Housing Vouchers, Income Shocks, and Crime: Evidence from a Lottery

Jillian Carr*

Vijetha Koppa†

Purdue University

Stephen F. Austin State University

May 2017 Abstract The Housing Choice Voucher Program (Section 8) is the largest federal housing assistance program; it provides in-kind transfers in the form of rent vouchers to low-income populations. This paper examines the effect of such voucher receipt on criminal activity. To overcome bias due to selection into the program, we exploit the exogenous variation in lottery-assigned wait-list positions in order to identify the causal effects of the vouchers. Using administrative arrest records, we find voucher receipt has no effect on the likelihood of all arrests, and arrests for drug and financially motivated crimes, but increases the probability of violent crime arrests. Keywords: Housing Vouchers, Section 8, Crime, Neighborhood Effects, Income Shocks JEL Codes: I38, K42, R23

Department of Economics, Krannert School of Management, Purdue University, 425 W. State Street, West Lafayette, IN 47907. Email: [email protected]. † Department of Economics and Finance, Stephen F. Austin State University, PO Box 13009; SFA Station Nacogdoches, TX 75962. Email: [email protected]. We thank Mr. Mark Thiele, Vice President of the Housing Choice Voucher Program at the Houston Housing Authority, for his support of this research and Mr. Michael Kelsch for providing us the lottery data and patiently answering our questions. We also thank Mr. Jeffery Monk of the Houston Police Department for assistance in obtaining the arrest records. The findings of this paper reflect the views of the authors alone and not of any other organization. We would also like to thank Mark Hoekstra, Jason Lindo, Jonathan Meer, Joanna Lahey, Ben Hansen, and seminar participants at Texas A&M University, and Southern Economic Association Conference for helpful comments. *

1. Introduction The U.S. government has provided housing assistance to families since the mid-twentieth century. Historically, it was in the form of public housing projects, though there has been a shift in the last few decades toward housing voucher programs. The federally-funded Housing Choice Voucher Program provides rent support to about 2.1 million households living in non-government housing, which is around 43% of all households receiving federal rental assistance (Center on Budget and Policy Priorities 2012 and 2013). The program, often simply called “Section 8,” is designed to provide an in-kind transfer to low-income families and individuals and allow them to reside in areas otherwise unaffordable. The program is means-tested, and participating families receive a rent subsidy that is paid directly to their landlords. In this paper, we examine the effect of Section 8 vouchers on crime committed by adult heads of households. Vouchers could affect crime through two major channels: income transfer effects and neighborhood effects. Income transfers can relieve financial pressures that could otherwise cause recipients to seek illicit income. Alternatively, income transfers could also provide the funds or leisure time necessary to participate in illegal activities. Voucher receipt could also affect criminal involvement by changing neighborhood influences. Moving to a better neighborhood could reduce crime via positive peer effects or social norms, or it could increase crime by providing easier and wealthier targets. Understanding the causal effects of housing mobility programs is challenging because individuals select to participate in these programs. Eligible families that opt to use vouchers may also take other steps to better their lives, creating a substantial source of selection bias. Often, Section 8 housing vouchers are given out via randomized lottery because it is not an entitlement program, and there are usually more applicants than vouchers. This random variation in voucher allocation has been relied upon for identification of effects on a host of youth outcomes (Jacob et al. 2015; Jacob et al. 2013; Mills et al. 2006) as well as adult labor market outcomes (Jacob and Ludwig 2012). Other studies of mobility programs rely on randomized social experiments, such as the Moving to Opportunity experiment, or various natural experiments.1

Others have used the Gautreaux Program (a precursor of MTO) (Popkin et al. 1993), random assignment into public housing (Oreopoulos 2003), or Hurricane Katrina (Hussey et al. 2011; Kirk 2012) to study mobility and crime. 1

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The largest body of work studying housing mobility programs has, in fact, been generated by the Moving to Opportunity experiment, often simply called “MTO.” MTO was a social experiment that randomized families living in public housing into either a control group or one of two treatment groups that were offered housing vouchers. Because MTO families were already receiving housing assistance through public housing at the time of the intervention, they did not experience an income effect as large as the one experienced by ordinary Section 8 voucher recipients. For instance, in our sample, the voucher amount is equal to 60% of the household income on average. Results from MTO studies may not be representative of the effects for typical Section 8 participants because such a large income shock is likely to have a profound impact on these adults. Criminal outcomes for voucher recipients have been studied in both the MTO and Section 8 literatures. For juveniles, the MTO literature suggests that both reported behavioral problems and violent crime arrests may be reduced when families receive vouchers (Ludwig et al. 2001; Katz et al. 2001; Kling et al. 2005), but there is also evidence that property crime arrests may actually increase for male youth (Ludwig et al. 2001; Kling et al. 2005). Sciandra et al. (2013) perform a longer run follow-up study of adult outcomes for the juvenile MTO recipients and show that the positive neighborhood changes observed immediately after the intervention diminish over time, as do the increased property crime arrests for males. Ludwig and Kling (2007) analyze the effects of various neighborhood characteristics on adult and juvenile recipients using MTO treatment by site interactions as instruments for new neighborhood attributes. Their results suggest that moving to a new neighborhood that is racially segregated has the largest effect on criminal involvement. Importantly, as MTO recipients, the families in this study were all public housing residents and therefore did not experience an income shock to the same degree as that experienced by families receiving Section 8 vouchers ordinarily. Current research on Section 8 and crime has focused on outcomes for individuals who were juveniles at the time their families received vouchers. Jacob et al. (2015) find little evidence that youth outcomes are affected, and although they do find statistically significant effects on the social cost of crimes committed by these juveniles, the magnitudes are relatively small. While this paper highlights the effects of voucher receipt on the criminality and other behavioral choices of the children in the households, it is difficult to assume that these effects would be the same for adults. The main contribution 2

of this paper is that it is the first to focus on the criminal outcomes of the adult heads of households receiving Section 8 vouchers (through the federal Section 8 Housing Voucher Program, and not through MTO).2 In this paper, we exploit the exogenous variation in randomized wait-list positions assigned using a lottery in order to identify the causal effects of Section 8 vouchers on arrests of adult household heads. The lottery we study was administered by the Houston Housing Authority (HHA). We link the voucher applicants to arrest records from the Houston Police Department (HPD) to determine whether voucher receipt has an effect on arrests for various types of crimes. We estimate the effects using intent-to-treat and two-stage least squares models that are identified using the timing of voucher receipt, which is determined by the randomized lottery. Because the proportion of applicants who eventually receive housing assistance through the program (or “lease-up”) is particularly low in this setting, we also report results for just the group of applicants who do receive assistance through the program (“leasers”).3 To support the assumption that wait-list positions are indeed random and that there are no differences between those who lease-up earlier and those who lease-up later (as required for identification within the leaser sample), we perform empirical tests for differences in pre-lottery characteristics between early and later leasers. The relationships between pre-lottery characteristics and wait-list positions are consistent with wait-list randomization, and the types of individuals who lease-up at different times are no different. We also perform a test for differential attrition between leasers with low and high lottery numbers, and find no evidence of such. Results indicate that arrests for most criminal activities are unchanged, while some actually increase due to voucher receipt. For the leaser population, we find that the probability of being arrested for a violent offense in a quarter increases by 0.069 percentage points (a doubling). Our results highlight a potential unintended consequence of the Section 8 Housing Voucher Program – an increase in arrests for violent crime.

Leech (2013) uses NLSY data to study the relationship between self-reported voucher receipt and selfreported violent altercations for young adult heads of household receiving vouchers. She suggests that selection bias is a methodological shortcoming of her study. She finds that voucher receipt is associated with reduced violent altercations, but that this association is not present in the subsample of black recipients. 3 The lease-up rates are similar across different sub-groups of applicants based on pre-determined characteristics. Since we cannot improve the first stage by narrowing the sample down based on any particular covariate, we instead condition on the fact that an applicant leases-up at some point of time. 2

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There is little evidence that voucher recipients move to better neighborhoods both in our study and in the Section 8 literature. We attribute this increase in arrests to the additional disposable income and leisure time available to voucher recipients that can be used to commit crimes. Both of these mechanisms have been linked to increased illegal activity and negative health outcomes previously (Dobkin and Puller 2007; Riddell and Riddell 2005; Evans and Moore 2011). These effects may be stronger for groups of recipients more susceptible to crime, and we find that the effects are driven by those who had been arrested in the past and by males. 2. Background 2.1

