Movin’ on Up?
The Impacts of a Large-Scale Home Ownership Lottery in Uruguay
Vincent Armentano∗
Craig McIntosh†
Felipe Monestier‡Rafael Piñeiro§
Fernando Rosenblatt¶
Guadalupe Tuñón‖
October 3, 2022

Abstract

We report on a large-scale urban resettlement program in Uruguay. Over the courseof seven years the program randomly assigned thousands of low-income households
to ownership of apartments in new buildings in middle-class areas, including a subsidy
averaging $44,000 per household. We match applicants to comprehensive administrative
data on employment, schooling, health, fertility, and voting over the decade subsequent
to the move. We find that the program led to a small decline in fertility for womenand a two percentage point increase in formal employment, but did not drive school
attendance. Likely due to the lack of strong spatial inequality in Uruguay, this relocation
program did not result in transformative improvements in the lives of its beneficiaries.

Keywords:
JEL Codes:∗

Housing policy, economic mobility, political participation
O18, I38, D72

University of California, San Diego
University of California, San Diego. Corresponding author, ctmcintosh@ucsd.edu.
‡
Universidad de la República, Uruguay§
Universidad Católica del Uruguay¶
Universidad Diego Portales, Chile‖
Princeton University. The authors gratefully acknowledge funding from the Fondo Maria Viñas, Agencia Nacionalde Investigación e Innovación (ANVII), Uruguay. The study filed the pre-analysis plan 20171101AA with Evidence inGovernance and Politics (EGAP), which can be found at https://osf.io/k472u. We thank Javier Chiossi and Lihuen
Nocetto for excellent research assistance. The authors declare no financial interests in the study.
†

1Introduction

One of the most fundamental changes that the government can induce in the life of its citizens is torelocate them in space. Residential mobility programs have long been of interest to social scientists
because they provide an unusually clear window into the role of context in driving human behavior(Kling et al., 2005). The best-known place-based policy in the US (Moving to Opportunity, or
MTO) randomized access to housing vouchers in five US cities conditional on moving to a less poor
neighborhood. Studies of MTO found modest short-term improvements (Katz et al., 2001; Ludwig
et al., 2008; Jacob and Ludwig, 2012), but then more transformative life-long benefits accruing
to children who moved young (Chetty et al., 2016), particularly for girls (Ludwig et al., 2013).1
However, little new experimental evidence has emerged since the MTO study was conducted, andthere are few rigorous studies of place-based programs outside of the US.2 Given the importance ofurban inequality and social mobility, understanding the broader impact of such policies is critical.
We provide evidence based on a series of 187 independent lotteries conducted by the governmentof Uruguay’s Compra de Vivienda Nueva program to assign subsidized mortgages to poor families
from peripheral neighborhoods, allowing them to buy an apartment in newly constructed buildings
closer to urban centers. These lotteries involve 4,883 households, and we have national ID numbers
for all 15,502 individuals who lived in these households at the time they applied for the housing
lottery. A data agreement with the Uruguayan government allows us to view formal employment
status, fertility, public K-12 and university enrollment status, as well as voter turnout in local
elections for the universe of lottery participants. The first lotteries took place in 2009 and wehave outcomes up through 2020, providing a relatively long post-treatment window to observe
the evolution of outcomes as the winners move, become home owners, and adapt to their newneighborhoods. We also have GIS locations for the neighborhood at the time of application as wellas the location of the new building, and so can look for signs of heterogeneity expressed in termsof how large the potential improvement in neighborhood would be. This environment represents
a unique combination of large-scale experimentation, real-world government implementation, anduniversal capture of outcomes using administrative data.
Roughly one in six applicant households win a place in a new building over all the lotteries. This
move entails a meaningful improvement in the quality of housing and local life; for example theaverage lottery winner moved to neighborhoods with property values that were one third higher,
1

Early evidence from the Gautreaux program in Chicago suggested substantial benefits to children and mothers frommoving away from high-poverty neighborhoods (Rosenbaum, 1995); evidence on why MTO may not have had alarger impact has centered on the fact that the beneficiaries chose to move to neighborhoods that were wealthierbut still minority-dominated and so may not have shifted peer groups (Clampet-Lundquist and Massey, 2008).
2
Barnhardt et al. (2017) analyze a randomized housing lottery in India after 14 years; they attribute null resultsof that program to the dislocation in social networks induced by the move. Franklin (2019) examines a housing
lottery in Ethiopia that moved slum-dwellers to large apartments on the periphery of the city, finding decreases inconflict but no change in labor supply or earnings. The most similar program to ours is Brazil’s My House, My Life
(PMCMV) program, which was found by Leape (2020) to have increased earnings by 13% and employment by 2%
within four years.

2

voter turnout rates that were almost 2 percentage points higher, housing formality goes from lessthan half to 100%, and the number of bedrooms rises by more than .5. Unlike most US programs,
CVN provided a very large subsidy to purchase the new unit (68% of the purchase price of theunit and 76% of the monthly payment, for an average of $44,000 per winning household), as wellas making them titled homeowners in their new neighborhoods. The existing literature leads us tobelieve that this ownership dimension will prove conducive to the economic incentives of families
to invest in their property (Galiani and Schargrodsky, 2010), as well as to participate politically(Rohe 2001). For example, homeowners are more inclined than renters to participate in voluntaryorganizations and in politics at the local level (Cox, 1982; Blum and Kingston, 1984; McCabe,
2013; Kumar, 2022). Hence the program provides beneficiaries with a bundle that includes an asset
transfer and a title to a home as well as locating them in a new neighborhood.
Despite the excellent statistical power, universal capture of outcomes, long duration of measurement, and bundle of transfers implied by treatment, we discover only relatively modest effectsof the program. We use three distinct techniques to measure the impacts of exposure to treatment.
First, we cumulate outcomes across all post-lottery years available for each outcome and examine
the simple Intention to Treat as a function of treatment status in the first lottery entered. Second,
we use an event study approach to measure the year-on-year effects of entry into the treatment,
which allows us to focus on the possibility of short-term disruption effects that might dissipate orreverse in the longer run.3 Finally, we follow Abdulkadiroğlu et al. (2011) and Cullen et al. (2006)
in estimating an IV/LATE on the number of years an individual had been a lottery winner, whichlooks for a linear slope in duration of treatment. None of the outcomes display patterns acrosslottery years and estimation approaches that are strong and robust, but the program does havedetectable effects. For employment, treatment effects across most lottery years are positive and thepooled effect is significant, with a point estimate indicating a two percentage point improvementin the likelihood of a family member being formally employed (over a control mean of 53%). Each
additional year of treatment increases employment rates by .4 percentage points. For female family
members, winning the lottery results in a small drop in fertility rates which is never compensatedfor by subsequent higher fertility and hence leads to suppressed subsequent fertility (about two
thirds of a percentage point below a control annual fertility probability of 3.9%). Far from it being
the case that home ownership encourages local political participation, we see a slight disruptive
effect and an overall insignificant suppression of voting among lottery winners. Moving appears
to have no effect on schooling enrollment (either public K-12 or universities we observe) in thiscontext.
In the final section of the paper we try to unpack the explanation for these relatively muted
overall results. Our analysis suggests that two features of the program and context may be particularly implicated: first, the provision of a subsidized mortgage requires eligibility requirements
3

For example, Kling et al. (2005) finds disruptive short-term effects of MTO on the schooling of adolescent boys, andGay (2012) shows that MTO depresses voting among adults as a result of dislocation effects.

