-standardized the dependent variables for each subgroup for this table. Thus, thedependent variable is the standardized test score by topic of the exam, year of the exam,students\u2019 grade, gender and race (when applied). Students\u2019 controls include students\u2019 char-acteristics such as gender, race, mother\u2019s education, if lives with the mother, if the studenthas failed a grade or dropped out of school before and if works outside home. Schools\u2019controls are the number of enrollments, the number of employees, the number of comput-ers and an infrastructure index composed by the presence of a computer lab, science lab,library and sports court. Standard errors are clustered at favela level and dependent vari-able is standardized for each year and grade. * significant at 10%; ** significant at 5%; ***significant at 1%.45Figure 2.4: Heterogeneity of UPP treatment effects on schooling by grades - Dynamiceffects(a) Math - 5th grade (b) Math - 9th grade(c) Reading - 5th grade (d) Reading - 9th grade46Chapter 3The Impacts of UPP on Violence3.1 IntroductionUrban violence is a primary concern for several countries in Latin America (Jaitman et al.,2017), imposing substantial welfare costs to its citizens (Cerqueira and Soares, 2016). More-over, with the rapid growth of cities, most citizens of the world will live in a city by 2030(UN, 2018). The urbanization process and specific urban characteristics can potentially ag-gravate the urban violence scenario in the following decades (Glaeser and Sacerdote, 1999;UN Habitat, 2016). This violent urban scenario creates incentives for the formation of youthand street gangs (Venkatesh et al., 2008). These gangs evolve with the lack of public goodsprovided by the State and become \u2018political actors\u2019 controlling parts of the territory in acity (Blattman et al., 2022). When the drug business became these groups\u2019 primary rev-enue source, maintaining the domain was even more critical to protect drug profits. Thedomination of territories by armed groups increases the cost of public goods provision andlaw enforcement in these areas by the state and makes these gangs more resilient (Lessing,2017)1.In many urban areas, criminal groups rule non-contiguous territories within the city or evenin more than one city. This spatial feature facilitates the mobility of criminals to non-adjacentregions, reducing the cost of coordinated actions in different localities, and imposes severalchallenges for the government to design policies that reduce the territorial control of thesegroups. For example, place-based policies focused on restoring the presence of the state inthese areas ruled by criminal groups may induce spatial spillovers to untreated areas. Thespatial spillovers created by this type of policy could be either positive or negative. On the1In the case of Rio de Janeiro, these groups display criminal governance characteristics in more than 16%of the territory, with almost 2 million citizens living under criminal rule (Couto and Hirata, 2022b).47one hand, drug gangs could optimally choose a decrease in criminal activities in non-treatedplaces to reduce the probability of receiving the treatment in other parts of their territory.In this case, I would observe a crime deterrence effect of the policy (Becker, 1968; Chalfinand McCrary, 2017). On the other hand, criminals could migrate to other areas ruled bytheir gangs and continue their criminal activities. Given the criminal context and the possibleresponses to the treatment, it is not apparent ex-ante which areas are prone to receive positiveor negative spatial externalities.The spatial distribution of criminal criminals also creates econometric challenges when eval-uating policies focused on territorial control. This spatial criminal structure can be charac-terized by a network of allies and enemies in space that is largely unknown to researchers dueto the lack of data. Thus, any critical shock in parts of this network can easily propagate tounits further away, creating local responses in areas that are hard to predict ex-ante. Thus,it is difficult to define \u2018pure\u2019 control units that are not affected by the policy.This paper focuses on the spatial consequences of a large place-based policy that focusedon reclaiming territorial control back to the state of areas under the previous domination ofcriminal groups in an urban context. In the first chapter of the Thesis, I use geocoded violencedata for ever-treated favelas, and I show that the UPP policy reduces total homicides andpolice killings in treated favelas. However, there is no official geocoded violence informationfor large untreated favelas. Therefore, I could not address spatial spillover concerns in thesenever-treated units. In this chapter, I overcome this lack of information by using moreaggregated data at the police station level. This data covers police stations with largeuntreated favelas within its boundaries in the city of Rio and also provides informationfor police stations in the metropolitan area and the countryside of Rio de Janeiro State,which allows me to address spatial spillover concerns to these other untreated units as well.The Pacification Police Units program (UPP) was launched in 2008 and took selected favelascontrolled by criminal organizations back to the state. The strategy of this policy is to regainthe territory and then settle a permanent community-oriented policing in the favela. Theprogram was gradually expanded to 38 police stations installed in large favelas \u2013 covering28 out of 53 of the large favelas in the city of Rio and reaching almost a fifth of the cityof Rio\u2019s population \u2013 with the human force of 9,000 newly trained and hired police agents.The rise in police officers permanently allocated in these localities implies an increase in lawenforcement and the cost of doing drug business locally, which can induce responses by thetreated criminal groups: they could adapt to the new equilibrium and reduce the display ofviolence; they could move to other areas that belong to the same criminal group; or, theycould leave the criminal career path.To estimate the impacts of the UPP on violence using data at the police station level, I define48a police station treated if there is at least one large favela treated within its boundaries.Analogously, I define a police station within the city of Rio as control if there is a largeuntreated favela in its domain. I opt for this treatment definition because it is comparable tothe first chapter (treatment and control defined the presence of UPP in a large favela), andI can provide suggestive evidence of spatial spillover to the large untreated favelas, althoughat a coarser geographical definition. Moreover, for empirical exercises using police stationsoutside the city (metropolitan area or the countryside), I define all these as untreated. Iseparate them into different geographic regions defined by their criminal characteristics.I perform some empirical exercises to shed light on crime displacement to areas in the city,in the metropolitan area, and the countryside of Rio de Janeiro State. I find that the policyreduced violence in treated places and induced a response in control units (untreated policestations with large favelas in its boundaries in the city of Rio) that lowered crime in theseareas. However, there is suggestive evidence that the UPP partially displaced crime to otherregions outside the city (metropolitan area and countryside).There are few papers examining public policies intended to reduce the control of parts ofthe urban territory by criminal gangs that could move to other non-contiguous places inthe city or metropolitan area. Close to this paper, (Magaloni et al., 2020) and Ferraz et al.(2015) evaluate the Pacifying Police Unit Program in Rio, but without explicitly addressingthe migration problem in a unified econometric framework. Other papers provide evidencethat spatial spillover may be either positive or negative. Blattman et al. (2021) find negativespatial spillovers to nearby areas caused by a place-based intervention targeted in hot spotsin Bogota and Dell (2015) evaluates the causal impacts of large-scale interventions to combattrafficking sponsored by Mexican conservative party PAN on drug-related violence. Herresults suggest negative spillover effects to places where multiple drug routes coincide. Dracaet al. (2011) and Di Tella and Schargrodsky (2004) discover no evidence of spatial spilloverdue to spatially targeted interventions.Verbitsky-Savitz and Raudenbush (2012) estimate the impact of a community-policing pro-gram established in Chicago using a \u2018buffer\u2019 treatment group given by neighboring units totreatment localities. There is a growing literature that addresses this type of estimationmore formally. Clarke (2017) and Butts (2021) propose frameworks to estimate difference-in-differences in the presence of spatial spillovers. Clarke (2017) generalizes the concept of aneighborhood by defining a flexible distance metric and assuming that the treatment effectdecays as distance to treatment increases, and Butts (2021) shows that defining a flexibleweighting matrix removes biases and allows to estimate the total effects of the treatment.Importantly, though, this matrix has to be known by the econometrician, and some of theweights have to be zero. Given Rio\u2019s criminal context, in which the network of alliances and49enemies is unknown to the researcher, I leave the implementation of these new difference-in-differences estimators with spillovers for future research. For this paper, I focus on providingsuggestive evidence of the effect of the policy in untreated areas and other cities in themetropolitan area.In the next section, I discuss the institutional context of non-state armed groups in Rio deJaneiro. Section 3 describes the data. In section 4, I examine the empirical strategy. Section5 investigates the results and robustness exercises, and Section 6 considers further steps andconcludes the paper.3.2 ContextIn the first chapter of the Thesis, I describe the importance of territorial control for thecriminal organizations in Rio and the UPP program in detail. In this chapter, I focus on twoessential aspects of this context: i) drug factions rule in non-contiguous areas of the territory,which generates an unobservable (to the researcher) network of alliances among favelas underthe same drug faction flag; ii) arguably, the UPP program creates general equilibrium effectsthat impact the criminal market in Rio\u2019s metropolitan and countryside regions. I also discussthat the program induces distinctive incentives for different criminal actors and drug factionsin this market.3.2.1 Spatial Distribution of Drug FactionsInitially, I discuss the geographical boundaries of Rio\u2019s criminal market. Historically, thedecision area for criminal actors was Rio\u2019s metropolitan area (Misse, 2007). The rise ofdrug gangs in the 1980s based on local criminal governance at the favela level and on theprojection of power within the prison system strengthened the metropolitan region as theprimary geographical criminal market in Rio for two reasons: first, criminal actors needto maintain their criminal governance in the favelas they rule. Then, if other drug gangsthreaten their positions, they can rely on criminal support from other favelas under the samedrug faction rule. Since the drug faction is present in different areas of the metropolitanregion, they could ask for help from any other favela in this area, potentially reinforcing thenon-contiguous network of alliances.The second reason is that, given that these factions act within the prison system and thatthere is a high probability that drug traffickers go to jail at some point in their lives (Lessing,2017), criminal actors can create and fortify ties with criminal actors from other favelas whilein prison. Besides, drug traffickers in Rio\u2019s metropolitan region, if caught, go to the sameset of prisons, which facilitates the exchange of information among criminal actors in thisgeographical boundary. Thus, the prison system also creates incentives for the presence of50a non-contiguous criminal network and reinforces the metropolitan area as the locus of thisillicit market.Furthermore, drug factions do not display a strictly vertical structure at the leadership level(Hirata and Grillo, 2017a). Drug traffickers from a favela have agency to ally with otherfavelas ruled by the same drug faction. The factions exhibit a rhizomatic network structure,i.e., a horizontal network of mutual protection set by sufficiently independent players in thetop distribution of power where alliances can be made in any direction (Duarte, 2019). Theleaders display vast degrees of autonomy and might form coalitions to protect the territoriesor invade other places with other leaders. These alliances help criminal actors protect theirenvironment from invasions and plan criminal operations together. While I can assume thatthe network is common knowledge to criminal actors, I do not have a good proxy for the setof alliances and enemies.Figures 3.7 and 3.8 display how the criminal groups are spread over the city and the stateof Rio and also how the spatial distribution of drug factions changes over time. I rely ondifferent sources to create the evolution of the spatial distribution of criminal groups overtime. I geocoded maps from other researchers\u2019 sources only for the city of Rio de Janeiro. Iuse more recent maps created by a group of journalists and criminologists that shed light onthe spatial distribution in Rio\u2019s metropolitan region and the countryside of the State. Notethat the criminal groups are spread over the metro region and even in areas in the countrysideof the state of Rio de Janeiro. Since 2006, militias have grown in Rio\u2019s West Zone and partof the metropolitan region known as Baixada.The spatial distribution of drug factions and criminals\u2019 networks can create correlated move-ments in the criminal market in non-contiguous areas. For example, suppose that drugtraffickers from Red Command who rule a community in the West Zone of the city decide toinvade a place ruled by another drug faction, say a militia group. In the invasion, they ask forsoldiers from an allied favela in the North Zone of the city. To weaken the invasion the militiagroup could counterattack the alliance by striking the favela in the North Zone. In this case,violent outcomes from these two areas would be positively correlated through the networkof alliances and enemies. That is, any shock in a favela in Rio can potentially reverberateto other areas and create a correlation in criminal actors\u2019 strategies in this criminal market.Since the UPP was an ambitious public policy that targeted several favelas in Rio de Janeiroand increased the cost of doing criminal business in these areas, the program can be seen asan aggregate shock to this criminal market.Therefore, the network structure among criminal actors may rise concerns about crime dis-placement to untreated favelas in Rio de Janeiro. Criminals from a treated favela could moveto an untreated favela in response to the UPP program, which could increase crime in the51non-treated area. This process could lead to negative spatial spillovers (crime displacement),which bias the results and overestimate the impacts of the police on violence reduction.In terms of drug factions exposed to the policy, most of the Pacification Police Units wereinstalled in areas from the Red Command, which caused an unanticipated economic shockto this faction (Misse, 2011; Zaluar, 2012; Muggah, 2017). Until 2009, Red Command wasstrongest in South Zone and the North Zone of Rio and most of the Pacification PoliceUnits locate in these areas (Rodrigues, 2013)2. The militias received only one UPP in theirterritory.Using ethnographic and survey data, Zaluar (2012) estimated that in 2005 Red Command(CV) was the strongest drug faction, controlling half of the slums while the other gangscontrolled 20 percent. Militias were present in around 10 percent of the favelas. After thebeginning of the UPP policy at the end of 2008, the spatial distribution of these factionschanged. In the same study, (Zaluar, 2012) shows that militia groups increased and becamethe strongest territorial gang, controlling 45% of the slums. CV lost territorial power andhad 30% of the shantytowns. The other factions kept roughly the same percentage of favelas.3.2.2 Police structure in RioThe Police system in Brazil is composed of two Police institutions controlled by the states.The Civil Police is responsible for investigative duties, and the Military Police for patrollingand favela incursions when necessary. In an attempt to rationalize and coordinate thesetwo Police forces, the Secretary of Public Security (SSP-RJ) created the Integrated Areas ofPublic Security (AISP) that define the area of operation of a military police battalion andthe districts of civil police stations contained in the site of each battalion. Then, the policebattalions are coarser than police stations, i.e., a police battalion may have several policestations within its boundaries.There are 40 police battalions in the State of Rio de Janeiro, of which 18 are only in the cityof Rio. Meanwhile, there are 130 police stations in the State and 39 in the city