Housing Choice Voucher Program Rules

The Section 8 Housing Voucher Program is the largest housing assistance program in the U.S. The vouchers are federally funded, and the U.S. Department of Housing and Urban Development (HUD) allocates the funds to local housing authorities and sets eligibility standards across the nation. HUD requires that participants’ incomes fall below 80% of the median family income in the area, adjusting for family size, and stipulates that 75% of new voucher recipients’ incomes be less than 30% of the local median family income (Center on Budget and Policy Priorities 2013). Voucher recipients must also be citizens or of other eligible immigration status, and local housing authorities can deny eligibility for a history of criminal activity (U.S. Department of Housing and Urban Development 2001; Houston Housing Authority 2013). In practice, the Houston Housing Authority maintains the official policy that recipients may have “no drug-related or violent criminal history during the past 5 years” (p. 18, Houston Housing Authority). Continued eligibility is assessed annually, and recipients are allowed to use their vouchers in any U.S. city with the program in place, although, according to HHA, less than 10% of their voucher recipients move to a different city. New program participants are allowed to use vouchers at their current (pre-voucher) address or use the vouchers to move to a new address. In practice, many do not move when they lease-up, possibly because they are given limited time to do so. Local housing authorities submit the subsidies directly to the recipients’ private market landlords. The subsidy amount is determined by a number of factors. The local housing authority calculates the number of bedrooms the family will need based on family size and composition and computes the family’s adjusted income (calculated according to HUD’s regulations). Families must contribute 30% of their adjusted income to rent at a minimum, 4

and they receive a set “maximum subsidy” amount calculated by the local housing authority as a percentage of fair market rent in a city for a given number of bedrooms. Even if the rental rate at the family’s desired apartment is less than 30% of their adjusted income plus the “maximum subsidy” the family still must pay the 30% of income, and the subsidy will be reduced. Families are not allowed to contribute more than 40% of adjusted income to housing (U.S. Department of Housing and Urban Development 2001). 2.2

The Houston Lottery

The Houston Housing Authority (HHA) serves around 60,000 Houstonians, over 80% of whom are participants in the Housing Choice Voucher Program. HHA opened its waitlist and accepted applications from December 11, 2006, to December 27, 2006; they received over 29,000 applications. All applicants were assigned a randomized lottery number (denoting wait-list position) regardless of whether they met the eligibility criteria. Vouchers were then extended to the applicants as the funding became available starting with the lowest lottery numbers. We use the term “voucher service process” to refer to the process of obtaining a voucher that begins when the applicant’s lotterygenerated wait-list position is reached and ends when the applicant leases-up with a voucher. Not all applicants complete the voucher service process. The lottery and voucher service processes are outlined in Figure 1. Once an applicant’s wait-list position was reached, he or she was sent a voucher screening packet from HHA and the verification process began. After their eligibility was verified, families were required to sign a lease in a Section 8 approved community in order to participate in the program. The average time between HHA sending the initial packet and the recipient leasing up with the voucher was 6 months. Because the speed of this process varied by applicant, the vouchers were not issued in perfect sequential order. A few lottery numbers were serviced too far out of order for this to be the likely cause. HHA says that there were no priority groups in the lottery, and there are no common characteristics of these applicants who were called more than a few numbers out of sequence. However, because we use the lottery number to identify the models, not the actual date the screening packet was sent or the date of move-in, our estimates should not be biased by any non-sequential servicing of lottery numbers. The first vouchers were issued in July 2007. However, the majority of vouchers were serviced starting in 2009, and HHA had sent screening packets to almost all the applicants by October 2012. Overall, only about 23% of applicants ever leased-up using a voucher. 5

The low lease-up is a result of applicants dropping out at every step of the voucher service process. Based on the last known application statuses, close to 60% of the verification packets were not returned to HHA by the families.4 2.5% of the applicants were found to be ineligible after verification and about 4% of them were unable to sign a lease in time, and their voucher expired. 2.3

Potential Mechanisms and Related Literature

Neighborhood effects are typically thought to impact individuals’ outcomes through a number of channels including social norm reinforcement and local opportunities. If the social norms in an individual’s neighborhood are pro-social in nature, a new resident may decide to commit less crime in order to conform to their neighborhood’s standards. Conversely, if a neighborhood has a high tolerance of criminal activity, new residents may become desensitized to crime and commit more of it. The opportunities a neighborhood provides can similarly contribute to crime or detract from it. A neighborhood with a multitude of employment prospects and available social services can reduce the need for family members to commit crimes and the time available to do so. If, on the contrary, the neighborhood provides criminal opportunities like access to the drug trade and ideal targets, the local resources could cause more crime. The empirical literature on neighborhood effects is generally small due to the challenge posed by the fact that residents choose where they live endogenously. Ludwig and Kling (2007) use the MTO experiment to get around this endogeneity issue by leveraging the fact that the 5 treatment cities provide different neighborhood characteristics for treatment group participants and that participants were randomized into treatment groups. They find that the only neighborhood characteristic that appears to assert much influence on arrests for violent crime is neighborhood racial segregation, which causes an increase. The authors suggest this increase is due to the presence of drug markets in areas with high concentrations of minorities. Voucher program participants also receive an income transfer that they may internalize in two ways: as a shock to their family income directly and as an impetus to reevaluate the way that members divide their time between labor and leisure.

We suspect that some of this was due to HHA’s lack of screening pre-application, but even in Chicago, where they did pre-screen, take-up was only 40%. 4

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Additional income can be spent on things that can increase or decrease the likelihood of arrest. Income spent on activities that contribute to human capital development may reduce criminal activity. It could also alleviate financial pressures, which would reduce the recipients’ motivations to be involved in crime that can lead to financial gain, such as selling illegal drugs or theft. Conversely, additional funds can be spent on complements to crime such as drugs, alcohol and weapons. The theoretical implications of an in-kind transfer on labor decisions are similarly ambiguous because they depend on the shape of each recipient’s indifference curves. If this additional income affords recipients the opportunity to take additional leisure time, they could use it to participate in crime or for positive activities like education or childrearing. Empirically, Section 8 voucher receipt does, in fact, cause lower labor force participation rates and earnings (Jacob and Ludwig 2012; Carlson et al. 2012), and a similar effect has been detected for Food Stamps (Hoynes and Schanzenbach 2012). The means-tested structure of the program may play a role in reducing labor force participation, as any increase in adjusted income is met with a reduction in benefits awarded. Jacob et al. (2015) suggest that a reduction in parental labor force participation may help explain why they find little effect of Section 8 vouchers on youth outcomes, while other research focused on aid programs with a work incentive component finds positive outcomes for youth (e.g. Dahl and Lochner 2012; Duncan et al. 2011; Milligan and Stabile 2011). We believe that the income transfer mechanism is the more influential in this study. Empirically, the neighborhoods in which voucher recipients use vouchers are only marginally different than those in which they lived at the time of application (see Table 1). Around 14% of voucher recipients did not move and instead used the voucher at their address listed at the time of application; nearly 30% stayed in the same Census Tract. Also, the median distance moved is only 3.01 miles. The income effects, on the other hand, appear to be quite large. The voucher paid an average of $627 toward rent every month. Only 1.71% of leasers were living in public housing at the time of application, indicating that this aid represents a new transfer to the majority of the families and not merely a change in the form of housing aid. This evidence suggesting that the income effects may dominate over neighborhood effects is in line with a number of past Section 8 studies (e.g. Jacob and Ludwig 2012; Jacob et al. 2015; Ellen et al. 2016). In fact, Ellen et al. (2012) even show that voucher recipients move into relatively high crime areas within cities. 7

2.4

Comparison of regular Section 8 and MTO Voucher Recipients

Although the Moving to Opportunity experiment gave treatment group families vouchers, there are a number of notable differences between the regular Section 8 program and MTO. Understanding these differences is important for interpreting and comparing results from empirical studies focusing on these two programs. MTO researchers recruited only public housing residents to participate in the experiment and split them into three groups. The first (the “MTO experimental group”) received vouchers and was only allowed to use them in Census Tracts with low poverty rates. The second group was simply given vouchers that could be used anywhere without restrictions. This group was called the “Section 8 experimental group.” The third was a control. MTO experimental families experienced significant improvements in neighborhood likely due to the program’s restriction on local poverty rates in Census Tracts into which families relocated (Katz et al. 2001; Kling et al. 2005). In comparison, the MTO Section 8 experimental group experienced smaller improvements in neighborhood (Kling et al. 2005). However, in the case of the regular Section 8 voucher recipients in our sample, we find the voucher-use neighborhoods to only be marginally better than their neighborhoods at the time of application. This is consistent with the findings in other Section 8 studies (e.g. Jacob and Ludwig 2012; Jacob et al. 2015; Ellen et al. 2016). For example, while the HHA voucher recipients moved to Census Tracts with a 7.5% lower average poverty rate, the MTO experimental group participants moved to Census Tracts with a 66% lower poverty rate, and the Section 8 experimental group participants saw a 38% reduction in poverty rate one year after the intervention (Kling et al. 2005). MTO required the families to move and provided little, if any, additional financial gains to them. Section 8, on the other hand, provides a substantial income transfer, and HUD does not allow local housing authorities to place restrictions on neighborhoods in which recipients can live while receiving vouchers. While we don’t have information on the Section 8 participants’ reasons for applying for the program, it is well documented that MTO families cite a desire to get away from gangs and drugs as the main reason for volunteering (e.g. Kling et al. 2005). This concern is likely addressed by the neighborhood change facilitated by MTO as well as the exit from public housing. On the other hand, Section 8 voucher receipt may have little effect on exposure to criminal activity if the families do not choose to move to better neighborhoods. The populations opting into these two programs are also likely to be quite different due to incongruous motivations. 8