3around ability pay that screen out the poorest potential applicants, meaning that the study sample
is lower-middle income but contains few individuals from the poorest deciles of the local income
distribution. Examination of heterogeneity by baseline income levels suggests that this feature of
the targeting limits overall impacts. Secondly, place-based mobility programs work precisely because they shift individuals across an urban gradient whose slope is implicitly determined by the
degree of inequality in the city in which they operate. Ironically for Latin America—a region inwhich inequality is pervasive—Uruguay generally and Montevideo specifically are relatively egalitarian. The intersection of the screening criteria and the urban geography of Uruguay result ina program for which changes in neighborhood quality are relatively modest. In one importantdimension, namely local violent crime rates, the intervention actually moves households towards
neighborhoods with slightly worse outcomes. The implication is that geographic mobility programs
will be a particularly effective tool in places where inequality is a severe problem to begin with.
The intersection of targeting rules and context (Korpi and Palme, 1998) simply does not feature theprimitive inequality necessary to make moving a household across the city a powerful intervention.

2

Design2.1

The Compra de Vivienda Nueva Program

In 2005, the Uruguayan government developed the Compra de Vivienda Nueva (CVN) program withan eye to promoting home ownership while providing housing opportunities in central urban areas.
The concern at that time was that the conventional approach of building housing in peripheral
areas simply reproduced segregation rather than addressing the structural problems that reduce
the quality of life in marginal communities. Consequently the design of CVN focuses on bringing
the marginalized poor into the geographic center of the city, and on providing a pathway to homeownership with the idea that the stability and enfranchisement from the title provides a more
durable pathway to the middle class.
The program was targeted at families with at least one child under 18 years old or one disabled
member. The maximum monthly income a family may have varies with family size, but it is 6.75
minimum wages (2,745 USD) for a family of four. Eligibility was restricted to families that havesufficient savings to make an initial down payment of 8-10% of the market value of a new apartment
and sufficient income to afford the monthly mortgage payments. To prove they will be able to afford
the monthly payments, families needed to demonstrate that they had a monthly income of between
557 and 1,336 USD in Montevideo, or between 523 and 2,092 USD in the rest of the country. As
we might expect from this mixture of progressive targeting and minimum payment requirements,
wealthy households are screened out and yet few of the very poorest households are included. (Seefigure A.2). The median applicant comes from the third income decile; 12% of applicants are fromthe poorest decile and we observe no applicants with income above the city median (and only 6.75%

4

of applicants from the fourth decile). According to our estimation, between 2010 and 2016, thetarget population of households that met the income requirements and had at least one minor childincluded around thirty percent of Uruguay´s total population.
Monthly payments are calculated based on families’ financial capacity, but never exceed 25% of
the family´s income. The mortgage is fixed-rate and has a maximum 25-year term. The quantity ofthe subsidy therefore varies by household and will be larger for a) larger families and b) householdswith lower incomes.4 The average winner of a lottery was purchasing a house worth $64,000, wasasked to make a 10% down payment from their own savings, and would have had an unsubsidizedmortgage payment of $337 per month. The payments were subsidized by 76%, leaving the average
winner with a post-subsidy mortgage payment of $80 per month on a loan averaging 15 years. The
average total subsidy received for a winning household is $44,000, representing a very substantial
investment in a single household and raising the bar for the scale of impacts we would hope to see
in a cost-effectiveness sense.
The program experienced substantial excess demand, and so access to the CVN units and theassociated subsidized mortgages was randomly assigned by lottery. When the units in a new building became available, the Housing Ministry (MVOTMA) put out a call for applications, specifying
the location of the building and the number of bedrooms in the apartments. The number of units
in each call for applications varied depending on the number of units of a given size in the newbuilding. Interested families were then invited to apply. After evaluating whether all registeredfamilies complied with the program guidelines, MVOTMA conducted a public lottery among eligible applicants, by drawing pieces of paper from a bowl with all participants invited to be present
in person. If a given family did not win the lottery for a given call, it could register again for
subsequent housing lotteries.
Between 2008 and 2016 the CVN program distributed 1,617 units; 776 of which were locatedin Montevideo and the remainder in the rest of the country. In this period, there were 345 calls
and 1,860 apartment units were assigned. 187 of the calls were ‘competitive’, defined as being a)lotteries that had more than one participant, and b) lotteries in which not all participants won.
1,248 apartment units were assigned in these competitive lotteries. Figure A.3 shows the locationof all the apartment buildings that were constructed under CVN. Panel A shows the complete
location of all buildings in the city of Montevideo, while Panel B provides an example, for a single
lottery, of the locations of the individuals at the time of application and the location of the building
they would move to if they won. Table A.1 provides summary statistics on the change in living
conditions experienced by those who won the lotteries; the average number of bedrooms increases
by .5, the share living with another family falls from 27% to 0, and the share with formal housing
rises from 45% to 100%.
Analysis of the pooled lotteries is complicated by two forms of non-compliance. First, winners
4

The full set of requirements can be found at https://www.mvotma.gub.uy/programas-permanentes-porpostulacion/comprar/vivienda-construida.

5may decide not to participate in the program after winning the lottery. This is rare but has
happened in 1.7% of cases; this is a typical form of non-compliance and can be handled simply by
estimating an Intention to Treat Effect ignoring this source of non-compliance. Second, households
who lost in prior lotteries are free to join subsequent ones; 35% of the households in our data
appear in more than one lottery and 3% appear in more than three. Figure A.4 shows both forms
of non-compliance; for every lottery year the non-compliance in the treatment is below 5%, and thesubsequent re-treatment rate among initial controls is 20% for the first cohort, 10% for the next
three, and then drops below 5% for cohorts lotteried after 2012.5 We account for this issue using
two strategies borrowed from the literature on US school lotteries, which share the same issue.
First, we calculate the equivalent of an Intention to Treat (ITT) effect by using only the outcomeof the first lottery regardless of how many subsequent lotteries are enrolled in. This estimate is
structurally biased towards zero and so provides a lower bound on the absolute magnitude of thetrue treatment effect (Cullen et al., 2006). Second, we can instrument for winning any given lottery
with the outcome of the first (following Abdulkadiroğlu et al. (2011)), which effectively inflates the
ITT above to provide an estimate of the Local Average Treatment Effect (LATE).