of Rio deJaneiro. In terms of workforce, there are around 45,000 Military Police officers3 and 9,000thousand Civil agents4.The commander of each police battalion has some leverage to allocate military police agentsin the territory, which can create spatial correlations within the boundaries of a division.2Figure 3.7 (a) shows the spatial distribution of the drug factions in 2006, before the beginning of theprogram.3http:\/\/olerj.camara.leg.br\/retratos-da-intervencao\/a-policia-militar-no-rio-de-janeiro. Accessed in August2022.4http:\/\/www.policiacivilrj.net.br\/policia civil em numeros.php. Accessed in August 2022.52Therefore, I opt to cluster the standard errors in the empirical specifications below at thepolice battalion level.3.3 DataTo overcome the lack of geocoded episodes of violence for the whole city of Rio (or, at least,aggregated at the favela level)5, I use police station data, a coarser geographic unit than largefavelas, to address spatial spillover concerns to large untreated favelas. That is, since thecity of Rio does not provide geocoded violence information for all of the large favelas, I usethe minimum geographical unit with consistent official data throughout the years \u2013 which isat the police station level.I rely on official crime data from the Institute of Public Security (ISP-RJ), the statisticaland data intelligence office of the Secretary of Public Security (SSP-RJ). ISP-RJ consolidatescrime incident information and makes the data monthly available. In this chapter, I utilizemonthly data from 2004 to 2016 at the police station level.Police station boundaries may change over time due to the re-optimization of policing strat-egy. Some police stations are created after the beginning of our database. To avoid missingobservations in an unbalanced panel of police stations over time, I aggregated the statisticsat the police stations before the changes. I do the same procedure for any other police sta-tion information that may change over time: I consider the information related to the policestation before the change6. In Appendix B.1, I show how I coded these changes.I utilize the official shapefiles with the precise boundaries for police stations and UPPs fromthe Institute of Public Security (ISP-RJ) and the shapefile for large favelas from MPRJ InLoco7, a data aggregator project from Rio de Janeiro\u2019s Public Attorney Office. Figure 3.3 (a)displays the distribution of large favelas in Rio on top of the police station\u2019s boundaries. Idefine that a police station is treated if at least one large favela is treated within its limits. Ifthere is more than one large treated favela, I consider the treatment time as the first periodin which a favela was treated. A control police station has at least one large untreated favelain its domain and no treated favelas. Figure 3.3 (b) exhibits the police stations treated andin the control for the city of Rio de Janeiro. I opt for this definition for treated and controlpolice stations in the city of Rio to shed light on possible spatial spillovers that might haveoccurred in untreated large favelas. Although police station data is coarser than the favelalevel, it is the maximum spatial disaggregation which I can get comparable violence data for5In the First Chapter, I used geocoded data aggregated at ever-treated large favelas. Thus, I observedata at the favela level but only for ever-treated favelas.6For example, some of the police stations change the Police Battalion they are related. In that case, Iconsider the previous Police Battalion.7http:\/\/apps.mprj.mp.br\/sistema\/inloco\/. Accessed in June 2022.53treated and control places because geocoded violence data is not available for all of theselarge favelas.In total, there are 37 UPPs units in the city of Rio located in 28 treated large favelas and 25large favelas not treated that I use to define the control group. At the police station level,these translate to 18 treated and 11 control police stations. Using information provided byISP-RJ, the population in treated police stations is around 2.8 million citizens, while controlpolice stations have more than 2.3 million individuals.Figure 3.4 presents the evolution of crime variables over time, and table 3.1 shows the sum-mary statistics for violence outcomes two periods before and one after treatment for policestations in the city of Rio. Control police stations are more violent in the baseline thantreated areas. The semester average total homicide rate per 100,000 citizens for the yearsbefore the beginning of the policy (2007 and 2008) is slightly smaller (p < 0.1) for treatedplaces (24.1) than for control police stations (30.4). The semester police killings rate is statis-tically the same for treated and control police stations: 7.7 and 6.8 (p = 0.54), respectively.Although the violence levels may differ, there are no clear differential trends in periods beforethe treatment, which is vital for my empirical strategy.Figure 3.8 shows the spatial distribution of drug factions in areas of the metropolitan regionand the countryside. I separate the police stations into groups based on the socioeconomicand criminal characteristics of each area. The region of Baixada is composed of poor munic-ipalities with the historical presence of death squads and paramilitary groups (Alves, 2003;Cano and Duarte, 2012); Niteroi is a rich neighborhood in the metropolitan region with thepresence of the drug gangs in some parts of its territory; Sao Goncalo a poor municipalityin which drug factions also operate in some areas, and the Countryside defined by the restof police stations in Rio de Janeiro State \u2013 these areas are more heterogeneous in terms ofsocioeconomic characteristics and there is anecdotal evidence that criminal groups migrateto these cities after the UPP policy.Figure 3.6 shows the time series for violence indicators for these groups. I added to thisfigure, the evolution of treated and control areas in the city of Rio for comparison reasons.All the regions display a similar downward trend before the beginning of the UPP policy in2009. After the policy, the trends differ: while violence indicators keep decreasing for treatedand control police stations in the city of Rio, there are inflection points in the trends forother regions outside the city.543.4 Empirical StrategyThere are two main differences between the sample I use in this chapter to the sample inthe First Chapter: i) there are never-treated units defined by police stations that have atleast one untreated large favela and no treated units within their boundaries, which I referto as the control group from now on and ii) there are monthly data since 2004, which I useto increase the sample size. I construct semester violence rates from monthly data, and Iapply an inverse hyperbolic sine transformation in the dependent variable to reduce concernsraised by the positive skewness of the data.I follow the same empirical strategy as the First Chapter but with dependent and treatmentvariables defined at the police station level. I exploit the staggered introduction of the policyto estimate the impact of UPP treatment on violence measures. The identification relieson parallel trends and no anticipation assumptions. Hadn\u2019t the treatment occurred, thetrajectory of treated areas would follow a similar path to control units.The estimation equation is:Yit = \u03bbi + \u03b4t + \u03b2Dit + \u03f5it (3.1)where, i denotes the police station and t semester; \u03bbi and \u03b4t are the police station and timefixed effects, respectively. Dit is a dummy that turns one for semesters after the semester ofthe beginning of the UPP\u2019s occupation in a favela; \u03f5it is the error term. In this specification,\u03b2 is the parameter of interest, and I test the hypothesis that \u03b2 \u0338= 0. I expect the UPPprogram to reduce violence, so \u03b2 would be negative. The standard error \u03f5it can be correlatedto other observations within the same police battalion, i; therefore, they are clustered at thepolice battalion level.The UPP policy caused differential responses in treated areas. Residents in early-treatedfavelas are more prone to approve the program than citizens in late-treated areas (Ribeiroand Vilarouca, 2018; Willadino et al., 2018). Moreover, there is suggestive evidence thatthe program did better in the beginning (Magaloni et al., 2018). Thus, it is likely thatthe treatment had heterogeneous effects among treated units. To avoid concerns relatedto applying a Difference-in-Differences estimation in this context, I employ the estimatorproposed by Borusyak et al. (2022).I also estimate a dynamic difference-in-differences specification:Yit = \u03bbi + \u03b4t +\u22122\u2211\u03c4=\u22127\u03b3\u03c4Di\u03c4 +7\u2211\u03c4=0\u03b2\u03c4Di\u03c4 + \u03f5it (3.2)55where Dit\u03c4 is a dummy that turns one if the temporal distance to treatment is \u03c4 . Positivevalues refer to periods after the beginning of the policy, and negative values to periods before.To increase precision for each bin, I collapse the observations of six consecutive months intosemesters. Thus, the estimates reflect the effects of semesters before and after the beginningof treatment. I binned all periods before and after 7 semesters to -7 and 7, respectively. Thecoefficients of interest, in this case, are {\u03b3\u03c4}\u03c4<0, which represent the effects of treatment inperiods before the policy started, and {\u03b2\u03c4}\u03c4>0, the treatment effects. I expect that estimatesfor \u03c4 < 0 are not statistically different from zero and that coefficients for \u03c4 > 0 display anegative sign.The dependent variables are the inverse hyperbolic sine transformation of semester ratesof violence indicators. I use three main violence measures: total homicides, police killings,and other homicides. Total homicides are defined by the sum of police killings and otherhomicides. Police killings refer to homicides committed by on-duty police officers. Usually,these events happen during police raids within the favelas (Monteiro et al., 2020) when thepolice perform military operations with the goals of arresting drug criminals and apprehend-ing drugs. Given that criminal organizations control the territory, police raids often causea shootout between police officers and drug traffickers (Hirata et al., 2022). The last vio-lence indicator is other homicides. The variable measures homicides caused by interpersonalviolence.3.5 Results and DiscussionFigure 3.2 exhibits the evolution of homicides and police killings in the city of Rio de Janeiro.There has been a downward trend for both crime indicators since 2009. Considering thatthe city of Rio has treated and control units, these figures suggest that if there is crimedisplacement to control areas in the city, the reduction in violence in treated police stationswould have to be larger than the displacement effect.I split the time series for treated and control areas in Rio in figure 3.4. These graphsshow that both units display a similar pattern after 2009. The two time series are stronglylinearly correlated. The Pearson correlation index is 0.94 for homicides and 0.86 for policekillings. These figures suggest that, at least on average, there is no evidence for possiblecrime displacement to control areas.The reduction of violence in control areas suggests possible alternatives. It could indicatea confounder of the UPP program drives the results in both treated and control areas. Forexample, an income shock at the city level. I am not aware of any policy or event thatsimultaneously happened at the city level to be a confounder of the UPP. Alternatively,Menezes (2018) and Cano et al. (2012) argue that the UPP was a critical moment for Rio\u2019s56criminal market, which induced criminal agents to respond. Serrano-Berthet et al. (2012)suggest that criminals in untreated favelas in the city of Rio changed their behavior inresponse to the policy. Due to the spatial proximity to other treated places, drug traffickersin favelas in the city of Rio became more discreet to reduce the probability of receivingtreatment in their favelas and to adapt to a new equilibrium in which their favelas willpossibly be treated. These mechanisms indicate that crime diffusion is a possible result ofthe UPP policy.This suggestive evidence is relevant for the estimation in the First Chapter. If crime dis-placement happens to units in the control group, the findings for school and medium-runresults would be overestimated. Given the findings in this chapter, the estimates in the FirstChapter would be a lower bound for the effects of UPP on school and medium-run outcomes.Despite these downward trends in both treated and control groups, the results for the em-pirical specification in equation (1) in table 3.2 show that the UPP program did have adifferential reduction in total homicides and police killings compared to control areas. Theestimates indicate a decrease of around 7% of homicides and 25% of police killings. Theresults are robust to specifications that deal with the skewness of the dependent variablescaused by the count data. Figure 3.5 presents the dynamic effects of the policy. Policekillings and homicides remain lower than in control areas up to 6 semesters after the start ofthe UPP treatment. Importantly, there is no evidence of pre-trends.Table 3.2 and figure 3.5 show that reductions in police killings drive decreased violence intreated police stations. This result is consistent with the change of police strategy in treatedplaces. Instead of transitory police raids that often caused shootings in the favelas, theUPP program focused on permanent settlements within treated areas, which increased lawenforcement and the cost of doing drug business there, reducing violent episodes.These outcomes add to the results in the First Chapter of the Thesis. Even at the policestation level, a coarser geographical area, the UPP program reduces lethal violence. Theimpacts on total homicides are smaller but expected since the UPP policy targeted violencerelated to drug trafficking inside the favelas. If anything, the police station level estimationalso incorporates any spatial spillovers to treated areas outside the favelas in a treated policestation. So, the effects on total homicides suggest that the UPP reduced this type of violenceaccounting for local spillovers. Notably, the estimates for police killings point in the samedirection as in the First Chapter. Considering that most police killings happen within thefavelas (Monteiro et al., 2020) and the UPP program focused on changing the logic of policinginside the favelas, these outcomes are reassuring. Finally, the consequences of the treatmenton other homicides are somewhat expected. The dynamics of other homicides outside thefavelas may be different than within the favelas. Although the UPP program could have57impacted this type of violence, it was not the focus of the policy.Thus, the UPP program led to a response of criminal actors in treated favelas. They couldstay in these favelas and adapt to a new equilibrium with police officers continuously operatingthere, migrate to other favelas, or leave the drug business. Indeed, some criminal actorsadapted to the new policy and became more discreet in their routine operations (Serrano-Berthet et al., 2012), which is consistent with the results above, and some migrated to otherfavelas (Menezes, 2018).There is anecdotal evidence that drug traffickers migrated to places I do not consider inthe First Chapter, such as the Metropolitan Region and the countryside of the state of Rio(Willadino et al., 2018). I do not intend to estimate the general equilibrium effects of thepolicy in this paper, and I leave it for future research. However, I provide suggestive evidencethat crime displacement to other areas in the state of Rio de Janeiro is possible.First, I analyze the temporal evolution of crime indicators to these areas in figure 3.6. Thefigure suggests that both treated and control police stations in the city of Rio followed similartrends as the other areas before the program started and until 2012. After this period, thetrends start to diverge as violence levels increase in other areas. Second, I show in table 3.4that DD estimates using these different samples as control groups are not stable.Conceptually, under the parallel trends and SUTVA assumptions, any group that capturescontemporaneous shocks could be a suitable control group for treated units. In these cases,the control group imputes the temporal trends after the treatment and provides a counter-factual to the treated group. Assuming that the criminal market was in equilibrium beforethe beginning of the UPP program, common shocks to this market are expected to affect theplayers similarly. Thus, under the assumptions discussed, the coefficients should be stableregardless of the control group used. That is not the case. The findings suggest that all otherunits in the state of Rio receive idiosyncratic shocks around the same period or, more likely,criminals in these areas respond to the UPP program in the city of Rio and migrate to theseareas (Miagusko, 2016).Taken together, these findings suggest that the policy reduced violence in treated places,induced a response in control units that lowered crime in these areas, and partially displacedcrime to other regions in the state of Rio.3.6 