3. Data The Houston Housing Authority provided us with information on all voucher applicants, applicants who eventually used a voucher (whom we call “leasers”), and participants in the program in 2014 (“current residents”). The data provided on these three groups contain different variables, explaining some of the variation in samples sizes throughout. The confidential data on applicants include lottery numbers, the number of bedrooms needed (calculated based on family size), their address at the time of application, and the date on which HHA sent the voucher screening packet. We also observe the name and birthdate of the head of household, which we use to match the HHA data to arrest records. For leasers, we know the lease start date on which they began using a voucher to pay part of their rent. For current residents, we also know their race, homeless status at the time of admission, the address of the unit at which they were using a voucher in 2014, the voucher amount, and the portion of the rent being paid by the family. HHA assigned lottery numbers up to 29,327, but we limit our sample to those living in Houston at the time of the lottery. Additionally, there are a small number of duplicate applicants; we assign them their lowest lottery number. We also drop applicants with lottery numbers greater than 24,000 because the lease-up rate is much lower among these applicants indicating a probable change in the voucher service process after that point. The resulting sample size is 19,621. Additionally, in our preferred models we restrict our analysis to leasers. The program lease-up rate is only 23%, which is low relative to the 69% national average take-up rate for Section 8 estimated by Finkel et al. (2001). We perform empirical tests, detailed in the following section, to support the assumption that the population of leasers with low lottery numbers is no different from the leasers with high lottery numbers. The resulting sample size is 4,510. We geocode the addresses listed on the applications for all applicants and the voucheruse addresses for the current residents group.5 We link the successfully geocoded addresses (some were poor quality) to Census Tracts and police divisions in order to generate measures of neighborhood characteristics. Figure 2 shows the density of these two types of addresses across the city using heat maps and contains the boundaries of HPD’s police beats. The distribution of addresses indicates that the current residents had We are grateful to Texas http://geoservices.tamu.edu/ 5

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not moved to different parts of the city on the whole, which helps to alleviate concerns about differential crime reporting rates between application and voucher use neighborhoods. Panel B of Table 1 shows the differences between the neighborhoods at the time of application and the neighborhoods in which current residents used vouchers in 2014 (for the group of leasers for whom we have geocoded 2014 voucher-use addresses as well as application addresses). We report median rent in 2012 from the American Community Survey, and we see that voucher-use addresses are in Census Tracts with only $39 higher monthly median rent. We report demographics and socioeconomic characteristics of the Census Tracts from the 2010 census and crime rates from 2000 to 2005 for the police divisions. The voucher-use neighborhoods are somewhat better off in terms of quality parameters such as unemployment rate, household income, poverty rate and crime rates. These differences in neighborhoods are minimal; for example,

voucher-use

neighborhoods had on average 2.1 less crimes per year per 1000 residents than application neighborhoods, which is a 1.5% improvement. As a result, we believe that any impact of the vouchers in this context can be most reasonably attributed to the income shock induced by an annual rent subsidy of more than $7,500 on average. Moreover, if we assume that voucher recipients were paying the median rent in their application address Census Tracts ($797), because they contribute on average $205 towards rent once they use a voucher, they are spending $592 less on housing per month. To voucher recipients, these newly-available funds are no different in effect from a direct cash transfer. The difference in the average median rent between pre- and post-voucher Census Tracts is only $39, indicating that the majority of the voucher does not go towards improved housing but instead impacts recipients like a cash transfer. We match the HHA data to arrest records provided by the Houston Police Department (HPD). The arrest records are reported at the time of booking and include information on the most serious offense as well as the arrestee’s name, birthdate, and reported home address. We match the HHA and HPD data using name and birthdate, and we perform secondary matches using the Levenshtein distance and soundex code of each name for

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unmatched records.6 The arrest records range from January 1990 to November 2011.7 We also use the matched arrest records to create measures of criminal activity in the period before the participants applied to the lottery and a quarterly panel of arrests for the study period after the program commenced (from quarter 1 of 2007 to quarter 2 of 2011). We consider arrests of any type and specifically categorize violent offenses, drug offenses and financially motivated offenses.8 We measure arrests as a binary indicator for whether the individual was arrested. The pre-lottery crime measures are constructed for the 5 years prior to the lottery, and we create an additional binary indicator for whether the applicant was arrested at least once between 1990 and 2006. Table 2 reports pre-lottery descriptive statistics. We report them for a number of groups: all applicants, low and high lottery numbers (applicants with lottery numbers below and above the median), leasers, and non-leasers. If the low and high lottery number groups are different on important measures, it could indicate that HHA gave preference to some groups in lottery number assignment. We report the leasers and non-leasers to show that the two groups are generally similar in observable characteristics. The first panel of Table 2 pertains to the lottery implementation. In the analysis that follows, treatment is defined as leasing-up using a voucher. Intuitively, the “voucher service quarter” (intent-to-treat) is the quarter during which the applicant should have leased-up according to his or her lottery number. We determine whether the individual’s lottery number has been serviced by a given quarter based on his or her lottery number relative to the numbers serviced by that point.9 On average, leasers take approximately 6 months to complete the voucher service process and actually lease-up using the voucher. For the arrest records that are unmatched by name and birthdate, we calculate the Levenshtein distance for the first and last names, if the sum of the Levenshtein distances is less than 3, conditional on an exact birthdate match, we accept the match. For example, conditional on having the same birthday, this would allow us to match “Michael” to “Micheal.” For the records that are still unmatched, we perform an exact soundex code match. Undoubtedly, there is room for mismatch, but since we do not expect the match quality to be correlated with lottery number, it should not be a concern for identification. 7 The Houston Police Department has denied our requests for additional data, so we are not able to extend the panel further into the post-lottery period. 8 A complete list of all offenses and crime categories are provided in Appendix Table A1. 9 Since the lottery numbers were not serviced in perfect sequential order, we cannot determine the voucher service quarter associated with a lottery number by simply using the smallest and largest lottery number serviced in a quarter. Additionally, for approximately 1,900 applicants, there is no recorded date of screening packet issue. As a workaround, within each quarter from 2007 to 2011, we take the lottery number at the 75th percentile of the numbers called in that quarter to be the last number called in that quarter. We assign the next lottery number as the first number called in the subsequent quarter. 6

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Lagging the quarter we estimate an applicant began the voucher service process by two quarters gives us the “voucher service quarter.” The low lottery numbers were serviced about 1.5 years (5.8 quarters) before the high lottery numbers on average. The average applicant was around 36 years old at the time of the lottery and required just over two bedrooms (indicating that the average family size was between 2 and 6) (U.S. Department of Housing and Urban Development 2001). Around 94% of residents are black,

and using 2012 voting records from the Harris County Tax Assessor’s office, we estimate that around 84% of applicants are female.10 Less than 1% of residents were homeless at the time of admission to the program. The number of observations varies for race and homeless status because they are only available for current (2014) HHA voucher recipients. The third panel pertains to criminal history of applicants. Around 20% of applicants were arrested during the 1990-2006 period, and approximately 9% of applicants had been arrested in the 5 years prior to the lottery.11 There are no statistically significant differences between applicants with high and low lottery numbers. Using the geocoded application addresses, we find that applicants lived in Census Tracts with around 47% black residents. The mean unemployment rate in those Census Tracts was around 11% and the mean of median family income was approximately $35,000. The mean poverty rate was quite high at nearly 30%. Voucher applicants with higher lottery numbers lived in Census Tracts with slightly higher unemployment rates. Voucher applicants lived in police divisions with an annual average of 133 crimes per 1000 residents. On average, nearly 60 of these crimes were property crimes and only 13 were violent. The similarity between these groups indicates that pre-lottery characteristics are distributed randomly across lottery numbers and suggests that the lottery was in fact random.

We calculate the percentage of Harris County voters whose reported gender is “male” for each unique first name in the list of registered voters. If there are at least 5 individuals with a given name, and 70% or more are listed as males, the name is assigned the gender “male.” If 30% or less are listed as male, we classify the name as “female.” Applicants with unmatched or ambiguous names are omitted from the gender subgroup analysis. 11 HHA performs criminal background checks on all adult family members to ensure that they have “no drug-related or violent criminal history during the past 5 years” (p. 18, Houston Housing Authority). HHA obtains conviction records, so applicants who were arrested but not convicted would be eligible. 10

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4. Identification and Methods In this study, we identify the effect of housing vouchers on criminal involvement using a lottery. The lottery randomized the order of the wait-list from which applicants were called to begin the voucher service process and, therefore, the order of actual voucher receipt. This randomization allows us to identify the causal effects of voucher use. Because the random variation we exploit for identification is in timing, we analyze criminal outcomes using a quarterly panel of arrests in a pooled cross-sectional model. HHA called almost all of the lottery numbers over the study period, so this panel method allows us to use the group of applicants whose lottery numbers were yet to be called as a control group. To estimate the impact of Section 8 vouchers on arrests, we estimate both intent-to-treat models that measure the effect of voucher service and two-stage least squares models that measure the effect of voucher use. To estimate the first stage, we use an indicator for whether individual i had leased up using a voucher by quarter t, called post lease-upit, as the outcome variable in an ordinary least squares regression: 𝑝𝑜𝑠𝑡 𝑙𝑒𝑎𝑠𝑒 − 𝑢𝑝𝑖𝑡 = 𝜌 + 𝜋 𝑝𝑜𝑠𝑡 𝑣𝑜𝑢𝑐ℎ𝑒𝑟 𝑠𝑒𝑟𝑣𝑖𝑐𝑒𝑖𝑡 + Ψ 𝑋𝑖 + 𝜂𝑡 + 𝜀𝑖𝑡 (1) In the above equation, post voucher serviceit is a dummy variable equal to one if we predict individual i’s voucher has been serviced by quarter t. The first stage captures the likelihood that an applicant has actually leased up with a voucher, given that we have predicted they had completed the voucher service process (recall that although most lottery numbers were called in sequential order, the time it takes to complete the verification process and start a new lease could vary). We estimate all models using quarter fixed effects (ηt) as well as robust standard errors that are clustered at the individual level. The vector Xi contains individual-level controls for criminal history, age and a measure of family size. With the exception of 2SLS models, we use ordinary least squares to estimate the models. We similarly estimate intent-to-treat (ITT) regressions of the following form: 𝑜𝑢𝑡𝑐𝑜𝑚𝑒𝑖𝑡 = 𝜌 + 𝜋 𝑝𝑜𝑠𝑡 𝑣𝑜𝑢𝑐ℎ𝑒𝑟 𝑠𝑒𝑟𝑣𝑖𝑐𝑒𝑖𝑡 + Ψ 𝑋𝑖 + 𝜂𝑡 + 𝜀𝑖𝑡 (2) The results should be interpreted as the effects of potential lease-up based on lottery number and can be rescaled by the first stage to recover a local average treatment effect. We estimate the intent-to-treat effects using a number of arrest outcomes: whether individual i was arrested for crimes of any type, violent crimes, financially-motived 13