2.2

Data and Outcomes

The initial data for the project consists of the application information that was filed with CVN by
beneficiaries in order to be eligible to participate in a lottery. The average age of the adults in eachapplicant household was 36 years old. 59.4 percent of the families that applied to the program wererenters while the remainder lived under various informal non-ownership arrangements (e.g. living
in a relative´s house).
The mapping of national ID numbers to government databases allow us to define five primary
outcomes for the study. First, we can measure formal employment by seeing whether workingaged adults are covered by the national worker health insurance scheme (Sistema Nacional Integradode Salud, or SNIS; employers are required to register employees under SNIS).6 This variable isobserved from 2010-2020 and is defined for all adults over the age of 18.
Second, we examine voting behavior by matching adults of voting age to the registry ofparticipation in Montevideo’s local council and participatory budget elections in 2008, 2011, 2013
and 2016. Our measure records whether an individual voted either on any participatory local
budget proposals, or in a local council election. Voting in these local elections is voluntary for all
residents of Montevideo sixteen years and older (while voting in national elections is mandatory),
and the issues on which they are voting are highly localized public good investments (parks, schools,
street paving, sports fields, and so on). Participation in these elections is therefore an interesting
metric of engagement with community issues.
5
6

Figure A.5 shows how the non-compliance changes across subsequent years for each initial lottery year.
SNIS covers the whole household of any formally registered employee, and so this variable effectively measures ‘any
household member employed’ and will not be affected by a second adult gaining formal employment.

6

Third, we measure female fertility by matching women aged 16-40 to data from the national
birth registry, which includes the ID of the mother. This allows us to measure the probability ofbirth in any year or the cumulative number of births over any interval. This outcome is observed
from 2010-2016.
Fourth, we measure public school enrollment by matching all children aged 6-19 in lottery
households to the enrollment records of the public primary and secondary school system. However,
only 80% of children in Uruguay attend public schools, so this measure is imperfect in that it
would, for example, measure a child moving from a public to a private school as dropping out.
Nonetheless we expect this to be a strong measure of enrollment in this context, given that eligible
households are low income by definition and hence more likely to rely on the public school system.
This outcome is observed from 2013-2020.
Finally, we measure tertiary enrollment by matching college-age youth to the enrollment
records of the two major universities in the capital of Montevideo, Universidad de la República andUniversidad Católica del Urugauy. These are the two most elite universities in the country, andso represent a reasonable measure of treatment effects on access to high-quality tertiary education.
This outcome is observed only in 2016; we define this outcome for all youth aged less than 19 at
the time of lottery and more than 18 in 2016.
Because we have the GPS locations of the household of residence at the time of application as
well as the location of the apartment they would move to, we can also define a number of covariatesthat describe the heterogeneity of the move households undertake if they win. These include thedifference in the property prices across old and new neighborhoods as well as the difference inhomicide rates.7 These differences can be calculated both for winners and losers of the lottery(e.g., the change they would have experienced if they won) and so can be used as interaction
variables for a standard experimental analysis of impact heterogeneity. We lack real estate pricedata for the entire country and we have homicide data only for the city of Montevideo, meaningthat we can examine only 182 and 124 lotteries, respectively, when we interact with these covariates
to look for signs of heterogeneity.
Table 1 provides summary statistics for our core data, as well as illustrating the balance between
treatment and control. It includes three types of variables; in the top panel it uses the information
on households that is included on the program application forms. In the middle panel we examine
the pre-treatment outcomes from the institutional data used later in the paper. In the bottom
panel we construct metrics of the change in neighborhood characteristics that would occur if theindividual won the lottery (post-pre) and compare those who will win to those who will lose. The
table presents 22 comparisons and finds one to be significantly different at the 95% level, as wewould expect by random chance. While the eventual winners are 5.5 pp more likely to be in rentals
at the time of application, critically all of the outcome variables appear to be well-balanced. While7

We have also examined other dimensions such as physical distance travelled and differences in political participationand found no evidence of heterogeneity, so they are omitted from our final analysis.

7the eventual winners would move to higher-theft neighborhoods than losers, the effects on the othermetrics of crime (homicide, assault, and IPV) all move in the opposite direction and so there does
not appear to be any systematic difference in the types of neighborhood changes that would be
experienced by winners and losers. This is particularly important as the researchers did not control
the lottery mechanism.
Table 1: Summary Statistics and Balance

Information from Application Forms
Monthly Family Formal Income
Any Formal Income
Two Titleholders
Minor At Lottery
Number of Minors At Lottery
Origin: House
Origin: Rental
Origin: Number of Bedrooms
Origin: Had Restroom
Origin: Under Construction
Pre-Treatment Outcomes
Never Unemployed
Never Missed School
Voted
Fertility
University
Neighborhood Characteristics, Post-Pre
Homicide Change Z Score
Theft Change Z Score
Assault Change Z Score
IPV Change Z Score
2004 Voter Turnout Change Z Score
2009 Voter Turnout Change Z Score
2014 Voter Turnout Change Z Score

Control

Treatment

Difference

23,218.88(8,511.75)
0.16(0.37)
0.57(0.50)
0.43(0.49)
1.41(0.66)
0.44(0.50)
0.60(0.49)
1.95(0.82)
0.81(0.39)
0.25(0.43)

21,133.41(8,230.81)
0.15(0.36)
0.60(0.49)
0.42(0.49)
1.40(0.65)
0.44(0.50)
0.54(0.50)
1.95(0.81)
0.81(0.39)
0.19(0.39)-532.075(363.818)-.001(.019).005(.025).001(.006).005(.023).011(.023)-.055**(.024).005(.036)
-.019
(.02)
.004
(.02)

0.62
(0.49)
0.11(0.31)
0.05(0.22)
0.11(0.32)
0.41(0.49)

0.59(0.49)
0.11(0.32)
0.05(0.22)
0.11(0.32)
0.42(0.49)-.034(.029)-.028(.026)
-.001
(.01)
.013
(.02)
.001
(.029)

0.00(1.00)-0.01(1.08)-0.01(1.08)-0.00(1.08)-0.02(0.99)-0.03(0.98)-0.04(0.97)

0.02(0.95)
0.00(1.13)-0.00(1.14)-0.02(1.14)
0.01(0.97)
0.04(0.96)
0.04(0.95).025(.033).02(.036).017(.036)-.002(.038).024(.056).065(.055).058(.051)

Notes: Table presents tests of balance for lottery winners versus losers. Panel A examines household data from the application forms, Panel B
uses the institutional data to examine pre-lottery outcomes, and Panel C looks at the change in neighborhood characteristics that would havebeen induced by winning the lottery. Difference column shows the beta on a treatment indicator representing the lottery outcome of a household
the first time it is observed. Standard errors in parentheses, weighted means and standard deviations reported. * p < 0.10, ** p < 0.05, ***p < 0.01.