Conclusion and Further StepsSeveral cities worldwide face urban violence problems that could be magnified by the presenceof organized crime that dominates some areas in the urban scenario. This paper addressesthe spatial consequences of a public policy - the Pacification Police Units program (UPP) -58designed to reduce the territorial control of drug gangs. These criminal organizations operatein non-contiguous parts of the metropolitan area of the city of Rio de Janeiro, which imposea challenge to estimate the impact of a place-based intervention such as the UPP.I find that the UPP program decreases crime outcomes in treated areas and reduces crimein untreated police stations in the city of Rio that have at least one large favela within theirboundaries. This last finding is consistent with a crime deterrence interpretation. Therefore,there is no evidence that using these units as control groups overestimates the conclusionsof the First Chapter of the Thesis. There is suggestive evidence of negative spillovers tountreated regions in the metropolitan area and the countryside of the state of Rio, though.In general, the empirical exercises in this paper suggest the importance of careful consid-eration of spatial spillovers while evaluating or designing this type of place-based policy.Considering untreated places that received negative spillovers as a control group might biasthe results and distort the cost-benefit analysis of the program. I intend to address how theUPP program changed the equilibrium of this criminal market in future research.First, the evolution of drug factions and militias over time creates the possibility of estimatingthe spatial game played by these criminal groups using a revealed preference argument forthe value of a favela (Seim, 2006; Adda et al., 2014). With the distribution of drug factionsand militias over time, I could define places of conflict and correlate these areas with theeconomic, demographic, and geographical characteristics of these places. Ideally, this couldshed light on the strategies played by the agents in the spatial game. Moreover, I can useanother source of homicide data from DATASUS, compiled at the neighborhood level (finerthan what I used in this paper), to capture the territorial conflicts of these factions moreprecisely.Second, I intend to discuss alternative policies to minimize the probability of migration oreven analyze the optimal selection of places to receive the program, considering the migrationresponses of criminals. In this case, I could build on Fu and Wolpin (2018), who studied theoptimal allocation of police forces across cities in the US, extending criminals\u2019 choice set toincorporate a locational choice as a response to the treatment.Understanding the dynamics of \u2018organized\u2019 crime in a city is critical to perform counterfactualtreatments. Inferring the drug gangs\u2019 preferences and objective function and the game playedwith the other criminal groups and the police is necessary to anticipate their responses causedby State intervention. This paper provides several stylized facts to comprehend the gameplayed by these actors and then design more cost-effective public policies.59Figure 3.1: Large favelas by treatment year60Figure 3.2: Temporal evolution for violence indicators for the city of Rio de Janeiro(a) Total homicides rate(b) Police killings rate61Figure 3.3: Treated and Control police stations in Rio de Janeiro(a) Large favelas and Police Stations boundaries(b) Treated and Control Police StationsNotes: The figure shows how I defined the police stations treated and in the control group. Apolice station is treated if there is at least one large treated favela within its domain. Similarly, apolice station belongs to the control group if there is no treated favela, but there is at least one largeuntreated favela in its catchment area.62Figure 3.4: Temporal evolution for violence indicators for treated and control stationsin the city of Rio de Janeiro(a) Total homicides rates(b) Police killings rate63Figure 3.4: Temporal evolution for violence indicators for treated and control stationsin the city of Rio de Janeiro (cont.)(c) Other homicides rate64Table 3.1: Summary statistics violence indicators per period of timePeriod Treat Control T-testPanel A: Total homicides rate2004-2006 27.1 32.3 0.122007-2008 24.1 30.4 0.082009-2016 12.6 19.4 0.00Panel B: Police killings rate2004-2006 6.7 6.1 0.562007-2008 7.7 6.8 0.542009-2016 3.0 3.7 0.12Panel C: Other homicides rate2004-2006 20.4 26.1 0.032007-2008 16.4 23.6 0.012009-2016 9.6 15.7 0.00Notes: Table shows the summary statistics for homicide indicatorsfor treated and untreated police stations in different periods of time.Total homicides are defined as the sum of police killings and otherhomicides. I divide the number of homicides in a semester by thepopulation in each police station to construct the semester rates per100,000 individuals. Column (1) displays the mean of these semesterrates for treated places, column (2) the mean for untreated policestations, and column (3) shows a T-test for the differences of themeans.65Table 3.2: Effects of the UPP on lethal violenceTotal homicides Police Killings Other homicidesPanel A: Borusyak et al. (2022)Treat -0.23 -0.49 -0.13(0.13)* (0.11)*** (0.13)Panel B: TWFETreat -0.25 -0.47 -0.16(0.11)** (0.12)*** (0.11)Obs. 754 754 754Semester FE Yes Yes YesPolice Station FE Yes Yes YesMean before treat. 3.57 1.91 3.29Notes: Table shows the results for regression equation (1) using Borusyak et al. (2022) imputationand TWFE estimators. The dependent variables are inverse hyperbolic sine of semesters\u2019 rates per100,000 citizens. Both regressions control for Semester and Police station fixed effects, have standarderrors clustered at the police battalion level, and use population as analytical weights. * significant at10%; ** significant at 5%; *** significant at 1%.66Figure 3.5: Dynamic effects of UPP on violence indicators(a) Total homicides rates(b) Police killings rate (c) Other homicides rateNotes: Figure shows the estimates for equation (2) using the TWFE estimator. I do not use Borusyaket al. (2022) estimator in these figures because the minimum effective number of observations is below theminimum recommended by the authors and the estimates may be unreliable. Total homicides indicator is thesum of police killings and other homicides. The dependent variables are inverse hyperbolic sine of semesters\u2019rates per 100,000 citizens. Both regressions control for Semester and Police station fixed effects, have standarderrors clustered at the police battalion level, and use population as analytical weights. Confidence intervalsare at 95%.67Table 3.3: Robustness for the effects of UPP on violence indicatorsTotal Homicides Police Killings Other HomicidesPanel A: Negative BinomialTreat -0.28 -0.44 -0.20(0.09)*** (0.14)*** (0.08)**Incidence Ratio 0.75 0.65 0.82Panel B: PoissonTreat -0.19 -0.47 -0.11(0.08)** (0.15)*** (0.08)Incidence Ratio 0.83 0.63 0.89Obs. 754 754 754Semester FE Yes Yes YesPolice Station FE Yes Yes YesMean before treat. 43.11 9.31 33.80Notes: Table shows the results for regression equation (1) using Negative binomial and Poisson es-timators. The dependent variables are counts of the events. Both regressions control for semesterfixed effect, police station fixed effect, and police station population (coefficient constrained toone); and, have standard errors clustered at the Police battalion level. * significant at 10%; **significant at 5%; *** significant at 1%.68Figure 3.6: Temporal evolution of crime indicators for police stations in the state ofRio de Janeiro(a) Homicides rates(b) Police killings rate69Figure 3.6: Temporal evolution of crime indicators for police stations in the state ofRio de Janeiro (cont.)(c) Other homicides ratesNotes: The figures show the temporal evolution of homicides and police killings in the State of Riode Janeiro. I consider six quarters before and six quarters after the current period to calculate the movingaverage. The police stations in the city of Rio that I use in the main estimation are the \u201cTreated\u201d and\u201cControl\u201d lines. The rest of the lines represent areas in the Metropolitan Region (\u201cBaixada\u201d, \u201cNitero\u00b4i\u201d, \u201cSa\u02dcoGonc\u00b8alo\u201d) and in the countryside of the state.70Table 3.4: Effects of UPP on crime indicators \u2013 different control groupsMain Baixada Niteroi Sao Goncalo CountrysidePanel A: HomicidesTreat -0.23 -0.58 -0.30 -0.47 -0.47(0.13)* (0.06)*** (0.05)*** (0.05)*** (0.06)***Mean before treat 3.57 3.74 3.53 3.60 2.79Panel B: Police KillingsTreat -0.49 -0.72 -0.82 -1.02 -0.82(0.11)*** (0.14)*** (0.12)*** (0.12)*** (0.12)***Mean before treat 1.91 1.48 2.06 1.83 0.56Panel B: Other homicidesTreat -0.13 -0.46 -0.04 -0.29 -0.33(0.13) (0.06)*** (0.06) (0.05)*** (0.06)***Mean before treat 3.29 3.56 3.18 3.33 2.70Semester FE Yes Yes Yes Yes YesFavela FE Yes Yes Yes Yes YesObs. 754 935 598 598 2,364Notes: Table shows the results for regression equation (1) for Borusyak et al. (2022) imputation esti-mator. The dependent variables are semesters\u2019 rates per 100,000 citizens. Both regressions control forSemester and Police stations fixed effects, have standard errors clustered at the police battalion leveland use population as analytical weights. Each column represents a separate regression that uses dif-ferent samples as control units. * significant at 10%; ** significant at 5%; *** significant at 1%.71Figure 3.7: Distribution of criminal groups in Rio de JaneiroSource: Zaluar (2012) and Zaluar and Barcellos (2014). Geocoded by the author.72Figure 3.8: Distribution of drug gangs and militia in Rio de Janeiro - 2019(a) State of Rio de Janeiro(b) Metropolitan RegionSource: Fogo Cruzado, NEV-USP, GENI-UFF, Pista News. Data comes from Disque-Denuncia.https:\/\/erickgn.github.io\/mapafc\/ and https:\/\/nev.prp.usp.br\/mapa-dos-grupos-armados-do-rio-de-janeiro\/ formore information. Accessed in June, 2022.73Chapter 4Heat and Health: A Tale of a TropicalCity4.1 IntroductionA growing stream of causal evidence has shown that changes in environmental factors affecthuman health. The heat-mortality relationship has attracted particular attention, as thepotential risks of climate warming and average temperature changes are expected to bewidespread across the globe. Detrimental effects of exposure to heat waves and extremelyhigh temperatures, considered one of the most damaging events, have been well documentedin different contexts in developed and developing countries. This has been made possible, toa great extent, by the utilization of plausibly exogenous variation in weather indicators atthe national and sub-national levels. A central empirical question, however, is how localizedthese effects are. This is especially relevant should damage be heterogeneous within regions.While much of the existing evidence comes from estimates of average treatment effects at theregional level, little is still known about the extent to which the impacts and the distributionof damages are localized in general and how effective localized policy responses can be inparticular.This paper examines the heat-mortality relationship at a fine-grained level within Rio deJaneiro, one of the world\u2019s largest and most heterogeneous cities. We rely on novel sourcesof satellite imagery on temperature and administrative health records at the individual levelto build a neighborhood-by-month panel over 14 years. These data allow us to use onlyintra-city, within-neighborhood variation in daily temperature to identify effects on healthoutcomes. By exploring the residual variation in temperature measures and outcomes, usuallyabsorbed in previous fixed-effect analyses at the national and sub-national levels, we can74contribute with novel evidence on the sources of heterogeneity in damages and for the optimaldesign of policy response.More specifically, we study the effects of extreme temperatures on the mortality rates dueto cardiovascular conditions of individuals aged 60 years and older. Hot days exacerbatethe capacity of the body to regulate its temperature, triggering a physiological process thatincreases the cardiac and pulmonary responses, which can lead to a higher risk of cardiovas-cular, respiratory, and cerebrovascular diseases (Kephart et al., 2022). Moreover, vulnerablepopulations, such as the elderly, have diminished capacity to regulate body core temperatureunder heat stress and, thus, can be more affected by extreme temperatures (Achebak et al.,2018).We use data products derived from satellite imagery that measure land surface temperature(LST), which is constructed using radiation emitted by the land surface observed by satel-lites. LST is highly correlated with air temperature, which weather stations measure, andcaptures thermal energy concentration and human comfort. While weather stations\u2019 spa-tial coverage is typically low and scattered within cities, LST data provide per pixel dailytemperature at a nominal pixel spatial resolution of 1km2. Given its latitude, the city ofRio de Janeiro has 1,524 pixels of 889m2, which are weighed by the census tract populationand used to construct temperatures for each of its 144 neighborhoods, in high-frequency,throughout the analysis. To compute mortality variables, we rely on a rich administrativemicrodata set, which contains the universe of all deaths in Rio and the exact neighborhood ofresidence, socioeconomic markers, date, and cause of death. These data allow us to computemortality rates at the neighborhood-by-month level and assess heterogeneity. Our empiricalstrategy draws upon a fixed-effects model, typically used to identify causal impacts of tem-perature on health outcomes in different contexts (Desche\u02c6nes and Moretti, 2009; Desche\u02c6nesand Greenstone, 2011; Barreca et al., 2016).Rio de Janeiro provides a unique empirical setting. First, the city is home to more than 6.3million people scattered across diverse neighborhoods regarding geographical elements andsocioeconomic characteristics. Rio spreads over 1,225km2 in the planet\u2019s tropical zone, whichexperiences intense insolation all year round. Forested massifs reaching heights superior to1,000 meters affect patterns of winds and temperature, as they shape the penetration ofthe Atlantic sea breeze into the hinterland and provide shade, contributing to the formationof microclimates within the city. Neighborhoods located behind the massifs receive the airoriginating from the ocean in a warmer way than those in the windward position. Thisphenomenon results in a significant variation in temperature among neighborhoods. Thereis substantial socioeconomic heterogeneity as well. HDI ranges from 0.970 in the area ofGa\u00b4vea to 0.732 in the contiguous Rocinha to 0.700 in the more distant Complexo do Alema\u02dco,75where income per capita is only a tenth in comparison to the first. The significant variationin socioeconomic conditions, across and within neighborhoods, overlapped with variation intemperature across microclimates, enabling us to explore heterogeneity in the heat-mortalityrelationship within the city.Second, Rio also provides unique variations in access to primary health care and emergencycare. We can exploit the restructuring of the city\u2019s primary healthcare system, mainly drivenby the staggered implementation of Family Health Clinics (FHC). Starting in 2008, thisprogram aimed to expand primary and preventive health care provision in their respectivecatchment areas. Population coverage started from 3.7% in 2008, reaching more than 50%in 2015, portraying significant variation over time both within and across neighborhoods.Beginning in 2007, in parallel, both the city and the state of Rio de Janeiro improved thephysical network of ER facilities with the implementation of more than 20 non-hospitalemergency care units to provide emergency care of low and medium complexity, togetherwith the restructuring of the previous physical network of hospital ERs (Bhalotra et al.,2020). This movement generally expanded access points to emergency care, thus reducingthe average distance of patients to ER facilities. We rely on precise geocoding of FHCcatchment areas and ER facilities and exploit idiosyncratic variation in the differential accessto public health care services across time and neighborhoods to examine the extent to whichand how the design of local health systems can effectively mitigate damages.We find that there is enough intra-city variation in exposure for the temperature-mortalityrelationship to manifest. Indeed, one extra hot day causes mortality rates to increase by0.53 (p < 0.01). In the typical neighborhood-month, these effects account for 2% of deathsdue to cardiovascular diseases in the population of 60 years and older. These results arerobust to different measures of heat stress. However, there is a possibility to mitigate theseeffects: access to preventive health care can attenuate the marginal effect of temperature oncardiovascular deaths. One standard deviation increase in coverage by Family Health Clinicsreduces the effects of one extra hot day by 27%. Moreover, if Rio had full primary healthcare coverage, these negative effects of heat stress would be completely mitigated.This paper contributes novel evidence to the active literature on the health