crimes, and drug crimes in quarter t. Appendix Table A1 contains a list of crimes that fall into each category. We, again, estimate these models using quarter fixed effects (ηt) as well as robust standard errors that are clustered at the individual level. Specifications are estimated both with and without controls (Xi) for past crime (probability of arrest for the particular crime category in the 5 years prior to the lottery), age at the time of the lottery and a proxy for family size (number of bedrooms); this tests whether timing of voucher service is correlated with any of the observable characteristics.12 If specifications that do and do not include controls yield similar estimates, this can be interpreted as evidence that is consistent with randomization of the timing of lease-up. Turning to the two-stage least squares models, the first stage is described by Equation (1) and the second stage regression can be described by: ̂ − 𝑢𝑝𝑖𝑡 + Γ𝑋𝑖 + 𝜆𝑡 + 𝜈𝑖𝑡 (3) 𝑜𝑢𝑡𝑐𝑜𝑚𝑒𝑖𝑡 = 𝛿 + 𝛼 𝑝𝑜𝑠𝑡 𝑙𝑒𝑎𝑠𝑒 The results from these models can be interpreted as the effects of treatment on the treated (TOT) and do not need to be rescaled as the intent-to-treat estimates do. The coefficient α represents this direct effect of voucher use. Again, we estimate the model using quarter fixed effects (λt) as well as robust standard errors that are clustered at the individual level. We estimate the ITT and TOT effects for both the full applicant sample and the sample of leasers. We use these models even within the leaser sample because there is some variation between when we expect someone to lease-up based on lottery number and when they actually do. This is because some numbers were called out of order (using the lottery numbers to predict lease-up timing prevents any endogeneity that this could introduce) and because some families took longer to complete the verification and home search processes. The additional analyses, however, are restricted to the leaser sample. For these leasers-only models, our identifying assumption is that the timing of voucher service among those who eventually lease up was exogenous. That is, we assume that within the group of leasers, the low lottery number individuals (who leased up earlier) had similar propensities to commit crime as those with higher lottery numbers (who leased up later). We condition on lease-up because the lease-up rate (out of total applicants) is particularly low for this lottery, resulting in imprecise estimates for the

We perform additional analyses controlling for application address Census Tract characteristics and police division crime statistics in Appendix Table A3 because they are not available for all applicants. 12

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entire sample. The proportion of applicants who lease-up is consistent across time and the leasers with low and high lottery numbers do not look different on pre-determined covariates. If there is reason to believe that the late leasers differ in their crime propensities from the early leasers due to unobservable reasons that are not captured by observable measures (criminal history, age, family size, race

and pre-lottery

neighborhood characters) despite the rate of lease-up remaining unchanged throughout our study period, then our identification assumption could be violated. Specifically, we support the identifying assumption empirically by examining the extent to which demographic and criminal history variables are correlated with lottery number or voucher service quarter. We represent this graphically by simply plotting these characteristics against lottery number and estimate it empirically according to the following equation: 𝑐𝑜𝑛𝑡𝑟𝑜𝑙𝑖 = 𝛾 + 𝛽 𝑣𝑜𝑢𝑐ℎ𝑒𝑟 𝑜𝑟𝑑𝑒𝑟𝑖 + 𝑢𝑖 (4) In the above equation, voucher orderi is either the randomized lottery number assigned to leaser i or his/her voucher service quarter (where the first quarter of 2007 is indexed to one). We test for correlations between voucher order and leaser’s age at the time of lottery, number of bedrooms, and the set of criminal history variables: whether (and how many times) the leaser was arrested in the 5 years prior for any type of offense, a violent offense, a drug offense, or a financially-motivated offense, and whether the leaser was ever arrested between 1990 and 2006. We also look for trends in race and homelessness status at time of admission (for 2014 residents), neighborhood characteristics prior to the lottery (for the leasers whose addresses were geocoded successfully), and gender (for those whose gender we could impute from their first name as described in Section 3). We also take a cue from the existing mobility literature and explore the possibility of dynamic effects over time (Kling et al. 2005). Specifically, we estimate separate intent-totreat effects for the first year after voucher service and later years after voucher service by using two binary treatment variables. We also represent these dynamic effects in an event study framework. In order to further explore potential mechanisms and policy implications, we replicate our main analysis for two pairs of subgroups. We compare results for leasers with and without past arrests because we believe that past arrests may signal a propensity for crime. We then separate out male and female leasers because men have much higher

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arrest rates for violent crime than women. As further support for the identification of the models, we also present results from a placebo exercise and perform a test for attrition.

5. Results 5.1

Effect of Voucher Service on Lease-Up

Before examining the effect of voucher receipt on criminal outcomes, we first document that the voucher recipients are likely to lease-up when we predict that their vouchers were serviced. Our ability to use lottery variation to identify effects hinges on the extent to which the lottery predicts timing of lease-up. Table 3 contains the main results, including those from the first stage regressions for both the samples of all applicants (Panel A) and leasers (Panel B) in column 1. Results are obtained by estimating Equation (1) using post lease-up as the outcome, as described above, and we report the coefficient on post voucher service. In Panel A results indicate that in 19.6% of the person-quarters after voucher service, the applicant had previously leased-up. Because the proportion of applicants who lease-up is only 23%, the small magnitude of this coefficient is both expected and reasonable. It is also one of the reasons that we consider the leaser sample to be preferred. In Panel B, we report that in 86.6% of the person-quarters after voucher service, the leaser had previously leased-up. The large magnitude of this first stage result means that the intent-to-treat estimates will be very close to the local average treatment effects in the leaser sample. It also indicates that the method that we use to predict voucher service quarter from lottery number is effective. Recall that the voucher service process took, on average, 6 months, and that lottery number determined when an applicant began the voucher service process. Because there was variation in the time it took for applicants to complete this process, it is reasonable for the first stage to be less than 100%. 5.2

Effect of Voucher Service on Arrests

The remaining columns in Table 3 contain the arrest outcome results for the samples of all applicants (Panel A) and leasers (Panel B). Column 2 reports the mean of each outcome variable from the year preceding the lottery (2006) for the relevant population; we refer to it as the “pre-lottery mean” or “PLM.” In columns 3 and 4, we estimate Equation (2) without and with controls and demonstrate that our results are unresponsive to their inclusion, indicating that the timing of voucher service is unrelated to these observable

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characteristics and, we expect, to unobservable characteristics.13 The last column (5) contains results from the two-stage least squares model described by Equations (1) and (3). Each row is labeled for the outcome variable for which the results are generated. Results show no evidence that voucher service and lease-up affect arrests for all types of crimes combined. All of the coefficients are statistically insignificant for both the applicants sample and the leaser sample. We also look at arrests for specific types of crimes that are likely to be affected by voucher receipt: violent crimes, drug crimes, and financially-motivated crimes. In the leaser sample we find statistically significant effects on violent crimes. The magnitude of said effect indicates that voucher service (ITT) increases quarterly probability of violent crime arrest by 0.0690 percentage points, and voucher use (TOT) increases quarterly probability of violent crime arrest by 0.0796 percentage points. Comparing this estimate to the mean pre-lottery quarterly probability of violent crime arrest (from 2006), it represents a twofold increase. In absolute terms, these results suggest an increase of 2.76 violent crime arrests per 1000 leasers annually. The neighborhoods into which the recipients move have on average 13.4 reported violent crimes per 1000 residents annually. If each reported violent crime results in one arrest on average, this increase may be associated with an approximately 21% increase in neighborhood crime. We also find evidence that leasers are arrested for more violent crimes in the 6 months during which their voucher service process is underway but they have not yet leased-up (Appendix Table A2). We attribute this increase to the impending income shock and interpret it as an anticipatory effect because during this time a leaser knows that his or her lottery number has been serviced, but is yet to receive benefits from the program. Drug crime arrests appear to be unaffected by voucher receipt. Effects are statistically indistinguishable from zero. While the coefficients for financially-motivated crime arrests are positive and large, they are not statistically distinguishable from zero.