8

3

Results

3.1

Intention to Treat Estimation

Our first approach to estimating the impact of winning a CVN lottery is to use an Intention toTreat, cumulating outcomes across all post-lottery years up to the last observation possible foreach outcome and for each lottery cohort. To avoid endogeneity from re-entry into subsequent
lotteries for losers, we retain the treatment status assigned in the first lottery entered in that year.
To preserve the balance of subsequent experiments we include individuals as many times as thenumber of lotteries they appear in during that year, but we use weights to remove the undue
influence of these repeat observations, as well as clustering standard errors at the household level.
We also utilize Horvitz-Thompson experimental inverse propensity weights based on the successrates in each lottery (these weights make each of the two potential outcomes equally important
despite the fact that lotteries rarely assigned close to 50% of subjects to treatment); the productof these two weights is used in analysis. The confluence of these issues means that for a given
household, the ‘first lottery’ treatment variable, the cumulated outcome, and the weights can allvary depending on the lottery cohort being considered.
We observe the post-treatment outcome Yitc for each household i, each outcome time periodt, and each lottery c. This outcome is explained with a binary indicator Ticp which indicates
whether a household present in lottery c was assigned to the treatment in that household’s firstlottery within pool p (where pool refers to the group of lottery cohorts and their outcomes being
aggregated together in a given analysis). To improve statistical power the regression includes abattery of covariates taken from the application data βXic (formal and informal income, numberof individuals who would be on the title, number of minors in the household, quality of home andtype of tenancy) and a set of indicator variables for each lottery (the randomization groups) αc .
Following Cullen et al. (2006), the ANCOVA estimate of the ITT regression is then:Yitc = αc + δTicp + βXic + ρYi0c + itcp(1)

The results of this estimation are presented in Table 2. Every coefficient in the table is from adifferent regression; the different samples lotteried in each year are in the rows, and the outcomes in
the columns. The bottom row pools together all of the samples and provides the highest-powered
test on the aggregate sample. With the exception of the ‘University’ outcome, which we only observein 2016, all outcomes are defined as the cumulative average across all observed post-treatment years.
Each outcome is only defined for the relevant group of individuals given in Section 2.2.
Beginning with the pooled results, we see statistically significant decreases in fertility andincreases in employment arising from the treatment.8 The fertility effect appears consistent with
8

The row at the bottom of Table 2 gives the post-lottery control mean and so is different from Table 1 which gives
the pre-exposure mean.

9

Table 2: ITT Estimates by Lottery Year

(1)
Employment, 09-21(2)
Voting, 08-16(3)
Fertility, 09-16(4)
Schooling, 09-21(5)
University, 20162009 Lottery Cohort.0012(.023)[3,296]-.0161(.01)[3,672].0018(.006)[1,745]-.0103(.044)[1,727]-.1472***(.052)[812]

2010 Lottery Cohort.015(.027)[640]-.0141**(.006)[738]-.0009(.007)[369].0433(.049)[384].2432***(.084)[196]

2011 Lottery Cohort.0111(.017)[3,523]-.0069(.008)[3,854]-.0052(.006)[2,018].0516**(.025)[2,048].0159(.051)[899]

2012 Lottery Cohort.0057(.016)[4,152].0094(.008)[4,563].0123(.009)[2,338].0139(.028)[2,302]-.06(.057)[931]

2013 Lottery Cohort.0477(.031)[1,023]-.0243***(.009)[1,142]-.0018(.012)
[608]

.0249
(.05)
[600]

.1909***(.073)[213]

2014 Lottery Cohort.1147***(.027)[1,026]

.0188
(.03)
[1,129]-.0391***(.009)[589]-.003(.045)[533].295***(.1)[173]

2015 Lottery Cohort.0303(.022)[1,483]-.035***(.01)[1,628]-.0319***(.008)[830]-.0476(.04)[755].1659*(.099)[229]

2016 Lottery Cohort-.1027(.089)[253]-.1126***(.035)[280].0034(.024)[163].1369**(.069)[128].7206(.647)[25]

Pooled Sample.0217**(.01)[15,502]0.53-.0063(.005)[17,006]
0.05-.0069*(.004)[8,755]0.04-.002(.017)[7,933]0.40-.0013(.03)[3,478]0.42

Pooled Average

Notes: Table presents Intention to Treat impacts of the winning status in the first lottery entered for the cohort
lotteried in each. Outcome is cumulated across all available post-lottery years. Every coefficient is from a separate
regression. Regressions include fixed effects for lottery, are weighted using randomization inverse propensity
weights. The Pooled Sample result in the final row includes all lottery years. Note that the number of observations
within a column will not sum to the pooled sample due to re-entry. Employment: Avg Number of Years without
gap in Employment, 09-21. Voting: Avg Participation Across Post-Treatment Years , 08-16. Fertility: Avg Births
Across Post-Treatment Years, 09-16. Schooling: Avg Number of Years without gap in Schooling, 09-21. University:
Attended in 2016. Standard errors in parentheses, and number of outcomes per regression in hard brackets; *p < 0.10, ** p < 0.05, *** p < 0.01.

10disruption arising from the move; the negative coefficients appear only shortly after the lottery(2014 and 2015 lotteries for 2016 outcomes). However, both coefficients are small in absolutemagnitude; the fertility effect implies a decrease in fertility of less than one percentage point,
and the employment effect of .02 would indicate one more week of formal employment over theentire post-treatment period. So even where the pooled effects are significant they are not large.
Voting similarly displays an apparent disruption effect with political participation being lower
for those who have relocated recently, but the pooled effect is insignificant. The two schooling
outcomes have years in which we see a significant positive effect, but the pooled impact is verysmall and insignificant. Hence while the ITT approach provides some glimmers of benefits in termsof employment and decreased fertility (as might be expected if female employment improves), notransformative benefits have occurred.