effects of environ-mental changes and their distributional damages, particularly the growing stream of researchon heat-related mortality. The heat effects on mortality have now been well documentedin different contexts, and many studies explicitly consider heterogeneity in the distributionof damages and mitigation response (Cohen and Dechezlepre\u02c6tre, 2022; Garg et al., 2019;Burgess et al., 2017).A critical aspect in assessing the current estimates, however, is that studies often focus on na-tional or subnational fixed-effects models and rely on temperature indicators measured from76a small number of weather stations near cities or in city centers as a proxy for heat stress(as reviewed in Deschenes (2014)). This approach potentially converts much of the existingheterogeneity within locations into average treatment effects across sites. It invariably leadsto measurement error since the heat stress experienced by the population is not adequatelyrecorded. This is particularly problematic if there is sorting in population density, vulnera-bility, and exposure to the most adverse weather conditions. In our setting, exposure to heatstress is neighborhood-specific. At the same time, time fixed-effects control for common city-specific trends, such as fluctuations in the overall healthiness of the population and economicactivity. Although not possible, adding location-by-time fixed-effects in previous subnationalfixed-effects models would be analogous. Neighborhood or neighborhood-by-month fixed-effects further absorb differences by SES and location that are month-specific. In that sense,by relying on the residual variation in temperature and health outcomes, conditional on aset of within-city fixed-effects, our results reveal that relevant heat-related damages manifestthemselves and are unevenly distributed at the local level.We also explore heterogeneity in damages and examine the extent to which policy responses,again at the very local level, can act as mitigation factors. A few but solid recent stud-ies have documented that access to primary health services can act as a protective factoragainst temperature fluctuations (Cohen and Dechezlepre\u02c6tre, 2022). We advance the exist-ing evidence in meaningful ways. We show that heat-related damages can be mitigated withcommunity-level actions, in the short-run, and at the very local level, with the adequate re-design and expansion of health services within cities. We find that access to preventive ratherthan curative healthcare is mainly instrumental for mitigation efforts. We conjecture thataccess to preventive care leverages the management of chronic conditions and the adherenceto treatment and medications that are typically prescript for continuous use.Finally, there are several relevant aspects in assessing an urban environment exclusively.While the need for adaptation is likely to be widespread worldwide, urban areas will be onthe frontlines of climate warming. Cities are expected to be home to nearly 6.7 billion people,or 70% of the world\u2019s population, by 2050 (UN, 2018). With 40% of the world\u2019s populationliving in tropical zones today, we should expect a remarkably swift expansion of tropical citiesin the near future. Therefore, this paper\u2019s results are especially informative for the optimaldesign of localized mitigation policies in an increasingly urbanized world. This is particularlysalient since the existing evidence on whether the heat-mortality relationship is stronger inrural vs. urban areas has been somewhat mixed \u2013 e.g., ranging from a predominantly ruraleffect (Burgess et al., 2017) to insignificantly different (Cohen and Dechezlepre\u02c6tre, 2022).This stands out in developing countries, where weather shocks affect agricultural productivity,food intake, and income per capita. In this paper, we place the urban environment under thespotlight. We can revisit the heat-mortality relationship by exploring within-city variation,77coupled with a novel approach that made it possible to measure heat stress at a fine-grainedlevel and net the influence of relevant mechanisms typically active in other developing contexts(e.g., agricultural production). Our reduce-form estimates indicate non-trivial and robustadverse effects of heat stress on health outcomes, particularly among the most vulnerable.The remaining of this paper is organized as follows. Section 3.3 describes the backgroundand the data. Section 4.3 presents and discusses the empirical strategy. In Section 2.4 wepresent the main results on the heat-mortality relationship in the city of Rio and the mainrobustness checks. In Section 4.5 we test whether and how access to health services canmitigate damages. Section 4.6 concludes.4.2 Background and Data4.2.1 Rio de Janeiro: Geography, Climate and InequalityThe city of Rio de Janeiro spreads over 1,225 km2 on the tropical zone of the planet, underintense insolation all year round. Rio experiences higher temperatures between Decemberto March, during the summer, and relatively warm winters. According to official measuresfrom weather stations, February is the warmest month, with average daily temperaturesaround 28C and average maximums higher than 34C. July is the coldest month, but dailytemperatures still average above 22C. Despite the small number of weather stations, officialrecords also document significant temperature variations within the city. The average differ-ence between daily maximums and minimums as measured at 1 pm is superior to 5C.1 Riois well-known for its natural landscape, with dramatic geographical features scattered acrossthe city being determinant to temperature variation, together with proximity to the ocean aswell as general and secondary atmospheric circulation (Neiva et al., 2017). Forested massifsreaching heights superior to 1,000 meters affect patterns of winds and temperature, as theyprovide shade to some areas and shape the penetration of the Atlantic sea breeze into thehinterland, contributing to the formation of microclimates. In particular, sites behind themassifs receive winds warmer than those in the windward position (Neiva et al., 2017; Rio deJaneiro, 2016; Serra and Ratisbonna, 1941). Neighborhoods in the North the West Zones areusually the warmest, in contrast to areas in the South Zone, where the Atlantic sea breezecools the air.The left map of Figure 4.1 shows the main geographical elements of Rio as well as its divisioninto neighborhoods, which are ordered in Administrative Regions (North, West, South, and1All temperature records cited were computed based on official data from INMET over our analysisperiod.78Central Zones).2 The city is home to more than 6.3 million people and significant socioeco-nomic heterogeneity across and within neighborhoods. Poverty rates are nearly twofold inneighborhoods in the North and West Zones in comparison to those in the South Zone, whilethe Gini index ranges from 0.53 in the North Zone to 0.62 in the South Zone \u2013 where, in spiteof lower poverty rates, the share of inhabitants living in slums reaches 17%. HDI ranges from0.970 in the neighborhood of Ga\u00b4vea to 0.732 in the contiguous Rocinha, both in the SouthZone, to 0.700 in Complexo do Alema\u02dco, where income per capita is only a tenth in compari-son to the first (IETS, 2015; IBGE, 2010).3 In that sense, while socioeconomic disadvantagelargely overlaps with exposure to higher temperatures across neighborhoods, there remainsmuch inequality within-neighborhood, generally under more homogeneous temperature con-ditions.4.2.2 TemperatureOur empirical approach draws upon a monthly panel of data at the neighborhood level,covering the period from January 2003 to December 2016, on indicators of temperature andheat stress, health outcomes, and access to health services4. A key challenge in computingtemperature variables in developing countries is the availability of data (Auffhammer et al.,2013), where weather stations\u2019 spatial and temporal coverage is typically low and short. Inthe city of Rio, two parallel official meteorological systems comprise a total of only eightground weather stations, and most of them have been recording temperature only from theearly 2000s onwards5. Many papers overcome this problem by using gridded weather dataproducts (e.g., Matsuura and Willmott, 2018), which interpolates weather station data acrossspace and time to form a balanced panel of observations on a fixed spatial grid. Outside ofthe United States, the grid resolution of these data products is typically high and superiorto many kilometers (Hooker et al., 2018). For our study region, this would leave us with aconcise cross-sectional variation.To overcome this challenge, we take an alternative approach and use data products derivedfrom satellite imagery that collect land surface temperature (LST), as opposed to air tem-2Rio\u2019s municipal government officially defines neighborhoods. The current number of neighborhoods inRio is 162, but this has changed over time with new neighborhoods being created. To maintain spatialcomparability in our health data, we aggregate the 162 neighborhoods into the original 144 units.3All figures cited refer to IBGE (2010). The year 2010 is the mid-point in our analysis period and refersto the latest Population Census available.4LST data become available from July 2002 onwards. We select January 2003 onwards into our sampleto have 14 full calendar years. We end in December 2016 as this was the last month available at the time ofanalysis.5Two systems provide meteorological information for the city of Rio de Janeiro. First, the Alerta RioSystem with seven ground stations retrieving data on several weather variables (https:\/\/www.rio.rj.gov.br\/web\/georio\/alerta-rio). Second, the National Institute of Meteorology (INMET) has one ground station inRio.79perature (Tair), which is what ground weather stations measure. LST is constructed fromspectrum bands that measure radiation emitted by the land surface observed by satellites(Wan, 1999). We use Version 6 of the MYD11A1 data product derived from the MODIS(Moderate Resolution Imaging Spectroradiometer) instrument aboard NASA\u2019s Aqua satel-lite (Wan et al., 2015), which has provided a high-quality global LST product (Lian et al.,2017).6 This data product provides daily per-pixel land surface temperature at a nominalpixel spatial resolution of 1km. Images have been captured at approximately 1 pm local timeevery day since July 2002.The use of thermal remote sensing has been an emergent trend in earth sciences, and envi-ronmental epidemiology and applications of satellite-derived LST are now widely reportedin the literature to characterize urban heat islands (Azevedo et al., 2016; Hu and Brunsell,2013; De Ridder et al., 2012; Dousset et al., 2011; Rajasekar and Weng, 2009), to study areasof higher relative temperature within cities (Neiva et al., 2017; White-Newsome et al., 2013;Johnson and Wilson, 2009), and to estimate the near-surface temperature in the absence ofmeteorological stations (Chen et al., 2015; Good, 2015; Kilibarda et al., 2014).7 Concep-tually, LST is the physical temperature of the top few micrometers underlying the Earth\u2019ssurface. At the same time, Tair is the thermodynamic temperature of the air at the heightof approximately 2 meters above the surface (Lian et al., 2017). Despite these fundamentaldifferences, a growing stream of studies has shown that LST and Tair are strongly related(Good et al., 2017). Both worldwide and local analyses have validated satellite-derived LSTby ground-truthing, which typically compares exposure assessments in a specific site coveredby both LST images and ground stations. The findings indicate cross-section and time-seriescorrelations between LST and average Tair are often intense, particularly at night. Duringthe day, LST is generally more related to maximum Tair. Yet, this relationship dependson surface type, insolation, and elevation \u2013 LST becomes relatively higher than maximumTair in more sparsely vegetated and bare areas and under stronger insolation (Good et al.,2017; Lian et al., 2017). This is the case of the urban regions in the tropics, where LSToften surpasses Tair records. Overall, the difference between LST and Tair increases withTair (Mildrexler et al., 2011). Consistent with that, LST has been used as a reliable markerof heat islands and weather anomalies. For instance, Good et al. (2017) analyze the August2003 European heat wave and show that LST maps closely resemble the equivalent Tair overtime and space.In the MODIS data product we use, the city of Rio de Janeiro comprises 1,524 pixels of6The main alternative to MODIS is the LANDSAT satellite, which produces images once every 16 days.Since we need daily data, MODIS is better suited for our purposes.7In the economics literature on the effects of temperature, this approach seems to be rare. We are onlyaware of the work of Arago\u00b4n et al. (2018), who study the impact of temperature on small farmers\u2019 inputdecisions in Peru.80889m2. We use these pixels to construct population-weighted daily temperature and heatstress measures for each of the city\u2019s 144 neighborhoods. We use geo-referenced informationfrom Rio\u2019s 10,504 census tracts to assign each census tract to a pixel.8 To make this assign-ment, we take the census tract\u2019s centroid and assign it to the pixel with this point. Thisprocedure creates a daily panel of census tracts. Next, we use geo-referenced information onneighborhoods to assign each census tract to a neighborhood. Finally, we aggregate LST atthe neighborhood level by taking the average over the neighborhood\u2019s census tracts. Sincecensus tracts are designed to have roughly equal population size (IBGE, 2010), this procedureyields a population-weighted average temperature for each neighborhood-day.Using satellite data to measure heat stress has advantages and disadvantages. Satellite-derived LST has global coverage and high spatial resolution. Because of that, we can sys-tematically count the daily temperature for the whole city, at a very fine-grained level, formore extended temporal coverage than weather stations allow. On the other hand, the majordisadvantage comes from the fact that MODIS cannot provide meaningful data when thereis thick cloud coverage. In other words, we have missing temperature data whenever there iscloud coverage. To deal with the issue of missing data, we take the following approach. First,we use data from the available weather stations in Rio. For each neighborhood, we regressland surface temperature (from the satellite data) on air temperature (from the weather sta-tion data). Next, we use the fitted values from this regression to fill in any missing data. Thisprocedure is discussed in detail in Appendix C.1. It is similar to that used in other studiesin the economics literature that deal with missing observation in weather station data (e.g.,Auffhammer and Kellogg, 2011; Schlenker and Roberts, 2009).We then construct temperature measures at a monthly frequency to compute indicators forheat stress at the month-neighborhood level. As for our first indicator, we count the numberof days in a neighborhood-month in which temperatures exceed a given threshold. As furtherdiscussed below, we consider 40C as the benchmark, which roughly corresponds to the 90thpercentile of the daily LST. As typical in the economics literature, we construct alternativethresholds and bins to explore non-linearities in the heat-mortality relationship. We alsouse the number of degree-days, the sum of degrees that exceed a given threshold T , e.g.,T = 40C. Formally the number of degree-days in neighborhood i and month m isDegree-Days > Tim =D\u2211d=1max{temperatureidm \u2212 Tim, 0}, (4.1)8Census tracts are defined by the Brazilian Institute of Geography and Statistics (IBGE) and typicallycontain around 100 households. Residential areas in Rio are fairly dense; therefore, census tracts are smallrelative to 1km x 1km pixel size. Therefore, one census tract is typically entirely contained in one pixel.81where D is the number of days in month m. Finally, we create measures of heat waves. Todefine a heat wave lasting k days (k = {3, 5, 7}), we count the number of consecutive dayswith temperature greater than T in the neighborhood-month.The evidence indicates that LST strongly correlates with Tair, as mentioned above. We followthe literature and verify this relationship in our data by ground-truthing. Figure 4.2 showshow LST and Tair are related in Rio de Janeiro by using air temperature measurements fromone of the ground stations in the city and comparing it to the satellite data we use for theexact location and the same time9. The two plots make it clear that the two measures arestrongly correlated. However, LST is typically higher than the air temperature, as expectedduring the day in urban areas under high insolation. A simple time-series OLS regression ofLST on Tair at the month-by-year level yields L\u0302ST = 1.565+1.146Tair. This indicates thatLST records in our data are expected to average approximately 14.6% higher than Tair, plus1.5C in absolute terms (e.g., 30C in Tair is roughly equivalent to 36C in LST).Table 4.1, Panel A, shows descriptive statistics of our main temperature variables. Thesample size corresponds to 23,016 month-by-neighborhood observations [14 years\u00d7 12 