Table 3 contains models that include controls observed for the entire sample. We also rerun the main models adding neighborhood controls only available for a subset of recipients. Results are not statistically different from those here, the effect on violent crimes remains statistically significant (the coefficient is 0.000684 compared to 0.000690) and coefficients change minimally between models with and without controls. Results are in Appendix Table A3. 13

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All results in Panel A for the applicant sample are also indistinguishable from zero. We attribute the lack of significance to limited statistical power given the low proportion of applicants leasing up. For these reasons, we focus on the results from the leaser sample. 5.3

Tests of Identifying Assumptions

Identification of the leaser model comes from the assumption that the timing of voucher service among those who eventually leased up was exogenous. That is, we assume that within the population of leasers, individuals with lower lottery numbers had similar propensities to commit crime as those with higher lottery numbers. Because the timing of screening packet issue and therefore the subsequent transition into subsidized housing was determined by a randomized lottery, this is a reasonable assumption. Nevertheless, we test this assumption empirically in several ways. First, we show that lease-up rates did not change over time. If the rate had changed as HHA serviced higher lottery numbers, it could indicate that within the population of leasers, those with high lottery numbers may be different from those with low lottery numbers. Figure 3 plots the proportion of applicants who lease-up over lottery numbers. These lease-up rates do not appear to change over the range of lottery numbers. We also test this empirically to determine whether there is a correlation between lottery number and the probability of lease-up, and there is not a statistically significant relationship. For compositional changes to occur within the leasers sample without any detectable change in lease-up rate, any reduction in the number of a certain “type” of leaser would have to be exactly offset by an increase in the number of another “type” of leaser. Second, we test for correlations between observable characteristics and both lottery number and voucher service quarter. If the identifying assumption holds, we expect to see no correlations between these measures and demographic or criminal history variables. For example, if the most motivated applicants secured lower numbers through manipulation of the lottery mechanism, we would see a negative correlation between lottery number and indicators of stability (e.g. they would be older and have less substantial criminal histories). Alternatively, within the group of high lottery numbers, if only the most stable individuals lease-up (because they are more likely to stay at the same address for an extended period, thereby remaining reachable by HHA), we would see a positive correlation. Figure 4 represents these relationships graphically for criminal history (probability of past arrests, past violent arrests, past drug arrests and past financial arrests) and 18

demographic variables (age and number of bedrooms) for both the sample of leasers and the applicant sample for comparison. Each hollow square and solid dot represent a local average of the variable for a bin of about 1000 applicants and 250 leasers respectively. If lottery number is truly random, the local averages for applicants (hollow squares) should exhibit a flat relationship, which they do. Similarly, if the leaser population is constant over time in observable characteristics, the local averages for leaser characteristics (solid dots) should also exhibit a flat relationship. This does appear to be the case, and we take this as support for the identification assumption. In addition, the full applicant sample and the leasers sample appear similar. Table 4 reports the results of the empirical tests. Column 2 contains the results from 24 separate regressions using lottery number as the independent variable as described by Equation (4). Similarly, the regressions that generated column 3 all use indexed voucher service quarter as the independent variable. Each row is labeled for the covariate used as the dependent variable. There is only one statistically significant correlation between individual characteristics and voucher order. This effect is on the number of bedrooms, but it is not economically significant. It predicts that the individual with the highest lottery number (24,000) would require 0.11 more bedrooms than the individual with the lowest lottery number. There are no significant relationships between lottery number or voucher service quarter and criminal history measures (perhaps the most important determinants of future arrests). There are a few significant correlations between voucher order and neighborhood characteristics, but none of them are economically significant. The leasers with higher lottery numbers come from Census Tracts with higher unemployment rates and lower median rents. They also come from police divisions with higher crime rates overall and for violent crimes. Again, these differences are too small to be economically significant. For example, if we consider 2 leasers whose vouchers were serviced 2 years apart (the maximum difference in timing), we would expect the later-served leaser’s original neighborhood to only have 3.27 (2.6% of the mean) additional crimes per 1000 population annually. Importantly, because we find an increase in violent crime arrests for leasers, if we assume recipients from low crime neighborhoods have a lower propensity for crime, any indication that leasers with lower lottery numbers came from better neighborhoods would imply that our findings are a lower bound of the true increase. As an additional check, we also estimate the main models with and without these controls and show that 19

the results are invariant, indicating that timing of voucher service is orthogonal to these characteristics. We also perform a joint F-test to determine whether we can reject the hypothesis that the relationship between lottery number and all of the control variables jointly is equal to zero. We consider all of variables available for all leasers (age, number of bedrooms, whether the leaser was arrested for each type of crime in the past 5 years and a binary indicator for whether he or she had been arrested between 1990 and 2006). We are unable to reject the null hypothesis that they are jointly equal to zero (with an F-stat of 1.24). 5.4

Dynamic Effects of Voucher Service on Crime

In line with the MTO effects found for juveniles by Kling et al. (2005), one might also expect differential effects by how long an individual has been treated. Table 5 contains the results from ITT models that allow for the effect of voucher service to vary over time. Specifically, we estimate effects of two different intent-to-treat measures in one regression: whether the leaser’s voucher was serviced within the last year, and whether the leaser’s voucher was serviced more than a year ago. Because the bulk of vouchers were serviced in 2009 or later and our panel ends in 2011, most leasers were treated for just over 2 years or less. Panels A to D contain results from different crime categories. Similar to results reported previously, there is little evidence of an overall effect for all arrests, drug arrests and financially-motivated arrests. Violent arrests are slightly more responsive to voucher receipt during the first year of voucher use, although the coefficients for the first year and later years are not statistically different from each other. Figure 5 presents the dynamic effects on crime using an event study framework. Each subfigure presents coefficients and 95% confidence intervals from a single regression in which we use separate intent-to-treat measures for 2 quarter intervals before and after treatment. Post-treatment, we consider the first 2 sets of quarters (“0 & 1” and “2 & 3”) and all later times (“4 and post”). We also include leading indicators (“-1 & -2” and“-3 & -4”). All time periods are measured relative to 5 quarters or more before treatment (“-5 & pre”). The first 2 quarters before voucher service (“-1 & -2”) correspond to the period during which the eventual voucher recipient completes the approval process and looks for an apartment, this is analogous to an “announcement” period. In the figure, the pretreatment, announcement, and post-treatment periods are separated by vertical lines and labeled. 20

For all types of crime, we see no indication that there were any effects pre-treatment. If the coefficients from the pre-treatment period were not close to zero and statistically insignificant, that would cast doubt on the identifying assumption that the timing of treatment is random. Importantly, it also rules out a “best behavior” dip in criminality just before voucher service. None of the announcement effects are statistically different from zero, although the coefficients for drug arrests and violent crime arrests are positive. Both of these are likely to respond to the expectation of an income shock, which could contribute to their sign. In the post-treatment period, coefficients for all crimes and financially motivated crimes stay near zero and are statistically insignificant. The main results presented in section 5.2 for violent crime appear to be driven by quarters 3 & 4 post-treatment. The coefficient on this time period is larger, positive and statistically significant on the 5% level. Drug crimes exhibit a similar pattern although the effect in quarters 3 & 4 is only significant on the 10% level. 5.5

Subgroup Analysis

There are a number of reasons to expect different types of individuals to respond differently to the vouchers. In this section, we test numerous hypotheses about the cause of this increase in violent arrests and narrow in on a plausible explanation. It is reasonable to postulate that if the voucher makes individuals more likely to commit a crime, those who have a higher propensity for crime will respond more strongly. We compare leasers who have been arrested in the past to those who have not because they have demonstrated such a propensity for crime. Then, we compare males to females because males are more likely to be arrested in general and in our sample. Additionally, MTO studies have consistently found asymmetric effects by gender (Katz et al. 2001; ClampetLundquist et al. 2011; Jacob et al. 2015; Ludwig and Kling 2007; Kling et al. 2005; Kling et al. 2007; Zuberi 2012). Table 6 contains results for the subgroups. The first 2 columns compare results for recipients with (column 1) and without (column 2) any past arrests. Panel A contains first stage results for the subgroups, and all are large and similar to the first stage for the complete leaser sample. The following panels contain results from an intent-to-treat model including individual-level controls, similar to the results in column 4 of Table 3. As in the complete leaser sample, the result for violent crime is large and statistically significant, but only for the leasers with at least one past arrest. The effect represents an increase of nearly 70% compared to the pre-lottery mean for this subgroup. The 21

coefficient for leasers without a previous arrest, although positive, is an order of magnitude smaller and not statistically significant. For the previously-arrested subgroup, there is a sizable positive effect on financially-motivated arrests, but the coefficient is not statistically different from zero. In the second set of columns (3 and 4) we compare results by gender. We are only able to perform this analysis for leasers whose gender we could impute by their first name as described in Section 3, so the number of individuals is less than that used for the main analysis. We find that males are in fact more likely to be arrested for a violent crime than females due to voucher receipt. The coefficient for violent crime for males is large, positive, and statistically significant, while that for females is small, negative and not statistically significant. Males are more likely to have a criminal history than females, so these results mimic those in columns 1 and 2. The males are also older than the women and more likely to “lease in place” (use a voucher to pay for rent in the same apartment they lived in before receiving the voucher). They are also more likely to need only 1 bedroom for their apartment, signaling that they may be childless. Instead, we interpret the characteristics of these males to suggest that those who experience the most substantial income effects (due to the lack of neighborhood changes) and without the crime suppressing effects of children are driving them.14 If male-headed households are more likely to have multiple adults, voucher receipt could increase partner domestic violence through a number of channels. For instance, the income shock accompanying the voucher could alter the domestic balance of power in families (as formalized by Felson and Messner 2000), allowing for increased consumption of alcohol and drugs (as documented by Hsu 2016 and Angelucci 2008, among others) or increasing adult leisure time spent at home. The arrest records from the Houston Police Department do not identify domestic violence as a particular type of offense, but because we observe both home and arrest addresses, we can consider violent crime arrests occurring at home as a proxy for reported domestic violence. Only 14% of violent crimes committed by these males occur at home, so these offenses are not driving our results.