3.2

Event Study Estimation

The ITT results suggest the possibility of disruption effects closer to the time of lottery, but thepooling of samples and years inherent in that analysis structure may mask these effects. To gain amore fine-grained view on the dynamics of outcomes around the time of the lotteries, we can pool
together all years and all observations (again repeating and de-weighting individuals participatingin more than one lottery) and for each year and lottery cohort define the leads and lags of treatment.
Along with fixed effects for lottery cohort and year of observation, this then gives an experimental
estimate of the time path of treatment effects. The results of this exercise are presented in Figure
1 for the four outcomes that are observed each year and hence amenable to this form of analysis.
Schooling displays no clear temporal pattern, and employment appears to rise slightly in the yearof the move and to stay elevated in a manner that is similar across years (but significant only whenpooled, as we saw in the prior table). Fertility and particularly Voting both display some sense of
disruption, with voting weakly disrupted in lags 1-3, and fertility somewhat below trend in the twoyears after the move. Nonetheless, the overall impacts are sufficiently muted as to be undetectablein this year-by-year format, and must be pooled to achieve statistical significance.

3.3

Local Average Treatment Effect Estimation

A related way of summarizing impacts is to ask whether the duration of exposure to the treatment of
a new house alters outcomes. An attractive way of summarizing the effects of duration of exposure
is to estimate an IV/LATE equation pool refers to the group of lottery enous) outcome of the firstlottery entered, following Abdulkadiroğlu et al. (2011). We now include each household only once,
while continuing to define the sample as the universe of households ever exposed to a competitive
lottery. For each outcome we always employ the full range of available years for calculating thepost-exposure average, and for each lottery year we pool all individuals who had been lotteried prior
to that year. This means that once we are examining the 2016 lottery (our last) we are effectively

11Figure 1: Event Study Treatment Effects

The figure shows the first lead and the lags of treatment across main study outcomes that are observable as panels. The analyses pool all lottery cohorts and present point estimates and confidence
intervals for post-treatment outcome years.

estimating the pooled regression that uses the maximum available sample size and the maximum
available number of post-treatment years.
The endogenous variable for the LATE estimation is Ditp , the duration for which household i has
been treated as of time t in pool p. We can instrument for the duration with the interaction between
the lottery fixed effects and whether the household won its first lottery in that pool. Treatment in
subsequent lotteries is ignored in the instrument but included in the duration of treatment Ditp , so
the coefficient δL gives the LATE estimate of one additional year of actually receiving the program.
The Two State Least Squares estimate is then:Ditp = αc + γc (αc ∗ Ticp ) + νXic + ψYi0c + µitcp

12

(2)

Yitc = αc + δL D̂itp + βXic + ρYi0c + itcp(3)This analysis is weighted using only the lottery treatment percentage-based inverse propensity
weights, and standard errors are clustered at the household level.
Table 3: LATE Estimates by Years Treated(1)
Employment, 09-21
2009-2010 Cohorts(2)
Voting, 08-16(3)
Fertility, 09-16-.0085*(.0049)[4,410].0001(.0029)[2,114](4)Schooling, 09-21(5)
University, 2016-.0598**(.0257)[1,008]

2009-2011 Cohorts.0125**(.0062)[7,565]-.0053*(.003)[8,264]-.001(.0018)[4,136].0061(.011)[3,857]-.0203(.0164)[1,907]

2009-2012 Cohorts.0086**(.0043)[11,717]-.0036*(.0019)[12,827]-.0006(.0014)[6,496].0034(.0074)[5,987]-.0123(.0118)[2,838]

2009-2013 Cohorts.0063*(.0033)[12,740]-.0025*(.0014)[13,969]-.0006(.0011)[7,111].0035(.0055)[6,559]-.0084(.009)[3,051]

2009-2014 Cohorts.0054**(.0026)[13,766]-.0016(.0012)[15,098]-.0009(.0009)[7,723].0031(.0043)[7,072]-.0057(.0071)[3,224]2009-2015 Cohorts.0047**(.0022)[15,249]-.0015(.0009)[16,726]-.0009(.0007)[8,586].0019(.0036)[7,805]-.0039(.0059)[3,453]2009-2016 Cohorts.0041**(.0018)[15,502]-.0012(.0008)[17,006]-.0009(.0006)[8,755].0014(.003)[7,933]-.0027(.005)[3,478]Notes: Analysis is a LATE instrumenting for years treated in 2016 with the outcome of the first lottery a household
participated in within each observation window. Each coefficient is the output from a separate regression,
cumulating across all cohorts that had been lotteried prior to a given year. Regressions include fixed effects forlottery, are weighted using randomization inverse propensity weights. Standard errors clustered at the household
level are in parentheses, and number of observations for each analysis is in hard brackets. * p¡0.10 ** p¡0.05 ***p¡0.01.

Results are presented in Table 3. Again every coefficient is from a different regression, but here
since the rows include all individuals lotteried prior to the named year, the sample cumulates as
we move down and the 2016 row contains all available observations. Despite posing the impact
question in terms of years of exposure to the move, the takeaway from this table is quite similar to13

the ITT Table 2. One additional year of treatment increases the employment rate by .4 pp, but inthe cumulated regressions in the bottom row none of the other outcomes display treatment effects
on number of years treated. As with the ITT results, the employment effect is significant but small
in absolute magnitude.

3.4

Heterogeneous Treatment Effects

We can contextualize the muted impacts found in this study through two types of heterogeneity
analysis. The first of these is the standard interaction analysis, as described in our pre-analysis
plan. Relevant heterogeneity may exist at the household level (the income of the household, or thepresence of a female household head), the individual level (age at the time of lottery), or acrossthe neighborhood change induced by a lottery win (measured either in terms of property prices
or of changes in crime rates). Accordingly, in Appendix tables A.2 through A.6 we sequentiallyanalyze the five primary outcomes for the study, with these dimensions of heterogeneity examined
separately in the columns of each table. The specification uses the same cumulative ITT approachas in Table 2, including all observations for whom we observe the heterogeneity covariate at thetime of application.
Analysis by the individual- and household-level attributes is straightforward; the counterfactual
neighborhood-level changes are somewhat more non-standard and are only enabled by the fact thatfor all control households we see the place they would have moved to had they won. That is, we
can take the value of the covariate Zi at the location of the household at the time of application,
and Zk at the location to which they would move if they won the lottery, and calculate dikc , thedistance between these two values for household i in lottery group c and lottery j. The analysis ofheterogeneity is then conducted via the following regression:
Yitc = αc + δTicp + βXic + χdikc + τ (Ticp dikc ) + itcp(4)