months\u00d7 137 neighborhoods]. The average neighborhood-month LST is 32.6C (SD 4.92C), withabout 13 days per month recording LST between 25C-35C, 5.6 days with LST between 35C-40C, and 3.85 days with LST higher than 40C. Figure 4.3 displays the exact distribution ofthe average number of days per month across 10 LST bins. We also document substantialvariation in LST across neighborhoods, as shown on the right map of Figure 4.1. For agiven point in time, the average difference between the maximum and minimum LST acrossneighborhoods is approximately 13C, reaching about 17C in December-February. Consistentwith official measures of Tair and complementary literature (e.g., Neiva et al., 2017; Rio deJaneiro, 2016), we find that average LST in neighborhoods in the North and West Zones areusually higher, in contrast to records in areas in the South Zone.Figure C.1 presents both temporal and cross-sectional variation of the temperature shocks.These figures show the variation of the variable Bin 40+, which calculates the number ofdays in a month that land surface temperature is above 40 degrees Celsius, in the time andcross-sectional dimensions. Subfigure (a) displays the average fraction of days above 40C in aneighborhood relative to the historical average of days above 40C in that neighborhood. Wecalculate this measure for each neighborhood-month and, then, average in the cross-section10.9For this comparison, we choose the ground station of Alerta Rio System, located in the neighborhoodof Sa\u02dco Cristo\u00b4va\u02dco as it provides hourly temperature, over a longer span of time among the existing stations.10Let B40iym be the number of days above 40C for neighborhood i in year y and monthm; B40im the historicalaverage for the number of days above 40C in that neighborhood-month. For each period y,m, define thefraction of number of days above 40C relative do the historical average as: F 40iym = B40iym\/B40im. Subfigure (a)shows the average F 40iym across neighborhoods for each period of time:1N\u2211Ni=1 F40iym.82A value above one suggests that in that period, the average number of days above 40C ishigher than the historical average. This figure intends to show the time-series variation inthe data. Subfigure (b) presents the cross-sectional variation of the data. It displays thepercentage of neighborhoods with a number of days above 40C in that time higher than 1.5standard deviation of the historical average for that neighborhood. We observe that heatstress varies over time but also in the cross-section. Even when a heat wave arrives, not allneighborhoods are equally exposed to extreme temperatures once controlled by the historicalaverage temperature in the neighborhood-month.I present a case study for three neighborhoods located in distinct zones of the city in FigureC.2. Interestingly, there is variation in heat stress for these places in the extensive and in-tensive margin. For the extensive margin, not all neighborhoods display higher temperaturesthan average in the same periods. That is, there are months in which only one neighborhood\u2019is exposed to heat stress. In the intensive margin, even in periods in which the three placesdisplay higher temperatures than average, there is variation in the shock intensity. Thesepieces together suggest that microclimates matter in determining heat stress at the local levelwithin the city of Rio (Neiva et al., 2017)11.4.2.3 Health OutcomesExcessive heat and abnormally high temperatures trigger physiological responses that maylead to death. Basu (2009) shows that high temperature increases the risk for cardiovas-cular, respiratory, and cerebrovascular diseases. Some specific cardiovascular diseases, suchas ischemic heart disease, congestive heart failure, and myocardial infarction, also displaya high risk of occurring in elevated temperatures. The author highlights that some sub-groups, such as Black racial\/ethnic groups, women, those with lower socioeconomic status,and several age groups, particularly the elderly and infants, are more affected by elevatedtemperatures. Achebak et al. (2018) reason that the elderly have diminished physiologicalcapacity to regulate body core temperature under heat stress conditions.We rely on data from the Brazilian National System of Mortality Records (Datasus\/SIM)to compute mortality rates. SIM gathers information on every death officially registered inBrazil. We accessed the data via Datasus\/Tabnet Rio, which provides, specifically for thecity of Rio, the counting of deaths by descendent\u2019s neighborhood of residence, age, race,gender, and education, as well as by diagnostic identified according to the InternationalClassification of Diseases, 10th Revision (ICD-10).12 Based on literature review and follow-11For a non-technical explanation of microclimates in Rio: https:\/\/www.washingtonpost.com\/news\/capital-weather-gang\/wp\/2016\/08\/05\/the-summer-olympics-begin-in-rio-despite-the-fact-that-its-technically-winter\/.Accessed in November 2022.12Accessed in July 2019: http:\/\/tabnet.rio.rj.gov.br\/.83ing closer Eisenman et al. (2016) and the Environmental Protection Agency,13 we selectedICD-10 codes associated with cardiovascular conditions at increased heat-related risk. Morespecifically, this includes diseases classified under I00-99 (diseases of the circulatory system),syncope and collapse (R55) and sudden deaths (R96), transient cerebral ischaemic attacksand related syndromes (G45), vascular syndromes of the brain in cerebrovascular diseases(G46), and hemiplegia (G81-83).Based on these codes, we compute mortality rates for each neighborhood and month bycounting the deaths of individuals aged 60 or older and dividing by population (per 100,000).Data on the population aged 60 or older are obtained from IBGE (2010), which provides thecounting of residents by neighborhood in 2010. As previously mentioned, the year 2010 isthe mid-point in our period of analysis and refers to the latest Population Census available.14Monthly mortality rates at the neighborhood level are then merged with LST variables toform our panel of data at the neighborhood-by-month level. Table 4.1, Panel B, showsdescriptive statistics of mortality rates by causes of death related to cardiovascular conditionsat increased heat-related risk. We observed a monthly neighborhood average of 109 deathsper 100,000 individuals aged 60 or older during the analysis period. Among these causes, weobserve that mortality is more pervasively related to urgent conditions, such as heart attacks(mean 56.5) and strokes (31.4), though it is also directly related to chronic diseases, such ashypertension (15.7).4.2.4 Auxiliary Data and ControlsWe make use of other pieces of data that are auxiliary to our analysis. First, we identifyand geocode healthcare facilities in Rio (this includes hospitals, primary care, and emergencycare units) and compute the catchment areas of Family Health Clinics and average distancesfrom census tracts to ER services. We provide further background and details on healthpolicies and the computation of access to healthcare services in Section 4.5. Second, we adda series of controls at the neighborhood-month level to our analysis. This includes mappingPacifying Police Units, which are part of a law-enforcement program aimed at restoringterritorial control of some areas in the city that were previously under the power of criminalsand drug gangs. Data on the location and timing of the introduction of these units wereobtained from the Institute of Public Security (ISP). We intersected them with the shapefileof neighborhoods to determine the number of units in each neighborhood-year-month. We13https:\/\/www.epa.gov\/climate-indicators\/heat-related-illnesses. Accessed in June 2019.14More specifically, the denominator of mortality rates is computed for the year 2010, and thus it isfixed over time. We perform tests to check whether the results are sensitive to this limitation by addingto our specifications a combination of neighborhood-by-year fixed-effects and specific linear trends on thepopulation, as well as by using the outcome variable, the logarithmic of the counting of deaths. The resultsremain qualitatively robust.84also collected indicators for access to transportation. Data on Bus Rapid Transit (BRT)and the number of subway stations in each neighborhood were obtained from Pereira PassosInstitute. We followed the same procedure of intersecting the shapefile of neighborhoods tocompute the number of stations in each neighborhood-year-month.4.3 Empirical ModelIn this paper, we examine the relationship between heat stress and mortality rates due tocardiovascular conditions of individuals aged 60 years and older. Our empirical strategyfollows closely fixed-effects models that have been typically used to identify causal impactsof temperature on health outcomes in different contexts (Deschenes, 2014; Deryugina andHsiang, 2014; Barreca et al., 2016). The equation below, which adapts this class of modelsto a neighborhood-by-month setting, provides our conceptual setup:hiym = \u03b1y + \u03b4im +J\u2211j=1\u03bbjBjiym + \u03b2it+ \u03b3\u2032Ziym + \u03f5iym (4.2)Where hiym is the health outcome of neighborhood i, in year y and month m. The term\u03b1y refers to year-fixed effects, while \u03b4im refers to the neighborhood by calendar month fixedeffects. Our variables of interest are defined by Bjiym, which indicates the number of days withLST within the temperature bin j for neighborhood i in year y and month m. As typical inthe economics literature, we test for different definitions of bins and markers of heat stress. Inmore saturated specifications we also add \u03b2it, which is a neighborhood-specific linear trend,where t is the combination of year-month, and control variables Ziym, which include theshare of population covered by family health clinics (FHC), a dummy for the presence of anEmergency Care unit, and the number of Pacifying Police Units, Bus Rapid Transportationstations, and subway stations in each neighborhood-month. Control variables thus isolatethe potentially confounding influence of relevant public policies on healthcare, transport, andsecurity.15 The term \u03f5iym refers to idiosyncratic error. We estimate standard errors clusteredat the neighborhood level, to allow for serial correlation within neighborhoods, and weightregressions by neighborhood population size to smooth noisy variation in mortality in smallcells.In our setting, exposure to heat stress is neighborhood-specific, while year fixed-effects con-trol for common municipality trends, such as fluctuations in the overall healthiness of thepopulation and economic activity. Neighborhood-by-month fixed-effects further control for15There were important expansions in transport and security policies in the late 2000s and early 2010sbecause of major international events hosted by Rio, such as the Olympics (2016) and the World Cup (2014).The main policy interventions are considered in our set of control variables.85differences by SES, local infrastructure, and other location features that are month-specificand fixed at the neighborhood level. Year fixed-effects also absorb temperature fluctuationsthat are common to all neighborhoods, while neighborhood-by-month fixed-effects isolatemonth-specific temperature averages that vary across neighborhoods. This is analogous tocontrol for typical seasonality across microclimates. Conditional on fixed-effects, the residualvariation in temperature is plausibly idiosyncratic and arguably unexpected for that neighbor-hood and month. Identification, therefore, relies on exogenous temperature deviations fromneighborhood-month historical averages, conditional upon yearly averages, neighborhood-specific linear trends, and covariates.Importantly to our empirical approach, the residual variation in LST used for identificationvaries significantly in the cross-section and in the time series. We examine these patterns inFigure C.1. First, we compute the monthly share of neighborhoods under heat stress, i.e.,with the number of days with LST higher than 40C greater than their respective historicaverage plus 1.5 standard deviation. Second, we compute the monthly average log-deviationof the number of days with LST above 40C from the respective neighborhood historicalaverage. The left-hand plot of Figure C.1 shows that this latter indicator varies substantiallyover time. The right-hand plot shows that the incidence of heat stress is not homogenousthroughout the city at a point in time. We observe months under more pervasive heatstress, hitting almost 80% of the neighborhoods, and periods with less pervasive or with noneighborhood experiencing harsh temperature conditions. In other words, at a point in time,some areas may be suffering harsh temperature conditions, while others may not be.Conceptually, the introduction of time (i.e., month-year) fixed-effects would underestimatethe marginal effect of temperature on mortality because it would discount the effect of heatwaves that affect all the neighborhoods in relatively the same way. For example, if Feb\/2010was too hot, the estimates with time fixed-effects would only capture differences amongbairros, discarding the average effect of the heat wave itself. The estimates, in this case,will not capture the whole effect of the heat wave and, therefore, they will be smaller. Asrobustness, we also run the empirical specification with time fixed-effect, but the results showbe analyzed with this caveat in mind.The use of monthly rather than daily data helps us to smooth the computation of noisy dailymortality events at the neighborhood level as well as to overcome the confounding influence ofharvesting and other displacement effects (as discussed in Desche\u02c6nes and Greenstone (2011)).While it is difficult to raise plausible concerns regarding reverse causality and omitted factorsin our empirical setting, a potential caveat pervading our analysis relates to measurement er-ror. The measurement errors in the LST variable could be non-classical due to the imputationmethod and, thus, the estimates of the parameter of interest could be inconsistent. However,86our imputation method based on the nature of missing data in the LST data reduces theseconcerns.First, the missing data for LST is not missing completely at random (MCAR). The mainreason for missing values in LST data is the presence of cloudy-sky conditions (Mildrexleret al., 2011; Shiff et al., 2021), which implies that regressing mortality on LST directly(complete cases) would introduce selection on clear-sky days. However, LST\u2019s data generationprocess creates missing values at random (MAR), i.e., the occurrence of a missing value isstrongly correlated with other observed covariates that predict cloud coverage. Rubin (1976)shows that missing at random happens when, after controlling for several covariates, themissing value is randomly distributed. Therefore, if we project LST on a rich set of weathervariables measured from ground-based weather stations, the residual shouldn\u2019t be correlatedwith any other variable.We use a regression framework to impute the missing values in our dataset. The idea isto explore the time-series variation of several weather variables from the two ground-basedweather stations with (almost) complete observations and create an econometric model topredict the missing values in a neighborhood i, year y, and month m. The weather variablesin these data are temperature, wind speed, wind direction, precipitation, relative humidity,atmospheric pressure, and evaporation. If LST data is missing at random, after control-ling for these several variables that predict cloud coverage, the missing values should notbe systematically correlated with other variables. Furthermore, we perform this exercisefor each neighborhood individually to account for microclimates in Rio. That is, we allowfor neighborhood-specific relationships among weather variables and LST:for each neighbor-hood, we regress the (complete cases) LST in that neighborhood on this rich set of weathercovariates.4.4 ResultsTable 4.2 shows the effects of five different measures of temperature shocks on mortalitydue to cardiovascular causes for individuals aged 60 years and older. Row 1 shows theeffect of one extra \u201chot\u201d day in a month \u2013 i.e., one extra day with temperatures above40C. The specification in column 1 controls for neighborhood-specific month fixed effects andyear dummies. The remaining columns add controls to expurgate spurious variation thatmight have survived the rich set of fixed-effects included in column 1. We start by addingneighborhood-specific year fixed-effects in column 2, which aims to capture any shock thataffects the neighborhood in a year. The point estimates across columns 2 and 3 remainvirtually unchanged.We choose the specification in column 2 as our preferred, as it has a stricter set of controls. In87that specification, one extra hot day causes mortality rates to increase by 0.53 (p < 0.01). Tointerpret the magnitude of these effects, note that the typical neighborhood-month has fourhot days and that the average mortality rate is 109. Therefore, on the typical neighborhood-month, hot days account for 2% of the average cardiovascular-related elderly fatalities. Forthe city of Rio de Janeiro and its almost 1 million inhabitants aged 60 years old