We do not report results for these subgroups within the male sample for 2 reasons. First, we are limited by sample size, but results are available upon request for subgroups of the leaser population across all the described attributes. Second, the decisions to lease in place and to change family structure suffer from selection bias, and we are hesitant to present these endogenous results. 14

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5.6

Placebo Exercise

If the leasers who lease-up with a voucher later have greater criminal proclivities than the earlier leasers, our results could be attributed to that difference. We have already shown that there is no difference in the criminal history of these two groups in the pretreatment period (Table 4) and that there is no evidence that they were on a different trajectory leading up to treatment (Table A2 and Figure 5). As additional evidence supporting the identification assumption, in this section we perform a placebo exercise that illustrates that our results are specific to the actual time of treatment. If these differing criminal trajectories were driving our results, we would expect to see treatment effects similar to those in Table 3 when we perform this placebo test. We perform the exercise using pre-period data from 2000-2006.15 Our actual study period is from 2007 quarter 1 to 2011 quarter 3. In each test, we assign a quarter from quarter 1 of 2000 to quarter 2 of 2002 to act as the starting quarter of the study period. That is, preserving the order of lottery numbers and the sequence of voucher service, we move the study period window by one quarter in each of the placebo tests. We preserve the ordering of voucher service to test whether the arrest outcomes for early and late leasers could diverge from each other as a statistical artifact in the absence of treatment. Table 7 reports results from this placebo test. In Panel A, we report the actual results for comparison (originally in Column 4 of Table 3) from the intent-to-treat model estimated with controls. Panel B reports the placebo estimates. Each coefficient is generated from an intent-to-treat model using a different placebo sample period first quarter. The columns are titled for the crime types used as the outcome variable and the rows are labeled for the placebo voucher service start date. Only one placebo estimate is statistically significant – the effect on financially-motivated crime arrests for the placebo start quarter of quarter 3 of 2000. It is only statistically significant on the 10% level. Importantly, there is no indication of any placebo results similar to those in Table 3 for violent crime arrests. We also represent these results in Figure 6. For each type of crime, we plot the estimated coefficients against the range of placebo start quarters. We also indicate the estimated coefficient from the actual program start date. For all types of crime, the placebo estimates In order to prevent overlapping with the real treatment period, while preserving our 18 month sample window, the last placebo voucher service start date we can use is Q2:2002. We are hesitant to go back further than 2000 because the individuals would be significantly younger. 15

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are close to zero and often change signs across quarters. This is in sharp contrast to the actual results for violent crime, and to a degree drug crime. The actual results are much larger than all placebo estimates for violent crime, indicating that our results are outside of the usual level of variation in arrests across the early and later leaser groups. 5.7

Test for Attrition

One potential concern for our study is attrition. That is, to the extent that individuals with low lottery numbers are more or less likely to move out of Houston than individuals with high numbers, our results could be biased. For example, if individuals who receive high lottery numbers are more likely to leave Houston and commit crimes elsewhere that are not measured in our data, then our results could overstate the increase in violent crime due to housing vouchers. We empirically test whether leasers with lower lottery numbers and earlier voucher service quarters are more or less likely to have stayed in Houston than those with higher numbers and later voucher service quarters. We proxy for continued Houston residence with whether the leaser was registered to vote in the City of Houston in 2012 and whether he or she voted in the 2012 general election. Specifically, we estimate an analog of Equation (4) used in the test of identifying assumption, to test for a relationship between when a leaser’s voucher was serviced and whether he or she stayed in the city. We show the raw data in Figure 7; it plots voter registration and actual voting in 2012 against lottery numbers. Each dot represents a local average for a bin of about 250 lottery numbers. There is no discernable correlation between lottery number and either voting outcome. This suggests that leasers whose numbers were called early in the sample period were no more or less likely to be in Houston several years later than those whose numbers were called late in the sample period. Table 8 contains the results of the empirical test. In column 1 the dependent variable is a binary indicator for being registered in 2012, and in column 2 it is a binary indicator for voting in 2012. There are no significant correlations between when a leaser was served by HHA (measured by lottery number and voucher service quarter) and the two proxies for Houston residence.16

Appendix Table A4 contains an additional test. We replicate the main results using only the population who were registered to vote in 2012. Point estimates are 0.000656, compared to 0.000690 in Table 3, but the coefficient is no longer statistically significant likely due to the reduced sample size. 16

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6. Conclusion In this study, we analyze whether receiving a housing voucher affects criminal activity of low income individuals. The timing of voucher receipt was determined by an individual’s position on the wait-list, which was assigned using a randomized lottery. We estimate intent-to-treat and two-stage least squares models using this lottery-induced variation in the timing of voucher issue to determine the effect of voucher receipt on arrests. Results indicate that voucher use causes a large increase in violent crime arrests of the adult heads of household. Over 90% of these arrests are for assaults, and most of those are simple assaults resulting in no bodily injury. We find that if 1000 individuals receive vouchers, we can expect at least 2.76 additional violent crime arrests a year.17 HHA issued vouchers to 4510 individuals, so they should observe at least 12.4 additional arrests per year. Using an estimated social cost of $9,971 per assault (from Lochner and Moretti 2004, who include incarceration costs in addition to the victim cost and property loss estimates from Miller et al. 1996), the social cost of 12.4 additional assaults (the least costly and most common type of violent crime arrest in our dataset) is $124,115.02 annually. To the extent that the arrests we observe are only a portion of the underlying crimes, this cost estimate is a lower bound. Recently, long-run studies of the Moving to Opportunity experiment as well as random moves precipitated by public housing demolitions have emphasized the positive later life impacts of moving to better neighborhoods for children (Chetty et al. 2015; and Chyn 2015). Although the Housing Choice Voucher Program was designed to facilitate such mobility in addition to providing an in-kind transfer to low-income individuals, our results indicate that the transfer may be the more dominant effect and could be leading to this increase in violent crime arrests. We show that the neighborhoods into which recipients move are only slightly less disadvantaged than their original neighborhoods, which is consistent with previous research (Lens 2013). We also calculate that the effective cash transfer experienced by the recipients could be as high as $600 per month. Based on the relative size of neighborhood and income effects, we believe that individuals in our sample may be spending the extra income on things that lead to violent crime such

17

Assuming effects are additive we calculate the annual arrests per 1000 vouchers as: 4*0.000690*1000 = 2.76

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as weapons, drugs, and alcohol, which is a well-supported outcome in the government transfer literature (Dobkin and Puller 2007; Riddell and Riddell 2005). Because Jacob and Ludwig (2012) show that Section 8 voucher recipients work less hours, we also believe that additional leisure time contributes to this negative consequence as it affords recipients more time to socialize. If that socialization also includes drugs and alcohol, this is even more likely to be the case. Although some analyses point towards weak, marginal increases in drug crime arrests, we are unable to substantiate the role of alcohol and drugs in our results for violent crime. Because the arrest offense in the data only includes the most serious crime for which an individual is arrested, some minor infractions are unobserved when coupled with a more serious crime, limiting our ability to consider them together. We find that subgroups that are highly likely to respond to such an income shock are driving the increase in violent crime arrests: males and individuals who had been arrested at least once before receiving a voucher. Both groups are more likely to have ties to criminal gangs, facilitating criminal use of these new resources. Past arrestees may also have difficulty obtaining jobs due to past criminal convictions, leaving them more leisure time. The most striking and actionable result is that the recipients who had been arrested before receiving a voucher were more likely to be arrested for a violent crime due to receiving a voucher. The Department of Housing and Urban Development empowers local housing authorities to screen applicants based on past criminal history (U.S. Department of Housing and Urban Development 2001), and the Houston Housing Authority does so in practice (Houston Housing Authority 2013). Voucher eligibility rules are focused on certain types of more serious crimes committed recently. (In Houston, applicants can be denied for a drug or violent crime in the past 5 years.) The policy implications of this result are simple and clear - housing authorities may be able to reduce this unintended consequence by further restricting eligibility or increasing monitoring on the basis of criminal history.