The coefficient τ measures the extent to which the impact of the treatment is heterogeneous
across distance dikc , and now δ measures a kind of ‘pure’ impact of home ownership that would
occur if there were no change at all for the beneficiaries across the distance dimension included in
the regression. We can include multiple distance interactions simultaneously in order to understandthe differential impact of one kind of distance holding others constant.
Table A.2 examines employment, the most straightforward economic outcome, and finds heterogeneity that helps to contextualize the overall results of the study. In it, we find that householdswith the lowest initial incomes are the ones seeing the largest employment boost from the program.
Similarly, female headed households see more than double the increase in employment as thosewith male heads. These heterogeneity results suggest that the program would have had larger
employment impacts if it had been targeted at poorer individuals, meaning that there is a tension
between the economic requirements of a mortgage-based poverty alleviation program and its over-14

all effectiveness. The remaining heterogeneity tables typically have a negative coefficient on theincome interaction but are not significant.
The final column of Table A.2 examines the change in crime rates across neighborhoods. It
uncovers the surprising result that moving to a higher-crime neighborhood actually increases employment rates. A deeper examination of this issue helps to contextualize our study and how thisplace-based program may have differed from its better-known antecedents in the US. Figure 2 plots
the distribution of homicide rates for the prior neighborhoods and the new locations in Montevideo(Panel A) and then in Boston, Chicago, and Los Angeles (Panel B). Two facts are striking fromthese pictures. First, there is substantially more inequality in crime rates within the US cities thanthere is in Montevideo. Partially this maps to higher overall levels of economic inequality in the US(the Gini coefficient of census-tract poverty rates in Montevideo is .28, while it is .39 in Chicago,.32 in Boston, and .35 in Los Angeles), and partly to lower overall levels of crime (homicides per
thousand are .12 in Montevideo, and average .2 in the MTO cities).
Figure 2: Comparing the Change in Census Tract Homicide Distribution, CVN vs. MTO

A

B2.0

Montevideo

3

BostonChicagoLos Angeles

densitydensity

1.5
2

1

1.0
0.5

0

0.0
0.0

0.5

1.0

1.5

2.0

0.0 0.5 1.0 1.5 2.0 0.0 0.5 1.0 1.5 2.0 0.0 0.5 1.0 1.5 2.0

Homicide Rate
typeafter cvn

Homicide Rate
type

before cvn

after mto

before mto

The figures compare the distribution of the homicide rate of the neighborhoods where program beneficiaries
were located before and after the interventions for CVN (Panel A) and for MTO (Panel B). For MTO, we
identify the relevant census tracts through the program guidelines. The “pre” distribution includes tracts withmore than 40% of their population under the poverty line; the “post” distribution includes tracts with less than
10% of their population under the poverty line. (Both required criteria for eligibility). Data on poverty andcrime at the census tract level for the 1990s comes from Peterson and Krivo (2010).

The more striking feature of this picture, however, is that in our study individuals are actually
moving to higher-crime neighborhoods on average, while MTO results in dramatic decreases in
exposure to local crime. Kingsley and Pettit (2008) find that MTO experimental movers saw a
72% reduction in neighborhood violent crime rate (from 40 per 1k pop to 11) as a result of theirfirst move. For Montevideo, the overall change is a 7% increase in crime [From 55.6 to 59.8 ]. In

15

fact, the median CVN winner moved to a census tract with a homicide rate that was 27% higher
than where they previously lived. How can this be the case? The answer lies in the different urban
geography of Montevideo, in which the peripheral neighborhoods from which individuals moved
are typically relatively safe, towards the city center where crime rates are higher. Indeed while thecorrelation between the poverty rate and the homicide rate in the MTO cities is .45, in Montevideo
it is only .1. Consequently two core features of urban geography appear to play important roles indetermining the outcome of this program: first, the relatively muted gradient of inequality acrossneighborhoods limited the extent to which relocation could achieve a transformative effect, andsecondly movements that were positive in economic space showed muted improvements (or evendeterioration) in terms of the level of crime to which winners were exposed.

4

Conclusion

Place-based programs have an impact by improving outcomes for those whose counterfactual outcomes would have been poor. Our results emphasize two dimensions of this problem. First, theyneed to be enrolling and treating individuals who would have struggled in the absence of the intervention. Our results suggest that the most economically deprived households gained most interms of employment from moving to wealthier neighborhoods, but the home purchase/mortgage
requirement in the program means that relatively few of these neediest households received theprogram. Hence the intention to treat of this intervention appears to be limited by the fact thatthe marginal treatment effects for many of the wealthier individuals were modest. This may suggest
that, the independent benefits of home ownership notwithstanding, the income bar imposed by theequity purchase dimension of the design limited overall impacts, and such programs may do betterto focus on rental subsidies that can be more easily targeted at the neediest households.
Secondly, to improve outcomes by moving an individual across space these programs fundamentally rely on the degree of spatial inequality in the cities in which they operate. Ironically for Latin
America, long one of the most unequal regions in the world, this program worked in a country
that has limited overall inequality, and in which the neighborhoods with the greatest economic
opportunity also have higher crime. The policy implication is that place-based programs induce atreatment effect proportional to the spatial gradient across which individuals can be moved inside
a city, and hence will be most effective in urban areas that suffer from high inequality to begin
with.

16

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Barnhardt, Sharon, Erica Field, and Rohini Pande, “Moving to opportunity or isolation?
network effects of a randomized housing lottery in urban india,” American Economic Journal:
Applied Economics, 2017, 9 (1), 1–32.
Blum, Terry C and Paul William Kingston, “Homeownership and social attachment,” Sociological Perspectives, 1984, 27 (2), 159–180.
Chetty, Raj, Nathaniel Hendren, and Lawrence F Katz, “The effects of exposure to better neighborhoods on children: New evidence from the Moving to Opportunity experiment,”
American Economic Review, 2016, 106 (4), 855–902.
Clampet-Lundquist, Susan and Douglas S Massey, “Neighborhood effects on economic selfsufficiency: A reconsideration of the Moving to Opportunity experiment,” American Journal of
Sociology, 2008, 114 (1), 107–143.
Cox, Kevin R, “Housing tenure and neighborhood activism,” Urban Affairs Quarterly, 1982, 18(1), 107–129.
Cullen, Julie Berry, Brian A Jacob, and Steven Levitt, “The effect of school choice onparticipants: Evidence from randomized lotteries,” Econometrica, 2006, 74 (5), 1191–1230.
Franklin, Simon, “The demand for government housing: Evidence from lotteries for 200,000
homes in Ethiopia,” Work. Pap., London Sch. Econ., London, 2019.
Galiani, Sebastian and Ernesto Schargrodsky, “Property rights for the poor: Effects of land
titling,” Journal of Public Economics, 2010, 94 (9-10), 700–729.
Gay, Claudine, “Moving to opportunity: The political effects of a housing mobility experiment,”
Urban Affairs Review, 2012, 48 (2), 147–179.
Jacob, Brian A and Jens Ludwig, “The effects of housing assistance on labor supply: Evidence
from a voucher lottery,” American Economic Review, 2012, 102 (1), 272–304.
Katz, Lawrence F, Jeffrey R Kling, and Jeffrey B Liebman, “Moving to opportunity in
Boston: Early results of a randomized mobility experiment,” The Quarterly Journal of Economics, 2001, 116 (2), 607–654.
Kingsley, G Thomas and Kathryn LS Pettit, Have MTO families lost access to opportunity
neighborhoods over time?, Urban institute Washington, DC, 2008.
Kling, Jeffrey R, Jens Ludwig, and Lawrence F Katz, “Neighborhood effects on crimefor female and male youth: Evidence from a randomized housing voucher experiment,” The
Quarterly Journal of Economics, 2005, 120 (1), 87–130.