or more,this represents around 20 additional monthly deaths.The remaining rows show comparable results using different measures of extreme temperatureshocks. For example, the second row exhibits the effects of degree-days above 40C. Theestimates reveal that an extra 1C over 40C in a month leads to a 0.11 increase in mortalityrates in our preferred specification. In the typical neighborhood-month, there are 13C degree-days above 40C, which translates into 1.3 percent of the average mortality rate. For the heat-wave measures, the mean effect varies from 0.85 to 0.4 percent of the mortality rates. Theserows capture the effects of having a determined amount of continuous days with temperaturesabove 40C. For instance, row \u20184.Number of 5-day Heat Waves\u2019 considers the effects of aheat-wave that lasts more than five continuous days with daily temperatures above 40C. Asexpected, the point estimates increase with the duration of the heat wave.We add time fixed-effects in column (3). These fixed-effects absorb most of the variation ofa temperature shock that contemporaneously hit the neighborhoods, such as a heat-wave forexample. As we expected, the point estimates are smaller. The results are still significant forsome measures of shocks but not for all. For our main measure in row 1, we find that evencontrolling for time fixed-effects, one additional hot day causes the mortality rate to raiseby 0.28 (p < 0.05) implying more than 10 extra monthly cardio-vascular deaths in a typicalneighborhood-month.Additional Robustness Checks We show that the estimates of column 2 hold for alternativedefinitions of the empirical specification. Figure C.3 displays these results. We control fordifferent bins, alter the temperature threshold and change specific controls for rainfalls. Thepoint estimates are fairly robust to any of these modifications.U-shape relationship between temperature exposure and mortality Next, we estimate a flexiblefunctional form for the impacts of temperature on health. We use three-degree bins as ourmain dependent variables. Each bin displays the number of days in a month the dailytemperature is within the bin range. This non-parametric specification allows us to test thenon-linearities in the relationship between temperature and mortality. Moreover, we performtwo additional exercises that i) shed light on the temporal displacement of temperatureshocks on deaths, an effect that is known as \u201charvesting\u201d that suggests the possibility ofdelayed effects of temperature exposure, and, ii) provide a placebo exercise in which we testif previous temperature shocks correlate with current deaths. Figures 4.4 and 4.5 exhibit88these results. Similar to other papers in the literature, we find a U-shaped response oftemperature exposure on deaths (Hsiang et al., 2017).Heterogeneity Table 4.3 shows how the effects of heat stress vary with the socioeconomicmeasures at the neighborhood level. We interact the measure of temperature shock withvariables retrieved from Census 2010 that shed light on socioeconomic differences amongneighborhoods. There is suggestive evidence that neighborhoods with a better socioeconomicenvironment are less affected by temperature shocks. Table 4.4 presents the effects of heatstress on cardiovascular mortality for subgroups within each neighborhood. We calculatethe number of deaths by education and race for individuals living in the same area16. Theresults indicate that an extra hot day in a neighborhood causes different effects on theindividuals who live there: lower-educated citizens are disproportionately more affected byheat stress. The effects, compared to the sample mean of each group, are almost twice as largeas higher-educated individuals who live in the same neighborhood. Taken together, there isevidence that vulnerable populations are more susceptible to the effects of heat stress andthat socioeconomic conditions can act as protective factors.Specific causes of death In table C.1, we breakdown the causes of death from Cardiovasculardiseases. As expected, heat stress affects mortality rates related to cardiovascular conditionssuggested in the literature (Basu, 2009). In particular, temperature shocks have a higherimpact (relative to the mean) on strokes. Each extra hot day causes an increase of 1% inmortality rates due to strokes.Other causes of death and age groups Table C.3 displays the consequences of heat stress onmortality for other cases of death and age groups. Temperature shocks do not impact otherage groups younger than 60 years old (Panels A, B, and C). For individuals aged 60 or more,heat stress impacts all-cause mortality. One extra hot day increases the all-cause mortalityrate by 1.55 (p < 0.01), which represents 0.46% of the sample mean. To give a glimpseof these results, Barreca et al. (2016) find that one additional hot day affects all-cause andall-age mortality rates by 0.34%17.We also observe that exposure to high temperatures increases mortality due to respiratorydiseases. Our results for cardiovascular and respiratory diseases are consistent with thefact that exposure to heat stress may exacerbate underlying chronic conditions (de Oliveiraet al., 2020; Vaidyanathan et al., 2020). Moreover, this outcome is in line with the findings16Due to data restrictions, we do not observe the population for these cells, such as middle school dropoutsaged 60+ in each neighborhood, to construct rates per 100,000 individuals and to weight these regressions.We opt to show these regressions but using an inverse hyperbolic sine transformation in the number of deathsfor each subgroup.17To make the comparison similar, we use the most recent sample in Barreca et al. (2016), thus we considerthe point estimate in column 3 of Table 3 in their paper.89from Barreca et al. (2016) where air conditioning can mitigate heat-related deaths due tocardiovascular and respiratory diseases. In this paper, we focus on heat-related deaths dueto cardiovascular diseases. We will address the channels through which exposure to hightemperatures affects respiratory deaths in future research.Alternative imputation methods In table C.2 we show that the main results are robust todifferent imputation methods. Interestingly, the point estimate for the regression with com-plete cases is almost twice as large as the benchmark estimation. This is expected given thatLST complete cases selected information on clear-sky conditions, which tend to be warmer.4.5 Access to Health ServicesTable 4.5 estimates differential effects of hot days on health outcomes by access to healthservices. We start by interacting the number of hot days in a month with the fraction of thepopulation in a neighborhood-month that is covered by a preventive health care program,the Clinicas de Saude da Familia (CSF), or family doctors (see section 3.3). The resultspresented in Columns 1 and 3 indicate that larger coverage of the CSF is associated withsmaller hot day effects on mortality and hospitalization, respectively. The interaction termestimates are around -0.66 (p < 0.05) for mortality rate. To interpret the magnitude of theinteraction term, note that the standard-deviation of CSF coverage is 0.21. Therefore, a onestandard-deviation increase in the CSF coverage reduces the effect on mortality rate by 27percent. Next, columns 2 and 3 interact the number of hot days in a month with the averagedistance to ER in the neighborhood. The magnitude of point estimates of the interactionterms are very small are not significant at any conventional level.Table 4.5 gives evidence that preventive health care can significantly mitigate the hot-dayeffect on mortality due to cardiovascular diseases. The cost of preventive health care istypically much lower than that of emergency room visits, and the evidence presented hereshows that it can also be much more cost-effective. Distance to emergency rooms may beineffective in protecting from temperature shocks because, as Kovats and Hajat (2008) suggestin an extensive literature review, individuals who pass away due to extreme temperatureseither die suddenly or fail to reach medical attention.4.6 ConclusionSeveral papers have shown that temperature shocks and heat stress, in particular, cause anincrease in mortality, primarily by cardiovascular diseases. However, we did not know thathigh local variation in temperature was substantial. We use high-frequency satellite data toconstruct intra-city temperature measures of temperature exposure and estimate the effectsof heat stress on mortality by exploiting neighborhood-specific variation.90We present evidence that temperature shocks are associated with higher mortality ratesdue to cardiovascular diseases in the elderly, accounting for almost 2% of these deaths in atypical neighborhood-month. Moreover, there is suggestive evidence that more vulnerableneighborhoods and populations are more affected by heat stress. However, preventive healthpolicies may mitigate almost all of these effects: if Rio had universal primary health carecoverage, these adverse effects would be completely mitigated.This last set of results adds to a growing literature discussing the positive effects of expandingprimary health care in Brazil and in the city of Rio de Janeiro (Hone et al., 2020; Mrejenet al., 2021; Castro et al., 2019; Hone et al., 2017). Since individuals with chronic diseases aremore affected by heat stress (Basu, 2009) and primary healthcare coverage improves medicaladherence to treatment of these chronic conditions, we show that primary healthcare accessindeed mitigates the harmful effects of heat stress.However, primary healthcare coverage may not be cost-effective for dealing with local tem-perature shocks. Given that heat stress at the neighborhood level matters, policymakers maydesign policies targeted to alleviate the negative effects of temperature shocks. An excitingavenue for future research is understanding which local policies are cost-effective to reduce theburden of heat-mortality deaths. Examples of other policies that could be analyzed are thecreation of green areas, parks, cooling centers, subsidies to buy air conditioning machines orelectricity bills, or urban interventions that improve the climate resilience of neighborhoods.91Figure 4.1: Rio de Janeiro: Land Use and Heat Map(a) Land Use (b) Average LSTData on land use are publicly available from Institute Pereira Passos data lake (data.rio). We constructaverage LST at the pixel level over the entire period of analysis.Figure 4.2: LST and Air temperature in Rio de Janeiro102030405060LST at 1pm (remote sensing, \u00b0C)10 20 30 40Air Temperature at 1pm (ground monitor, \u00b0C)(a) Daily Measures2530354045Degrees Celsius2003m1 2005m1 2007m1 2009m1 2011m1 2013m1 2015m1 2017m1MonthLand Surface Temperature Air Temperature(b) Monthly AveragesThese figures use temperature data from two sources. Land surface temperature is measured by the MODISsensor aboard of NASA\u2019s Aqua satellite, which overpasses Rio de Janeiro approximately around 1pm localtime daily. We construct temperature measures by neighborhood according to the procedure described inthe text. We select the Sa\u02dco Cristo\u00b4va\u02dco, for comparison with the air temperature data. Air temperature ismeasured by Sa\u02dco Cristo\u00b4va\u02dco\u2019s ground station, which provides hourly temperature readings. We select the 1pmreading for comparison with the land surface temperature data. Figure 4.2a shows the daily measures of LSTand air temperature at 1pm. The red line represents the linear fit L\u0302STt = 1.565 + 1.156AirTemperaturet(R2 = 0.58). Figure 4.2b aggregates these data by taking monthly averages. In the Appendix, we providefurther analysis of correlations between different temperature measures.92Table 4.1: Summary Statistics of Neighborhood-Month PanelMean sdPanel A - Temperature MeasuresNumber Days > 40 C 3.85 6.04Degree Days > 40 C 12.9 25.0Number of 3-day Heat Waves 0.38 0.83Number of 5-day Heat Waves 0.15 0.47Number of 7-day Heat Waves 0.076 0.30Missing daily Temperature 4.24 6.52Panel B - Health OutcomesCardiovascular deaths per 100,000 individuals aged 60+ 109.5 71.4Panel C - ControlsShare population covered CSF 0.093 0.21Avg. Distance to ER (km) 2.51 2.17number bus stations in the neighborhood 0.18 0.98number subway stations in the neighborhood 0.021 0.18number upps in the neighborhood 0.24 0.70Notes: Data is a monthly panel of neighborhoods.93Figure 4.3: Neighborhood-Day Monthly Temperature Distribution15 20 25 30 35Air Temperature Equivalent (\u00b0C)12345days in neighborhood-month<16 20 25 30 35 40 \u226543Daily land surface temperatures (\u00b0C)94Table 4.2: Effects of Hot Days on Mortality due to Cardiovascular CausesShock Cardiovascular Deaths per 100,000 individuals aged 60+(1) (2) (3)1. Number Days > 40 C 0.534 0.526 0.278(0.112)*** (0.112)*** (0.138)**2. Degree Days > 40 C 0.101 0.111 0.039(0.023)*** (0.022)*** (0.027)3. Number of 3-day Heat Waves 2.006 1.945 0.913(0.668)*** (0.667)*** (0.717)4. Number of 5-day Heat Waves 4.968 5.163 2.486(0.888)*** (0.918)*** (1.021)**5. Number of 7-day Heat Waves 5.001 5.730 1.800(1.165)*** (1.274)*** (1.327)Bairro x Month \u2713 \u2713 \u2713Bairro x Year \u2713 \u2713Month x Year \u2713Controls \u2713 \u2713 \u2713Observations 23,016 23,016 23,016Mean dep. var. 109.5 109.5 109.5Notes: Data is a monthly panel of neighborhoods. Each row shows the effect of an alternative measure of a temperature shock.In row 1, the shock variable is the number of days with LST greater than 40C for a neighborhood i in year t and month m. Inrow 2, the shock variable is the sum of daily temperatures exceeding 40C in the month. In rows 3 through 5, the shock is thenumber of events with more than 3, 5, or 7 consecutive days of temperatures exceeding 40 C.Cardiovascular are diseases coded as I00 to I99, R55, R96, G45-46 and G81-83 in ICD10.Standard errors clustered at neighborhood level in brackets. All regressions are weighted by the population aged 60+ in eachneighborhood. All regressions control for the number of daily LST missing observations in the neighborhood-month.Linear trend refers to a specific neighborhood linear trend. Controls include the share of population covered by family healthclinics (CSF), a dummy for the presence of an emergency care units (UPA), and the number of Pacifying Police Units, bus rapidtransportation stations, and subway stations in each neighborhood-month.* significant at 10%; ** significant at 5%; *** significant at 1%.95Figure 4.4: The Effect of Daily Temperatures on Mortality due to CardiovascularCauses in Population 60+15 20 25 30 35Air Temperature EquivalentEffects on same month-1.5-1-.50.511.5Moratlity Rate (Deaths per 100,000)<16 20 25 30 35 40 \u226543Daily land surface temperatures (\u00b0C)(a)15 20 25 30 35Air Temperature EquivalentEffects on month m + 1-1.5-1-.50.511.5Moratlity Rate (Deaths per 100,000)<16 20 25 30 35 40 \u226543Daily land surface temperatures (\u00b0C)(b)This figure plots the coefficients from the specification controlling for daily temperatures, binned into three-degree bins, in the previous month. This specification allows for displacement (or \u201charvesting\u201d) and delayedeffects of temperature exposure.Figure 4.5: The Effect of contemporaneous and future (placebo) temperature exposureon Mortality15 20 25 30 35Air Temperature EquivalentEffects on same month-1.5-1-.50.511.5Moratlity Rate (Deaths per 100,000)<16 20 25 30 35 40 \u226543Daily land surface temperatures (\u00b0C)(a)15 20 25 30 35Air Temperature EquivalentEffects on month m - 1-1.5-1-.50.511.5Moratlity Rate (Deaths per 100,000)<16 20 25 30 35 40 \u226543Daily land surface temperatures (\u00b0C)(b)This figure plots the coefficients from the specification including for daily temperatures, binned into three-degree bins, in the next month. The coefficients associated with forward-lagged temperature should have noeffect on current temperature. This works as a placebo test.96Table 4.3: Differential Effects of Temperature on Mortality due to Cardiovascular Causesby Socioeconomic MeasuresShock Mortality Rate (per 100,000 individuals aged 60+)(1) (2) (3) (4)Number Days > 40C 0.811 1.205 0.657 3.025(0.202)*** (0.352)*** (0.137)*** (1.250)**Greater 40 x inc. per capita \u22120.146(0.094)Greater 40 x % pop. greater 1 min. wage \u22120.012(0.006)*Greater 40 x % pop. greater 5 min. wage \u22120.013(0.010)Greater 40 x SES index \u22124.121(2.066)**Year Dummies \u2713 \u2713 \u2713 \u2713Bairro x Month Dummies \u2713 \u2713 \u2713 \u2713Bairro x Linear Trend \u2713 \u2713 \u2713 \u2713Controls \u2713 \u2713 \u2713 \u2713Observations 23,016 23,016 23,016 23,016Mean dep. var. 109.5 109.5 109.5 109.5Notes: Data is a monthly panel of neighborhods. Each column is a regression with a different socioeconomic variable inter-acted. In column (1) we interact the temperature shock with the income per capita of the neighborhood, in column (2) withthe percentage of people who have income per capita greater than one monthly minimum wage, column (3) with the percent-age of people who have monthly income per capita greater than 5 monthly minimum wages, and in column (4) with an indexof socioeconomic development of the neighborhood created by Rio\u2019s City Hall from 2010 Census Data \u2013 higher value means abetter socioeconomic environment.Cardiovascular are diseases coded as I00 to I99, R55, R96, G45-46 and G81-83 in ICD10.Standard errors clustered at neighborhood level in brackets. All regressions are weighted by the population aged 60+ in eachneighborhood. All equations controll for the number of daily LST missing observations in the neighborhood-month.Linear trend refers to a specific neighborhood linear trend. Controls include the share of population covered byfamily healthclinics (CSF), a dummy for the presence of an emergency care units (UPA), and the number of Pacifying Police Units, bus rapidtransportation stations, and subway stations in each neighborhood-month.