26

References Angelucci, M. (2008). Love on the rocks: Domestic violence and alcohol abuse in rural Mexico. The BE Journal of Economic Analysis & Policy, 8(1), 43. Carlson, D., R. Haveman, T. Kaplan, and B. Wolfe. "Long-term effects of public low-income housing vouchers on neighborhood quality and household composition." Journal of Housing Economics 21 (2), 2012.101-120. Center on Budget and Policy Priorities. “National Federal Rental Assistance Facts.” 2012. http://www.cbpp.org/files/3-10-14hous-factsheets/US.pdf Center on Budget and Policy Priorities. “Policy Basics: The Housing Choice Voucher Program.” 2013. url: http://www.cbpp.org/files/PolicyBasics-housing-1-25-13vouch.pdf Chetty, R., N. Hendren, and L. Katz. “The Effects of Exposure to Better Neighborhoods on Children: New Evidence from the Moving to Opportunity Experiment.” forthcoming American Economic Review, 2015. Chyn, E. “Moved to Opportunity: The Long-Run Effect of Public Housing Demolition on Labor Market Outcomes of Children” working paper, 2015. Clampet-Lundquist, S., K. Edin, J. R. Kling, and G. J. Duncan. "Moving teenagers out of high-risk neighborhoods: How girls fare better than boys." American Journal of Sociology 116 (4), 2011.11541189. Dahl, G. and L. Lochner “The Impact of Family Income on Child Achievement: Evidence from the Earned Income Tax Credit.” American Economic Review 102 (5), 2012.1927-1956. U.S. Department of Housing and Urban Development. “Voucher Program Guidebook: Housing Choice” 2001. url: http://portal.hud.gov/hudportal/HUD?src=/program_offices/public_indian_ housing/programs/hcv/forms/guidebook Dobkin, C. and S. L. Puller. “The effects of government transfers on monthly cycles in drug abuse, hospitalization and mortality.” Journal of Public Economics 91 (11), 2007.2137-2157. Duncan, G.J., Morris, P.A. and Rodrigues, C. “Does money really matter? Estimating impacts of family income on young children's achievement with data from random-assignment experiments.” Developmental Psychology, 47(5), 2011.1263. Ellen, I. G., Horn, K. M., & Schwartz, A. E. (2016). Why Don't Housing Choice Voucher Recipients Live Near Better Schools? Insights from Big Data. Journal of Policy Analysis and Management, 35(4), 884-905. Ellen, I. G., Lens, M. C., & O'Regan, K. (2012). American murder mystery revisited: do housing voucher households cause crime?. Housing Policy Debate, 22(4), 551-572.

27

Evans, W. N. and T. J. Moore. “The short term mortality consequences of income receipt.” Journal of Public Economics 95 (11), 2011. 1410-1424. Felson, R. B., & Messner, S. F. (2000). The control motive in intimate partner violence. Social psychology quarterly, 86-94. Finkel, M., L. Pistilli and L. Buron. "Study on Section 8 voucher success rates." Washington, DC: US Department of Housing and Urban Development, 2001. Harris County Tax Assessors Office. “2012 Voting Records.” Dataset provided by Harris County Tax Assessor. Houston Housing Authority. “Administrative Plan for Section 8 Housing Programs.” 2013. Houston Housing Authority. “2007 Voucher Lottery Records.” Confidential dataset provided by HHA. 2014. Houston Police Department. “Arrest Records 1990-2011.” Dataset provided by HPD. 2011. Houston Police Department. “UCR Reportable Crimes 1990-2011.” Dataset provided by HPD. 2011. Hoynes, H. and D. Whitmore Schanzenbach. “Work incentives and the Food Stamp Program.” Journal of Public Economics 96 (1), 2012. 151-162. Hsu, L. C. (2017). “The Timing Of Welfare Payments And Intimate Partner Violence.” Economic Inquiry, 55(2), 1017-1031. Hussey. A., A. Nikolsko-Rzhevskyy, and I. S. Pacurar. “Crime spillovers and Hurricane Katrina.” Working Paper. 2011. Jacob, B. A., M. Kapustin and J. Ludwig. ““The impact of housing assistance on child outcomes: Evidence from a randomized housing lottery” The Quarterly Journal of Economics 103 (1), 2015. 465506. Jacob, B. A., and J. Ludwig. "The effects of housing assistance on labor supply: Evidence from a voucher lottery." The American Economic Review 102 (1), 2012. 272-304. Jacob, B. A., J. Ludwig, and D. L. Miller. “The effects of housing and neighborhood conditions on child mortality.” Journal of Health Economics 32 (1), 2013. 195-206. Katz, L. F., J. R. Kling, and J. B. Liebman. "Moving to opportunity in Boston: Early results of a randomized mobility experiment." The Quarterly Journal of Economics 116 (2), 2001.607-654. Kirk, D. S. “Residential change as a turning point in the life course of crime: Desistance of temporary cessation?” Criminology 50 (2), 2012.329-358.

28

Kling, J. R., J. B. Liebman, and L. F. Katz. "Experimental analysis of neighborhood effects." Econometrica 75 (1), 2007.83-119. Kling, J. R., J. Ludwig, and L. F. Katz. "Neighborhood effects on crime for female and male youth: Evidence from a randomized housing voucher experiment." The Quarterly Journal of Economics 120 (1), 2005.87-130. Leech, T. “Violence among young adults receiving housing assistance: Vouchers, race, and transitions into adulthood.” Housing Policy Debate 23 (3), 2013.543-558. Lens, M. C. "Safe, but Could Be Safer: Why Do HCVP Households Live in Higher Crime Neighborhoods?" A Journal of Policy Development and Research 15 (3), 2013.131. Lochner, L. and E. Moretti. “The Effect of Education on Crime: Evidence from Prison Inmates, Arrests, and Self-Reports” American Economic Review, 94 (1), 2004.155-189. Ludwig, J., G. Duncan, and P. Hirschfield. “Urban poverty and juvenile crime: Evidence from a randomized housing-mobility experiment.” The Quarterly Journal of Economics 116 (2), 2001.655679. Ludwig, J., and J. R. Kling. "Is crime contagious?" Journal of Law and Economics 50 (3), 2007.491. Miller, T.R., Cohen, M.A. and Wiersema, B., “Victim costs and consequences: A new look.” 1996. Milligan, K. and Stabile, M. “Do child tax benefits affect the well-being of children? Evidence from Canadian child benefit expansions” The American Economic Journal: Economic Policy, 3(3), 2011.175205. Mills, G., D. Grubits, L. Orr, D. Long, J. Feins, B. Kaul, and M. Wood. “The Effects of Housing Vouchers on Welfare Families” Washington, DC: US Department of Housing and Urban Development, 2006. Oreopoulos, P. “The long-run consequences of living in a poor neighborhood” The Quarterly Journal of Economics, 118 (4), 2003. 1533-1575. Popkin, S. J., J. E. Rosenbaum and P. M. Meaden. “Labor market experiences of low-income black women in middle-class suburbs: Evidence from a survey of Gatreaux Program participants” Journal of Policy Analysis and Management 12 (3), 1993. 556-573. Riddell, C. and R. Riddell. “Welfare checks, drug consumption and health: Evidence from Vancouver injection drug users.” Journal of Human Resources 41 (1), 2005. 138-161. Sciandra, M., L. Sanbonmatsu, G. J. Duncan, L. A. Gennetian, L. F. Katz, R. C. Kessler, J. R. Kling, and J. Ludwig. "Long-term effects of the Moving to Opportunity residential mobility experiment on crime and delinquency." Journal of Experimental Criminology 9 (4), 2013.451-489. U.S. Census Bureau. “American Community Survey: 2006-2010.” Accessed via American Fact Finder. url: http://factfinder2.census.gov (accessed: 16 August 2016).

29

Zuberi, A. "Neighborhood poverty and children’s exposure to danger: Examining gender differences in impacts of the Moving to Opportunity experiment." Social Science Research 41 (4), 2012.788-801.

30

Table 1: Comparison of application and voucher use addresses for recipients Mean 4.8 828 627 206 1.71

Observations 1920 2974 2974 2965 4510

Application Address

Voucher Use Address

48.19 30.44 54.33 70.53 31.93 767 12.24 33266 37911 29.19 1920

48.02 34.19 48.28 69.4 30.79 807 11.05 35996 39712 27.06 1920

-0.17 (0.11) 3.75*** (0.51) -6.05*** (0.65) -1.13*** (0.15) -1.14*** (0.14) 40*** (5) -1.19*** (0.14) 2730*** (343) 1801*** (401) -2.13*** (0.32)

133.33 0.159 13.16 58.07 1240

-1.87*** (0.61) -0.003*** (0.001) -0.34*** (0.09) 0.10 (0.24)

Panel A: Voucher Use Characteristics Distance moved in miles Post voucher rent Rent paid by voucher Rent paid by resident Percent leasers living in public housing before

Panel B: Neighborhood Characteristics Census Tract Characteristics Percent male Percent white Percent black Percent over 18 years Median age Median rent Unemployment rate Median household income Median family income Percent poverty Observations

Police Division Characteristics (Annual rates per 1000 population) 135.2 Crime rate 0.162 Murder rate 13.5 Violent crime rate 57.97 Property crime rate 1240 Observations

Difference

Notes: Statistics are shown for voucher recipients for whom both pre and post-lottery addresses were available and geocodable. Crime rates at the police division level are from 2000 to 2005. Significance: * 10% level; ** 5% level; *** 1% level

31

Table 2: Descriptive statistics Observations

All

Low Lottery Numbers

High Lottery Numbers

Difference

Leasers

Non-leasers

19621 19621 19621

11982 13 0.23

5979 10 0.23

17984 16 0.23

12006*** (50) -6*** (0) 0.003 (0.006)

11852 13 1

12021 13 0

HHH Demographic Characteristics - as on the application to HHA Age (in years) 19621 36.3 Number of Bedrooms 19621 2.2 Male 16614 0.15 Female 16614 0.79 Black 2974 0.94 White 2974 0.03 Other race 2974 0.02 Homeless at the time of admission 2974 0.004