17

Korpi, Walter and Joakim Palme, “The paradox of redistribution and strategies of equality:
Welfare state institutions, inequality, and poverty in the Western countries,” American sociological review, 1998, pp. 661–687.
Kumar, Tanu, “Home Price Subsidies Increase Local-Level Political Participation in Urban India,”
The Journal of Politics, 2022, 84 (2), 000–000.
Leape, Jonathan Hoagland, “Winning the housing lottery in Rio de Janeiro: curse or cure?”
PhD dissertation, Massachusetts Institute of Technology 2020.
Ludwig, Jens, Greg J Duncan, Lisa A Gennetian, Lawrence F Katz, Ronald C Kessler,
Jeffrey R Kling, and Lisa Sanbonmatsu, “Long-term neighborhood effects on low-income
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226–31.
, Jeffrey B Liebman, Jeffrey R Kling, Greg J Duncan, Lawrence F Katz, Ronald C
Kessler, and Lisa Sanbonmatsu, “What can we learn about neighborhood effects from themoving to opportunity experiment?,” American Journal of Sociology, 2008, 114 (1), 144–188.
McCabe, Brian J, “Are homeowners better citizens? Homeownership and community participation in the United States,” Social Forces, 2013, 91 (3), 929–954.
Peterson, Ruth D and Lauren J Krivo, Divergent social worlds: Neighborhood crime and the
racial-spatial divide, Russell Sage Foundation, 2010.
Rosenbaum, James E, “Changing the geography of opportunity by expanding residential choice:Lessons from the Gautreaux program,” Housing Policy Debate, 1995, 6 (1), 231–269.

18

Appendix A

Online Appendix

Figure A.1: Share of Applicants by Deciles of Montevideo’s Income Distribution

Share of Participants in Decile of Income Distribution

0.3

0.2

0.1

0.0
2.5

5.0

7.5

10.0

DecileData on Montevideo’s income distribution comes from the Instituto Nacional de Estadı́stica.

Figure A.2: Applicant Pool and City-Wide Income Distributions, by Year2008
0.00008

N=10350.00006

2009

2010

N=530

N=277

2011

2012

N=2314

N=16400.00004

density

0.000020.00000
2013
0.00008
0.00006

2014

2015

2016

0

N=760

N=340

N=845

N=169

50000100000
1500000

50000100000
1500000

50000100000
1500000

50000100000
15000050000100000
1500000.00004
0.000020.00000
0income
PDF of applicants in red; city in black. vertical line marks median of city-wide income distribution. Data on
Montevideo’s income distribution comes from the Instituto Nacional de Estadı́stica.

19

Table A.1: Change in Living Conditions
Pre-Treatment
Mean

Post-Treatment
Mean

Difference

Housing Quality
Has Own Bathroom

0.84

1

Has Own Kitchen

0.84

1

Connected to Water Network

0.99

1

Connected to Energy Network

0.97

1

Connected to Sewage Network

0.83

1

Housing Quality Index

8.86

10

0.16
(0.01)
0.16(0.01)
0.01(0.01)
0.02(0.01)
0.17(0.01)
1.14(0.03)

Housing Size
Number of Bedrooms

1.96

2.52

0.56
(0.03)

Housing Stability
Shares Housing with Another Family

0.27

0

Formal Housing Arrangement

0.45

1

-0.27
(0.01)
0.55(0.01)

Neighborhood Quality
Price of Square Meter (Uruguayan Pesos)

3,828

4,492

664
(155)

The table describes the housing characteristics for winning families (N = 1, 255) at the time of application and after treatment. Data on housing quality and housing stability was self-reported by families
at the time of application to the program. To obtain data on neighborhood quality, we geocoded applicants’ addresses as well as the addresses of the apartment buildings where the applicants relocatedand used official data on housing prices to calculate the mean price of square meter in the relevantneighborhood.

20Figure A.3: Location of Montevideo Apartment Buildings−34.7

LatitudeLatitude

−34.7

−34.8

−34.9

−34.8

−34.9

−56.4

−56.3

−56.2

−56.1

−56.0

−56.3

Longitude

−56.2

−56.1

−56.0

Longitude(a) Study Building Locations in Montevideo(b) Detail of Prior Residences for One Lottery

21

−55.9

As we seek to measure longer-term effects, the interval over which households may havere-entered subsequent lotteries increases and hence the non-compliance in the control
increases. Figure A.4: Two-Sided Non-Compliance by Year

.1
0

.05

Percentage

.15

.2

Two-Sided Non-Compliance, by Year

2008

2010

2012
Year of Lottery

Controls Subsequently Treated

2014

2016

Treatments Withdrawn

The figure shows the over-time evolution of each type of non-compliance. Controls subsequently
treated gives theFor
fractionof analysis,
individuals
lotteriedin eachasyear
whooflosttheir initiallottery
the ITTa cohort
is defined
the sethouseholds
exposedto a but thenapply for a subsequent one. Treatments withdrawn is the fraction of winners in each year who do
specific lottery, and the sample is the universe of households exposed to any lottery by
not occupy the CVN apartment for any reason.
the time of the endline measurement. If a household entered in multiple lotteries it isincluded multiple times in the regression, once for each cohort in which it belongs. For
each household i we observe the post-treatment outcome Yi1 . This outcome is explained

Figure A.5: Differential Non-Compliance and Sample Sizewith a binary indicator Tic which indicates whether a household was assigned to thetreatment in lottery c.
The cross-sectional post-treatment estimator for the ITT, following Cullen et al.
cohort0.10(2006) is then:

COHORT 2009
COHORT 2010

noncompliancesamplesize

6000

Yi1 = α c + δ Tic + β X i 0 + ε ic

(1.1)

COHORT 2011
COHORT 2012
COHORT 2013

For outcomes that are observed
prior to be the first lotteries, we have a baseline
0.05

4000

COHORT 2014

dependent variable and hence can estimate the ANCOVA version of the ITT:COHORT 2016

Yi1 = α c + δ Tic + β X i 0 + ρYi 0 + ε ict

(1.2)
2000

0.00
where X i 0 is a set of baseline household-level
control variables (formal and informal
2010

COHORT 2015

2012

2014

2010

2016

year

2012

2014

2016

year

income, number of individuals who would be on the title, number of minors in the(a) Sample Size Growth

Non-Compliance in the Control Group by Year Cohort
household, quality of home and type of(b)tenancy),Yi 0 is the pre-treatment outcome, andPanel A shows the simple growth in the number of households who have participated in a competitive lottery by
is a setof fixedof
effects
for eachsubsequent
lottery. To lotteries
preserve symmetryof potential
α c theyear. Panel B shows
evolution
re-entering
among losersof firstoutcomes,lotteries for each year.