* significant at 10%; ** significant at 5%; *** significant at 1%.97Table 4.4: Effects of Hot Days on Mortality due to Cardiovascular Causes by Educationand RaceShock IHS number deathsBaseline Middle School Middle School White Non-Whitegraduated dropoutNumber Days > 40C 0.005 0.002 0.006 0.004 0.004(0.001)*** (0.001)* (0.001)*** (0.001)*** (0.001)***Year Dummies \u2713 \u2713 \u2713 \u2713 \u2713Bairro x Month Dummies \u2713 \u2713 \u2713 \u2713 \u2713Bairro x Linear Trend \u2713 \u2713 \u2713 \u2713 \u2713Controls \u2713 \u2713 \u2713 \u2713 \u2713Observations 23,016 23,016 23,016 23,016 23,016Mean dep. var. 2.2 1.0 1.6 1.7 1.2Notes: Data is a monthly panel of neighborhoods. Each column shows a different dependent variable. The dependent variablesare the inverse hyperbolic sine transformation of the number of deaths by education or race in a neighborhood, year, and month.We don\u2019t have the population for these cells, such as middle school dropouts aged 60+ in each neighborhood, to construct ratesper 100,000 individuals and to weight these regressions.Cardiovascular are diseases coded as I00 to I99, R55, R96, G45-46 and G81-83 in ICD10.Standard errors clustered at the neighborhood level in brackets. Hyperbolic inverse sine transformation was used on the depen-dent variables. All equations control for the number of daily LST missing observations in the neighborhood-month.Linear trend refers to a specific neighborhood linear trend. Controls include the share of population covered by family healthclinics (CSF), the average distance of each neighborhood to the closest emergency room (ER), and the number of Pacifying Po-lice Units, bus rapid transportation stations, and subway stations in each neighborhood-month.* significant at 10%; ** significant at 5%; *** significant at 1%.98Table 4.5: Mitigation Policies to Temperature shocks on Mortality due to CardiovascularCausesShock Mortality Rate (per 100,000 individuals aged 60+)(1) (2) (3)Number Days > 40C 0.481 0.319 0.470(0.134)*** (0.144)** (0.177)***Number Days > 40C\u00d7 Preventive Care \u22120.667 \u22120.660(0.320)** (0.337)*Number Days > 40C\u00d7 Distance to ER 0.048 0.006(0.057) (0.060)Bairro x Month \u2713 \u2713 \u2713Bairro x Year \u2713 \u2713 \u2713Controls \u2713 \u2713 \u2713Observations 23,016 23,016 23,016Mean dep. var. 109.5 109.5 109.5Notes: Data is a monthly panel of neighborhoods.Cardiovascular are diseases coded as I00 to I99, R55, R96, G45-46 and G81-83 in ICD10.Standard errors clustered at neighborhood level in brackets. 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Dados,55:327\u2013365.110Appendix AAppendix to Chapter 2111Figure A.1: Spatial and Temporal Evolution of UPPs in the city of Rio de Janeiro(a) Before Treatment (b) 2008(c) 2009 (d) 2010(e) 2011 (f) 2012(g) 2013 (h) 2014112Table A.1: Summary statistics violence indicators - semester rates per 100,000 indi-vidualsPeriod Mean sd min p25 p50 p75 maxPanel A: 2007-2008Total homicides 25.4 23.2 0.0 8.8 19.0 35.6 139.2Police killings 14.0 17.9 0.0 0.0 8.3 20.4 114.4Other homicides 11.3 13.0 0.0 0.0 7.5 17.7 56.8Panel B: 2009-2016Total homicides 10.6 16.2 0.0 0.0 5.7 14.5 127.3Police killings 4.2 10.2 0.0 0.0 0.0 5.0 106.1Other homicides 6.4 10.6 0.0 0.0 1.4 9.9 127.3Notes: Table shows the summary statistics for violence indicators fortwo periods: before the consolidation of the UPP policy (2007-2008)and after the beginning of the program (2009-2016). The values aresemester rates per 100,000 citizens. ISP-RJ defines total homicidesas the sum of police killings and homicides committed by individuals,which I label as other homicides in the following tables and graphs.113Figure A.2: Dynamic effects of UPP treatment on police killings and other homicidesrates(a) Police killings (b) Other homicidesNotes: Figure shows the estimates for equation (2) using the TWFE estimator. I do not use Borusyaket al. (2022) estimator in these figures because the minimum effective number of observations is below theminimum recommended by the authors and the estimates may be unreliable. The dependent variables areinverse hyperbolic sine of semesters\u2019 rates per 100,000 citizens. Both regressions control for Semester andFavela fixed effects, have standard errors clustered at the favela level, and use population as analytical weights.Confidence intervals are at 95%.Table A.2: Robustness for the effects of UPP treatment on violence ratesTotal homicides Police killings Other homicidesPanel A: Negative BinomialTreat -0.51 -0.98 -0.18(0.17)*** (0.31)*** (0.16)Incidence Ratio 0.60 0.37 0.83Panel B: PoissonTreat -0.61 -1.23 -0.24(0.19)*** (0.31)*** (0.17)Incidence Ratio 0.54 0.29 0.79Obs. 740 740 740Semester FE Yes Yes YesFavela FE Yes Yes YesMean before treat. 3.40 1.66 1.74Notes: Table shows the results for regression equation (1) using Negative binomial and Pois-son estimators. The dependent variables are counts of the events. Both regressions control forsemester fixed effect, favela fixed effect, and favela population (coefficient constrained to one);and, have standard errors clustered at the favela level. * significant at 10%; ** significant at 5%;*** significant at 1%.114Figure A.3: Treated and Control clusters of favelas115Table A.3: Socioeconomic characteristics form Census 2010 of Treated and UntreatedComplexes of favelasVariables Mean - Treat Mean - Control T-test Kolmogorov-SmirnovSocio-devolopment index 0.53 0.52 0.19 0.47% Inc. < min. wage 2.09 1.73 0.05 0.15% Inc. < 2 min. wage 78.74 80.28 0.38 0.15% Inc. > 10 min. wage 1.89 0.43 0.02 0.06Water service 95.30 97.29 0.39 0.62Sewage service 92.99 86.71 0.05 0.06Garbage service 97.56 98.55 0.15 0.54Avg. bathrooms hh 0.38 0.36 0.06 0.38Illiteracy rate 10y-14y 2.96 2.98 0.94 1.00Literacy rate above 5y 94.17 94.27 0.87 0.22% Non-white 65.29 66.95 0.28 0.08Avg. residents 22,415 25,854 0.60 0.95# households 6,889 8,177 0.54 0.96Avg. residents per hh 3.25 3.24 0.85 0.95Min. distance to Olympic (km) 3.75 8.26 0.01 0.03Notes: Table displays summary statistics for socioeconomic variables at the favela level. I retrieve the data from census tractsfrom Census 2010 and I aggregate at favela level by taking the census tracts in which its centroids are within a favela. Fordistance to Olympic venues, I geocoded the Olympic venues displayed in Towle (2013) and calculate the minimum distance ofa complex of favela to a Olympic venue.116Table A.4: Summary statistics for Treated and Control schools from School Census2007Variables Mean - Treat Mean - Control T-test Kolmogorov-SmirnovComputer Lab. 0.58 0.38 0.02 0.14Science Lab. 0.12 0.14 0.68 1.00Sports Court 0.55 0.68 0.12 0.62Kitchen 1.00 0.99 0.38 1.00Library 0.68 0.81 0.09 0.67Recreation Area 0.43 0.27 0.04 0.32Washroom outside the building 0.10 0.13 0.61 1.00# Classrooms available 14.12 14.50 0.70 0.52# Classrooms used 13.83 14.41 0.56 0.49# Computers 7.08 6.33 0.40 0.31Internet 0.97 0.94 0.43 1.00# Employees 48.43 52.15 0.30 0.18Teachers\u2019 office 0.87 0.85 0.74 1.00Director\u2019s office 0.88 0.87 0.84 1.00# Enrollment 722.78 843.88 0.06 0.11# Enrollment Elementary school 442.52 477.37 0.48 0.49# Enrollment Middle school 161.10 239.31 0.16 0.18# classes 23.97 26.32 0.22 0.78# students 716.85 842.83 0.05 0.11Avg. class size 29.69 31.86 0.00 0.01Notes: Table displays summary statistics for variables related to school infrastructure and composition of students from 2007School Census. Variables in which names don\u2019t start with \u201c#\u201d or \u201cAvg.\u201d show the percentage of schools in a treated or controlareas that have the characteristic defined by the variable. The remaining variables are nominal values that show the averagenumber of that characteristic in a treated or control area.117Table A.5: Differences between whites and non-white boys for socioeconomic charac-teristics in Prova BrasilVariables Mean: White Mean: Non-white T-testAvg. Math score 2007 207.35 200.75 0.00Avg. Reading score 2007 188.64 180.55 0.00Avg. Math score after 2007 232.58 228.19 0.00Avg. Reading score after 2007 210.44 205.38 0.00Lives mother 0.90 0.86 0.00Lives parents 0.56 0.48 0.00Only public school 0.79 0.79 0.44Failed 0.29 0.34 0.00Dropped out 0.08 0.12 0.00Mother lit. 0.95 0.93 0.00Father lit. 0.91 0.89 0.00Mother reads often 0.86 0.85 0.10Father reads often 0.75 0.74 0.00Mother above primary 0.62 0.60 0.63Mother above high school 0.40 0.39 0.50Works outside home 0.15 0.18 0.00# Bathrooms 1.30 1.23 0.00# Rooms 2.00 1.91 0.00TV 0.97 0.97 0.45Car 0.36 0.33 0.00Computer 0.72 0.68 0.00Notes: Table displays summary statistics for socioeconomic variables for white and non-whiteboys. I use students\u2019 socioeconomic survey to construct these variables. Variables in which namesdon\u2019t start with \u201c#\u201d or \u201cAvg.\u201d show the percentage of students in treated or control areas thathave the characteristic defined by the variable. The remaining variables are nominal values thatshow the average number of that characteristic in a treated or control area for each subgroup. Thelast column (\u2018T-test\u2019) shows the p-value of a T-test for the mean difference between the subgroups.118Table A.6: Heterogeneity of Treatment Effects of the UPP on standardized test scores- Early vs. Late treatedAll 2009\u2212 2011 2013\u2212 2015(1) (2) (1) (2) (1) (2)Panel A: MathTreat 0.095 0.085 0.14 0.14 0.01 0.03(0.042)** (0.037)** (0.06)** (0.05)*** (0.04) (0.04)Panel B: LanguageTreat 0.065 0.058 0.13 0.12 -0.03 -0.01(0.039)* (0.035)* (0.05)** (0.05)** (0.03) (0.03)Obs. 54,879 54,879 44,402 44,402 44,700 44,700Year FE Yes Yes Yes Yes Yes YesSchool FE Yes Yes Yes Yes Yes YesControls No All No All No AllNotes: Table shows the results of regression for Borusyak et al. (2022) imputationestimator. Students\u2019 controls include students\u2019 characteristics such as gender, race,mother\u2019s education, if lives with the mother, if the student has failed a grade ordropped out of school before and if works outside the home. Schools\u2019 controls arethe number of enrollments, the number of employees, the number of computers andan infrastructure index composed by the presence of a computer lab, science lab,library and sports court. Standard errors are clustered at favela level and the de-pendent variable is standardized for each year and grade. * significant at 10%; **significant at 5%; *** significant at 1%.119Table A.7: Robustness of the effects of UPP treatment on standardizedtest scores: alternative definitions of treatment(1) (2) (3) (4)Panel A: MathTreat until 6 months before the exam 0.097 0.101 0.100 0.103(0.042)** (0.037)*** (0.040)** (0.036)***Panel B: LanguageTreat until 6 months before the exam 0.065 0.071 0.067 0.072(0.038)* (0.034)** (0.037)* (0.033)**Obs. 54,879 54,879 54,879 54,879Year FE Y es Y es Y es Y esSchool FE Y es Y es Y es Y esControls No Students Schools AllNotes: Table shows the results of regression for Borusyak et al. (2022) imputation es-timator. In this table, I consider that a school is treated in a exam wave if the favelawhere the school is located was treated at least 6 months before the exam. Students\u2019controls include students\u2019 characteristics such as gender, race, mother\u2019s education, if liveswith the mother, if the student has failed a grade or dropped out of school before and ifworks outside home. Schools\u2019 controls are the number of enrollments, the number of em-ployees, the number of computers and an infrastructure index composed by the presenceof a computer lab, science lab, library and sports court. Standard errors are clustered atfavela level and dependent variable is standardized for each year and grade. * significantat 10%; ** significant at 5%; *** significant at 1%.120Table A.8: Robustness of the effects of UPP treat-ment on standardized test scores: alternativedefinitions of treatment(1) (2) (3) (4)Panel A: MathTreat - buffer 250m 0.067 0.069 0.067 0.069(0.037)* (0.035)* (0.038)* (0.036)*Panel B: LanguageTreat - buffer 250m 0.048 0.049 0.050 0.051(0.033) (0.032) (0.033) (0.031)Obs. 75,389 75,389 75,389 75,389Year FE Yes Yes Yes YesSchool FE Yes Yes Yes YesControls No Students Schools AllNotes: Table shows the results of regression for Borusyak et al.(2022) imputation estimator. In this table, I consider schoolsthat are up to 250m of distance to a treat or control favela. Stu-dents\u2019 controls include students\u2019 characteristics such as gender,race, mother\u2019s education, if lives with the mother, if the studenthas failed a grade or dropped out of school before and if worksoutside home. Schools\u2019 controls are the number of enrollments,the number of employees, the number of computers and an in-frastructure index composed by the presence of a computer lab,science lab, library and sports court. Standard errors are clus-tered at favela level and dependent variable is standardized foreach year and grade. * significant at 10%; ** significant at 5%;*** significant at 1%.121Figure A.4: Age of the individual when treatment starts: variation by cohorts of birthand year of treatment in the school.Notes: The figure displays information about treated and control cohorts and places used in the medium-run empirical strategy. The vertical variation, from \u201cNever Treated\u201d to \u201c2014\u201d, represents the year when aplace was treated; the horizontal variation, from \u201c1992\u201d to \u201c2000\u201d shows the year when a person was born.By combining these two pieces of information, I can define how old an agent was when treated started in thefavela she lives. For example, an individual born in 1997 who lives in a favela that was treated in 2010 is 13years old at the beginning of the treatment.Figure A.5: Example for years of exposure to treatment in primary schoolNotes: This example refers to an individual who is born in 1998 and enters primary school in 2004,at age 6. Suppose that she studies in a place that was treated in 2010. Then, she would be predicted to bein grade 7 when treatment started, and, therefore, she would be exposed to treatment for 2 years while inprimary school.122A.1 LinkageA.1.1 Conceptual Framework\u2022 There are two sets A and B, in which each element of these sets is defined by covariatesthat characterize the element.\u2022 Without loss of generality, I want to match elements of set A with elements in set B.\u2022 Ideally, for each element of a \u2208 A, I would search elements in a neighborhood of a inthe whole set B. However, this is computationally intensive because I would need tocalculate the distance of a to all elements of B.\u2022 For each element of A, we define a subset of B to look for matches.\u2200a \u2208 A, \u00b5(a) := {b \u2208 B;VX(a, b) < \u03b4}\u2022 where, VX is a distance function based on some covariatesX and \u03b4 is a criteria\/thresholddefined by the researcher.\u2022 This criteria doesn\u2019t have to be very strict.\u2022 Now, I calculate string and other distances for each element a \u2208 A and b \u2208 \u00b5(a). Thatis:For each a \u2208 A, calculateD(a, b) \u2200b \u2208 \u00b5(a)\u2022 Define a criteria (threshold) \u03f5 and matching function M such that:M(a, b) =\uf8f1\uf8f2\uf8f31 if D(a, b) < \u03f50 if D(a, b) \u2265 \u03f5Then, define:M(a,B) =\u2211b\u2208\u00b5(a)M(a, b)\u2022 Trade-off: \u03f5 and false-positive. If the criteria is loose, there is a higher probability ofdeclaring a false match.\u2022 If M(a,B) = 1, consider a match.\u2022 If M(a,B) > 1, choose a stricter criteria, i.e., \u03f5\u2032 < \u03f5 until we find an unique element in123B related to a.