22Table A.2: Employment Heterogeneity

Treatment
Heterogeneity Dimension
Interaction Term
Control Group Y-Mean
Control Group Het. Mean
Observations
R2(1)
Formal Income(2)
Age at Lottery(3)
Female HH Head

(4)
Property Price Change(5)
Homicide Change

0.0183(0.0112)0.109*(0.0653)-0.0264**(0.0118)

0.0297(0.0309)
0.00212***(0.000543)-0.000219(0.000901)

0.0214**(0.0103)
0.0214***(0.00656)
0.0232**(0.0101)

0.0308***(0.0104)-0.00633(0.00543)-0.0102(0.0105)

0.0422***(0.0119)-0.00442(0.00603)
0.0353***(0.0113)0.5301-0.0213
13,4280.20570.530133.0612
13,4280.20680.5301-0.0151
13,4280.20770.53090.0016
11,5990.2171

0.54360.015910,3470.217923

Notes: Analysis of heterogeneity on the Employment outcome, pooling together all available data using the ITT strategy of Table
2, and including an interaction effect to measure heterogeneous treatment effects. The dimension of heterogeneity is listed in thecolumn title, and the third row provides the measure of heterogeneity. * p¡0.10 ** p¡0.05 *** p¡0.01.

Table A.3: Voting Heterogeneity

Treatment
Heterogeneity Dimension
Interaction Term
Control Group Y-Mean
Control Group Het. Mean
Observations
R2(1)
Formal Income(2)
Age at Lottery(3)
Female HH Head

(4)
Property Price Change(5)
Homicide Change-0.00657(0.00509)
0.0280(0.0221)-0.00278(0.00483)

0.00409(0.00879)
0.000670***(0.000190)-0.000332(0.000275)-0.00651(0.00470)
0.00735*(0.00379)-0.00160(0.00534)-0.00969*(0.00505)-0.00166(0.00290)-0.00338(0.00476)-0.0146**(0.00593)
0.00166(0.00317)-0.00421(0.00549)

0.0492-0.0261
14,7100.09740.049231.0715
14,7100.09840.04920.007914,7100.09780.05120.0053
12,6930.1011

0.05800.0154
11,3190.087424

Notes: Analysis of heterogeneity on the Voting outcome, pooling together all available data using the ITT strategy of Table 2, andincluding an interaction effect to measure heterogeneous treatment effects. The dimension of heterogeneity is listed in the column
title, and the third row provides the measure of heterogeneity. * p¡0.10 ** p¡0.05 *** p¡0.01.

Table A.4: Fertility Heterogeneity

Treatment
Heterogeneity Dimension
Interaction Term
Control Group Y-Mean
Control Group Het. Mean
Observations
R2(1)
Formal Income(2)
Age at Lottery(3)
Female HH Head

(4)
Property Price Change(5)
Homicide Change-0.00811*(0.00415)-0.0140(0.0441)-0.00563(0.00447)-0.0108(0.00763)-0.00235***(0.000268)
0.000136(0.000246)-0.00717*(0.00397)-0.0118***(0.00283)
0.00425(0.00363)-0.00466(0.00415)
0.00238(0.00211)-0.00127(0.00424)-0.00128(0.00504)-0.00223(0.00211)-0.00316(0.00632)

0.0411-0.0587
7,606
0.12540.041129.30077,606
0.14430.04110.18697,606
0.12820.04090.00166,552
0.13770.0398-0.0082
5,835
0.142225

Notes: Analysis of heterogeneity on the Fertility outcome, pooling together all available data using the ITT strategy of Table 2,
and including an interaction effect to measure heterogeneous treatment effects. The dimension of heterogeneity is listed in thecolumn title, and the third row provides the measure of heterogeneity. * p¡0.10 ** p¡0.05 *** p¡0.01.

Table A.5: School Heterogeneity

Treatment
Heterogeneity Dimension
Interaction Term
Control Group Y-Mean
Control Group Het. Mean
Observations
R2(1)
Formal Income(2)
Age at Lottery(3)
Female HH Head

(4)
Property Price Change(5)
Homicide Change-0.00528(0.0181)0.246***(0.0804)-0.0168(0.0182)0.00943(0.0368)-0.0274***(0.00176)-0.00228(0.00372)-0.00284(0.0170)-0.000377(0.0190)0.00531(0.0173)-0.000252(0.0187)
0.00549(0.0103)0.0000918(0.0188)0.00530(0.0224)-0.00735(0.00982)
0.00820(0.0205)

0.4033-0.1165
6,827
0.15990.40338.43816,827
0.24640.40330.13886,827
0.1576

0.3990-0.0089
5,885
0.16570.3850-0.0133
5,211
0.1717

26

Notes: Analysis of heterogeneity on the Schooling outcome, pooling together all available data using the ITT strategy of Table 2,
and including an interaction effect to measure heterogeneous treatment effects. The dimension of heterogeneity is listed in thecolumn title, and the third row provides the measure of heterogeneity. * p¡0.10 ** p¡0.05 *** p¡0.01.

Table A.6: College Heterogeneity

Treatment
Heterogeneity Dimension
Interaction Term
Control Group Y-Mean
Control Group Het. Mean
Observations
R2(1)
Formal Income(2)
Age at Lottery(3)
Female HH Head

(4)
Property Price Change(5)
Homicide Change

0.00643(0.0348)-0.116(0.235)0.0197(0.0354)0.150(0.125)-0.00299(0.00625)-0.00811(0.00652)-0.00348(0.0303)
0.0325(0.0216)0.00247(0.0288)-0.00129(0.0320)-0.0200(0.0185)-0.00365(0.0310)-0.0258(0.0372)
0.0447**(0.0202)-0.0523*(0.0297)

0.4170-0.2208
2,894
0.22010.417018.5633
2,894
0.22170.41700.15112,894
0.22120.42090.01952,5120.24130.45440.00602,168
0.231527

Notes: Analysis of heterogeneity on the College attendance outcome, pooling together all available data using the ITT strategy ofTable 2, and including an interaction effect to measure heterogeneous treatment effects. The dimension of heterogeneity is listed in
the column title, and the third row provides the measure of heterogeneity. * p¡0.10 ** p¡0.05 *** p¡0.01.