\u2022 If M(a,B) = 0, loosen the criteria, i.e., \u03f5\u2032\u2032 > \u03f5, until we find a element in B that mightbe a possible match to a. In this case, the likelihood of being a true match is lower.In the linkage application, I restrict the searches for individuals born in the same year andthat have the same first letter of the first name. This would be analogous to selecting the\u03b4 in the discussion above. In the linkage algorithm, it is analogous to block the search tothese two variables. Then, I calculate the Jaro-Winkler distance to elements that have thesame year and the same first letter of the first name. I define very conservative criteria fora match: the observations must have a Jaro-Winkler distance above 0.95 and have the samedate of birth. To run the linkage algorithm I use the package \u201cRecordLinkage\u201d in softwareR.124A.2 Panel student x yearFirst, I maintain only movements related to grades between the 1st grade and the 9th grade.This choice drops entries associated with Youth and Adult Education (EJA)1 and withpre-school movements2 The main reason for this choice is that these students attend sep-arate classrooms with different curricula and have different time schedules than children andteenagers, and, therefore, don\u2019t give information about the composition of peers attending aschool in a year that can influence the grades in standardized test scores.Second, I calculate the number of schools that appear for a student in a year. If a studentattends only one school in the year, I allocate that school to the student in that academicyear. If the student has entries associated with more than one school in a year, I either usethe school related to the student\u2019s enrollment in that year or, if there is no entry definingan enrollment, I keep the school with the minimum date of inclusion in the data. If thereare still more than one school for a student x year, I keep the observation associated with atransfer to that school. If, after all these steps, a student appears in more than one schoolin a year, I randomly pick which school she attended in that year.Then, I merge this data with the students\u2019 socioeconomic characteristics and I collapse atschool x year level, creating a panel that shows the average socioeconomic composition ofthe schools in a year.1Youth and Adult Education captures students who never attend school before or have more than 15years old and have not completed Middle school yet.2Although it is extremely important to understand if there are differences for Youth and Adult Educationor pre-school attendances in treated and control areas caused by the Pacification, these questions are not thefocus of the paper and I will leave the discussion for future research.125Appendix BAppendix to Chapter 3B.1 Corrections in police station informationI use official information data for the changes in police station information retrieved fromthe Institute of Public Security (ISP-RJ). I consider the first information related to a policestation. For example, if a new police station is created, I define that its violence data is addedto the former police station to which it was related. Then, I consider only police stationsthat appear over the entire period, from 2004 to 2016.Moreover, the police stations may change the police battalion to which it belongs. This infor-mation is important because police battalions allocate police officers within their boundariesand I cluster the standard error at the police battalion level.I document these adjustments below.Changes in police stations\u2019 information:\u2022 Data from police station 11 is added to police station 15;\u2022 Data from police station 45 is added to police station 22;\u2022 Data from police station 67 is added to police station 65;\u2022 Data from police station 70 is added to police station 71;\u2022 Data from police station 132 is added to police station 126;\u2022 Data from police station 148 is added to police station 143;\u2022 Data from police station 42 is added to police station 16;126\u2022 Data from police station 130 is added to police station 123.Changes in police battalions\u2019 information:\u2022 Police station 5 belongs to police battalion 13;\u2022 Police station 6 belongs to police battalion 1;\u2022 Police station 7 belongs to police battalion 1;\u2022 Police station 18 belongs to police battalion 6;\u2022 Police station 27 belongs to police battalion 9;\u2022 Police station 29 belongs to police battalion 9;\u2022 Police station 31 belongs to police battalion 14;\u2022 Police station 39 belongs to police battalion 9;\u2022 Police station 43 belongs to police battalion 39;\u2022 Police station 100 belongs to police battalion 28;\u2022 Police station 101 belongs to police battalion 10;\u2022 Police station 168 belongs to police battalion 10;\u2022 Police station 35 belongs to police battalion 39;\u2022 Police station 54 belongs to police battalion 40;\u2022 Police station 111 belongs to police battalion 11;\u2022 Police station 112 belongs to police battalion 11;127Appendix CAppendix to Chapter 4128Figure C.1: Time-Series and Cross-Sectional Residual Variation in Heat Stress(a) Time-Series Variation(b) Cross-Sectional VariationThese figures show the variation of the variable Bin 40+, that calculates the number of days in a monththat land surface temperature is above 40 degrees Celsius, in the time and cross-sectional dimensions. Figure(a) displays the average fraction of days above 40C in a neighborhood relative to the historical average ofdays above 40C in that neighborhood. A value above one suggests that in that period of time the averagenumber of days above 40C is higher than the historical average. This figure intends to show the time-seriesvariation in the data. Figure (b) presents the cross-sectional variation of the data. It displays the percentageof neighborhoods that have the number of days above 40C in that period time higher than 1.5 standarddeviation of the historical average for that neighborhood.129Figure C.2: Time-series variation for the number of days above 40C as a fraction ofthe historical neighborhood-month average for selected neighborhoodsThis figure shows the temporal evolution of the number of days above 40C in a neighborhood-monthas a fraction of its historical average for that neighborhood-month. We present the time series for threeneighborhoods in three different regions of the city and that differ in socioeconomic environment and exposureto heat stress. The neighborhood of Bangu in the West Zone of the city has the lowest socioeconomicenvironment and it is the warmest of the three, while Copacabana in the South Zone is the richer andcoolest. Tijuca located in the North Zone stays in the middle for both variables. The goal of this figure is toshow there is variation in the timing and magnitude of heat stress among the neighborhoods in the city.130Figure C.3: Robustness to different specificationsLower temp control-<23C<25C<27CHot day definition38C +39C +40C +41C +42C +Controls for rainfallNo# days no rainmonthly rainfallbins0.51  Main spec. Point estimate 95% CI 90% CIWe show alternative definitions of the empirical specification displayed in Column 3 of Table 2. We control fordifferent bins, alter the temperature threshold and change specific controls for rainfalls. The point estimatesare fairly robust to any of these modifications.131Table C.1: Specific Causes - Age 60+(1) (2) (3) (4)Heart Strokes Hypertensive Other CardioNumber days > 40C 0.14 0.29 0.10 0.00(0.07)** (0.06)*** (0.04)*** (0.02)Observations 23,016 23,016 23,016 23,016Bairro x Year \u2713 \u2713 \u2713 \u2713Bairro x Month \u2713 \u2713 \u2713 \u2713Controls Full Full Full FullMean Dep. Var. 56.50 31.41 15.70 5.875Notes: The ICD codes for each specific cause are: heart (I20-I52,R55, R96), strokes (I60-I67, I69, G45-G46, G81-G83), hypertensive(I10-I15), other cardio (remaining of the CID letter I). The estimatesare for bin 40+, which calculates the number of days with LST tem-perature greater than 40 celsius for a neighborhood i in year t andmonth m. Standard errors are clustered at neighborhood level andthe regression equation is weighted by the population with 60 or moreyears old within each neighborhood. Full controls for specific neigh-borhood linear trend, family health clinics (CSF), emergency careunits (UPA), the presence of Pacifying Police Units, bus rapid trans-portation units and subway stations in each neighborhood \u00d7 month.All equations are controlled by the number of LST temperature miss-ing observations in the neighborhood-month. * significant at 10%; **significant at 5%; *** significant at 1%.Table C.2: Effects of LST temperature on Cardiovascular outcomes(per 100,000 Individuals aged 60+) - Alternative Imputations(1) (2) (3) (4) (5)Benchmark Alt - Imput. Only Temperature Complete Cases Missing below 40Number days \u00bf 40C 0.526 0.593 0.684 1.021 0.963(0.112)*** (0.110)*** (0.112)*** (0.186)*** (0.141)***Observations 23,016 23,016 23,016 23,016 23,016Bairro x Year \u2713 \u2713 \u2713 \u2713 \u2713Bairro x Month \u2713 \u2713 \u2713 \u2713 \u2713Controls Full Full Full Full FullNotes: Cardiovascular are diseases coded as I00 to I99 in ICD10. The estimates are for bin 40+, which calculatesthe number of days with the complete cases LST temperature greater than 40C for a neighborhood i in year t andmonth m. Alt-imput. uses ground-based weather observations from 11am to 3pm only, instead of 6am to 5pm asin the Benchmark. Only Temperature uses only temperature variable, Complete cases consider only raw LST data,without the imputation mechanism described in Appendix A, and Missing below 40 considers all missing observationsas LST below 40. Standard errors are clustered at the neighborhood level and the regression equation is weighted bythe population with 60 or more years old within each neighborhood. Linear trend refers to a specific neighborhoodlinear trend, Health services, and infra. controls for family health clinics (CSF) and emergency care units (UPA)and socioeconomics controls for the presence of Pacifying Police Units, bus rapid transportation units, and subwaystations in each neighborhood \u00d7 month. All equations are controlled by the number of LST temperature missingobservations in the neighborhood-month ; * significant at 10%; ** significant at 5%; *** significant at 1%.132Table C.3: Effects of Hot Days on Mortality by Age and Cause of DeathAll Cardio- Respi- Infec- Neoplasm Violent\/Causes vascular ratory tious AccidentalPanel A - Infants (\u00a1 1y)Number Days > 40 C -0.14 0.04 -0.03 0.13 -0.01 -0.02(0.03) (0.04) (0.10) (0.09) (0.02) (0.08)Mean 161.5 1.75 11.52 0.39 1.21 5.05Panel B - 1y to 19yNumber Days > 40 C 0.01 -0.00 -0.00 -0.01 0.00 0.00(0.02) (0.00) (0.00) (0.00) (0.00) (0.02)Mean 6.13 0.18 0.28 0.43 0.08 3.34Panel C - 20y to 59yNumber Days > 40 C 0.04 0.00 -0.01 0.01 0.00 -0.01(0.03) (0.01) (0.01) (0.01) (0.01) (0.02)Mean 41.26 7.32 1.99 8.08 1.98 7.16Panel D - 60y+Number Days > 40 C 1.55 0.53 0.27 0.03 0.04 0.02(0.34)*** (0.11)*** (0.07)*** (0.15) (0.09) (0.06)Mean 330.7 109.5 47.25 15.20 56.26 12.84Observations 23,016 23,016 23,016 23,016 23,016 23,016Bairro x Month FE \u2713 \u2713 \u2713 \u2713 \u2713 \u2713Bairro x Year \u2713 \u2713 \u2713 \u2713 \u2713 \u2713Controls \u2713 \u2713 \u2713 \u2713 \u2713 \u2713Notes: Data is a monthly panel of neighborhoods. Each column is a separate regression for the dependent variable expressed in the col-umn. Each panel shows the estimates of heat stress on several mortality outcomes for that specific subsample. All regressions are weightedby that subgroup population in the neighborhood.Cardiovascular are diseases coded as I00 to I99, R55, R96, G45-46, and G81-83; Respiratory deaths are coded as letter J; Infections areletters A and B; Neoplams are letter C, and Violent and Accidental deaths are letters V, W, X, Y in ICD10.Standard errors clustered at neighborhood level in brackets.. All regressions control for the number of daily LST missing observations inthe neighborhood-month.Linear trend refers to a specific neighborhood linear trend. Controls include the share of population covered by family health clinics (CSF),a dummy for the presence of emergency care units (UPA), and the number of Pacifying Police Units, bus rapid transportation stations,and subway stations in each neighborhood-month.* significant at 10%; ** significant at 5%; *** significant at 1%.133C.1 Dealing with Missing ValuesThere are several methods used to deal with missing values in satellite data. Kang et al.(2018), Malamiri et al. (2018), Gerber et al. (2018), Zhang et al. (2018), Kou et al. (2016),Williamson et al. (2014) and Mildrexler et al. (2011) discuss different methodologies tohandle the missing observations.We use a regression framework to impute the missing values in our dataset. The idea isto explore the time-series variation of several weather variables from the two ground-basedweather stations with (almost) complete observations and create an econometric model topredict the missing values in a neighborhood i, year y and month m. The variables inthese data are temperature, wind speed, wind direction, precipitation, relative humidity,atmospheric pressure, evaporation. The assumption above translates as: after controlling forthese several variables, the missing values should not be systematically correlated with othervariables.Our goal is to find the set of variables and the econometric model that minimizes the averagedifference between the predicted values and the satellite realizations. To do that, we regressthe LST vector for each neighborhood i on the set of chosen variable from the complementarydatasets and use the predicted values to calculate the root mean squared errors with respectto the raw LST in that neighborhood1.The minimization problem is described as:minimize{gi,Xi}Ni1N\u2211iRMSE(g\u02c6i(Xi)), Yi))subject toXi = X, gi = g \u2200i and X \u2208 Xg is a linear functionwhere, Yi is the LST time series of place i, g is the econometric model and X is the set ofvariables in the model. The constraints say that we are choosing the same econometric modeland the same set of variables in the model for all neighborhoods. The objective function isthe average of the root mean square error between the predicted model and the LST timeseries.In order to solve this problem, we implement the following algorithm:1Since there are missing values in the vector for the raw LST, this exercise minimizes the average rootmean squared errors for the days with complete cases. An useful analogy is that the algorithm below istrained in the sample with complete observations and then creates out-of-sample predictions for the missingvalues.1341. Take g and X given.2. We run N regressions, one for each neighborhood of Yi on g(X).3. Calculate the empirical distribution of the predicted values g\u02c6i(X) and compare withthe empirical distribution of LST data for the same neighborhood.4. Calculate the RMSE.5. Go back to the first step and try different g and X until we minimize the objectivefunction.The chosen model uses the following set of variables: (i) from Alerta Rio System - hourlyobservations of air temperature, humidity, a dummy for precipitation and wind speed from6am to 5pm and (ii) from the National Institute of Meteorology (INMET) - daily observa-tions of maximum air temperature, minimum air temperature, average air temperature, aprecipitation dummy, relative humidity and Piche evaporation.We use two alternative models for robustness checks: one with the same set of variables butrestricting observations from the Alerta Rio System to be between 11am and 3pm; the otheruses only temperature variables.C.2 Timing and expansion of health infra-structureFigure C.4: Expansion of health infrastructure over time and across neighborhoods inRio(a) (b)This figure shows the variation over time and across space that we explore to construct the measures ofdistance to ER and percentage of individuals covered by primary health care.135C.3 Neighborhoods\u2019 aggregationIn order to make our datasets consistent, we aggregated the 162 neighborhoods into 144bairros. To do so, we consider recently emancipated neighborhoods as still belonging to theirneighborhood of origin. We do the following corrections:\u2022 Gericino is considered as Bangu.\u2022 Vila Kennedy as Bangu.\u2022 Vasco da Gama as Sao Cristovao.\u2022 Parque Columbia as Pavuna.\u2022 Lapa as Centro.\u2022 Freguesia, Ribeira, Zumbia, Cacuia, Pitangueiras, Cocota, Bancarios, Jardim Guan-abara, Jardim Carioca, Taua, Monero, Portuguesa and Galeao as Ilha.The main regressions for individuals aged 60 years old or more consider only neighborhoodswith population for this age group greater or equal than 500 people. Seven bairros areexcluded: Camorim, Campo dos Afonsos, Cidade Universitaria, Grumari, Joa, Paqueta andSaude. We chose this criteria because since these neighborhoods have very low population,their mortality and hosp. were inflated.136","type":"literal","lang":"en"}],"http:\/\/www.europeana.eu\/schemas\/edm\/hasType":[{"value":"Thesis\/Dissertation","type":"literal","lang":"en"}],"http:\/\/vivoweb.org\/ontology\/core#dateIssued":[{"value":"2023-05","type":"literal","lang":"en"}],"http:\/\/www.europeana.eu\/schemas\/edm\/isShownAt":[{"value":"10.14288\/1.0427413","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/language":[{"value":"eng","type":"literal","lang":"en"}],"https:\/\/open.library.ubc.ca\/terms#degreeDiscipline":[{"value":"Economics","type":"literal","lang":"en"}],"http:\/\/www.europeana.eu\/schemas\/edm\/provider":[{"value":"Vancouver : University of British Columbia Library","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/publisher":[{"value":"University of British Columbia","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/rights":[{"value":"Attribution-NonCommercial-NoDerivatives 4.0 International","type":"literal","lang":"*"}],"https:\/\/open.library.ubc.ca\/terms#rightsURI":[{"value":"http:\/\/creativecommons.org\/licenses\/by-nc-nd\/4.0\/","type":"literal","lang":"*"}],"https:\/\/open.library.ubc.ca\/terms#scholarLevel":[{"value":"Graduate","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/contributor":[{"value":"Ferraz, Claudio","type":"literal","lang":"en"},{"value":"Lemieux, Thomas","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/title":[{"value":"Essays on urban violence and health","type":"literal","lang":"en"}],"http:\/\/purl.org\/dc\/terms\/type":[{"value":"Text","type":"literal","lang":"en"}],"https:\/\/open.library.ubc.ca\/terms#identifierURI":[{"value":"http:\/\/hdl.handle.net\/2429\/83911","type":"literal","lang":"en"}]}}