36.3 2.2 0.15 0.79 0.94 0.03 0.03 0.004

36.4 2.2 0.15 0.79 0.94 0.03 0.02 0.004

-0.07 (0.21) -0.01 (0.01) -0.002 (0.006) 0.001 (0.006) -0.002 (0.009) -0.001 (0.007) 0.003 (0.006) 0.001 (0.002)

35.3 2.2 0.10 0.84 0.94 0.03 0.03 0.001

36.7 2.1 0.16 0.77 0.96 0.03 0.02 0.025

HHH Criminal History - measured 5 or more years prior to the lottery Arrested in 5 years prior to lottery 19621 0.09 Violent offense in 5 years prior 19621 0.02 Drug offense in 5 years prior 19621 0.02 Financial offense in 5 years prior 19621 0.02 Arrested between 1990 and 2006 19621 0.18

0.09 0.02 0.02 0.02 0.18

0.09 0.02 0.02 0.02 0.18

0.003 (0.004) -0.001 (0.002) 0.002 (0.002) 0.002 (0.002) -0.001 (0.006)

0.09 0.02 0.02 0.02 0.20

0.09 0.02 0.03 0.02 0.18

0.47 0.28 778 35272 11.31 132.4 12.9 58.4

0.47 0.28 779 35329 11.45 133.1 13.0 58.6

0.005 (0.004) 0.001 (0.002) -1 (3) -57 (222) 0.14* (0.087) -0.71 (0.45) -0.08 (0.06) -0.2 (0.2)

0.53 0.29 774 33816 12.04 135.1 13.4 58.6

0.45 0.27 780 35739 11.18 132.1 12.9 58.4

9810

9811

4510

15111

Lottery Variables Lottery Number Voucher Service Quarter Leased Up with Voucher

32

Neighborhood Characteristics - based on the address at the time of application Percent black in Census Tract 15933 0.47 Poverty rate in Census Tract 15931 0.28 Median Rent in Census Tract 15913 779 Median Household Income in Census Tract 15931 35300 Unemployment rate in Census Tract 15933 11.38 Crime Rate 12788 132.8 Violent Crime Rate 12788 13.0 Property Crime Rate 12788 58.5 Total applicants per group

19621

Notes: Lottery numbers are classified as low or high based on whether they are below or above the median (11960). HHH stands for Household Head. As described in the text, gender could only be imputed for 16614 applicants. Race and other demographic characteristics are only available for applicants who were participating in the HCVP when we obtained the data (2974). Neighborhood characteristics are available only for those applicants whose pre-lottery addresses were geocodable and matched to a census tract (15933) or police division (12788). Neighborhood crime rates are annual rates reported at the police division level from 2000 to 2005 provided by HPD, who also supplied the arrest data. Census tract attributes are from the American Community Survey. Significance: * 10% level; ** 5% level; *** 1% level

Table 3: Effect of vouchers on crime - By crime type First stage (with controls)

PLM

ITT (without controls)

ITT (with controls)

2SLS (with controls)

All arrests

0.0066

Violent arrests

0.001

Drug arrests

0.0017

Financial arrests

0.0011

0.000316 (0.000484) 0.0000167 (0.000146) 0.000143 (0.000217) 0.000121 (0.000181) 353178 19621

0.000235 (0.000474) 0.0000220 (0.000146) 0.000112 (0.000215) 0.000108 (0.000180) 353178 19621

0.00120 (0.00242) 0.000112 (0.000744) 0.000574 (0.00110) 0.000549 (0.000921) 353178 19621

0.000431 (0.00100) 0.000701* (0.000361) 0.000168 (0.000379) 0.000189 (0.000442) 81180 4510

0.000395 (0.000990) 0.000690* (0.000359) 0.000215 (0.000376) 0.000155 (0.000439) 81180 4510

0.000456 (0.00114) 0.000796* (0.000414) 0.000248 (0.000434) 0.000179 (0.000506) 81180 4510

Panel A: Full Sample Voucher use

Observations Individuals Panel B: Leaser Sample Voucher use

0.196*** (0.00419)

353178 19621

0.866*** (0.00376)

All arrests

0.0055

Violent arrests

0.0007

Drug arrests

0.0012

Financial arrests

0.0007

Observations Individuals

81180 4510

Notes: Panel A presents results for the full sample and panel B for only those applicants who eventually leased up with a voucher. Each cell of each column represents a separate regression estimating equation 2. Unit of observation is a person-quarter. First stage results are shown in column 1 where the dependent variable is an indicator for post lease-up. The pre-lottery means (PLM), mean of quarterly probability of arrest in the crime category from the year 2006, are shown in column 2. Intent-To-Treat effects for each of the crime categories without and with controls are shown in columns 3 and 4. Two-stage least squares estimates are shown in column 5. The dependent variables in columns 3 to 5 are dummy variables indicating an arrest in the person-quarter for the particular category of offense. Controls include age at the time of the lottery, number of bedrooms and a dummy indicating an arrest in the crime category in the 5 years prior to the lottery. Robust standard errors, clustered at the individual level, are presented in parentheses. Significance: * 10% level; ** 5% level; *** 1% level

33

Table 4: Test of identification Independent variables Dependent variables

Observations

Lottery number/1000

Voucher service quarter

Arrested in 5 years prior to lottery

4510

Violent offense in 5 years prior

4510

Drug offense in 5 years prior

4510

Financial offense in 5 years prior

4510

Number of arrests in 5 years prior

4510

Number of violent arrests in 5 years prior

4510

Number of drug arrests in 5 years prior

4510

Number of financial arrests in 5 years prior

4510

Arrested between 1990 and 2006

4510

Age

4510

Number of bedrooms

4510

Male

3844

Female

3844

Black

2612

White

2612

Other race

2612

Homeless at the time of admission

2612

Percent black in Census Tract

3633

Median Rent in Census Tract

3629

Poverty rate in Census Tract

3632

Unemployment rate in Census Tract

3633

Median Household Income in Census Tract

3632

Crimes per 1k population

2939

Violent Crimes per 1k population

2939

Property Crimes per 1k population

2939

0.0003 (0.0006) 0.0000 (0.0003) 0.0005 (0.0003) -0.0001 (0.0003) 0.0008 (0.0009) 0.0002 (0.0003) 0.0005 (0.0004) 0.0001 (0.0003) 0.0003 (0.0009) 0.0109 (0.0312) 0.0046** (0.0021) -0.0005 (0.0007) -0.0003 (0.0009) 0.0004 (0.0007) -0.0001 (0.0005) -0.0004 (0.0005) -0.0001 (0.0001) 0.0008 (0.0007) -0.701* (0.413) -0.0004 (0.0003) 0.0272* (0.0139) 21.51 (31.48) 0.15** (0.0653) 0.0195** (0.0086) 0.0436 (0.0291)

0.0003 (0.0013) -0.0002 (0.0006) 0.0009 (0.0006) -0.0004 (0.0006) 0.0016 (0.0018) 0.0001 (0.0006) 0.0011 (0.0008) 0.0002 (0.0007) 0.0005 (0.0018) 0.0405 (0.0638) 0.0088** (0.0043) -0.0012 (0.0015) 0.0001 (0.0018) 0.0009 (0.0015) 0 (0.0011) -0.0009 (0.001) 0.000 (0.0002) 0.0024* (0.0014) -0.878 (0.848) -0.0009 (0.0006) 0.0723** (0.0283) 50.57 (63.97) 0.409*** (0.136) 0.0539*** (0.0179) 0.111* (0.0604)

Notes: Each cell represents a separate regression, estimating equation 4 with the listed covariate as the dependent variable. Unit of observation is an individual. Column 2 shows the coefficients of lottery number scaled down by 1000 and column 3 shows coefficients of the quarter in which the voucher is serviced (where Q1:2007 is indexed to one). Robust standard errors are presented in parentheses. Significance: * 10% level; ** 5% level; *** 1% level

34

Table 5: Effect of voucher service on crime - By time since voucher service (1)

(2)

0.00107 (0.00112) -0.000770 (0.00141) 0.0055

0.00103 (0.00111) -0.000805 (0.00140)

0.000712* (0.000386) 0.000682 (0.000563) 0.0007

0.000702* (0.000385) 0.000666 (0.000560)

0.000278 (0.000424) -0.0000392 (0.000562) 0.0012

0.000318 (0.000423) 0.0000212 (0.000559)

0.000394 (0.000546) -0.000294 (0.000510)

Pre-Lottery Mean

0.000424 (0.000549) -0.000253 (0.000512) 0.0007

Observations Individuals Quarter FE Controls

81180 4510 Yes No

81180 4510 Yes Yes

Panel A: All Arrests < 1 yr since voucher service > 1 yr since voucher service Pre-Lottery Mean Panel B: Violent Arrests < 1 yr since voucher service > 1 yr since voucher service Pre-Lottery Mean Panel C: Drug Arrests < 1 yr since voucher service > 1 yr since voucher service Pre-Lottery Mean Panel D: Financial Arrests < 1 yr since voucher service > 1 yr since voucher service

Notes: Each column within a panel represents a separate regression estimating ITT models with the independent variable split up by duration since voucher service. The dependent variables in Panels A to D are dummy variables indicating an arrest in the person-quarter for any offense, violent offense, drug related offense, and financially motivated offense respectively. Pre-lottery mean is the mean of quarterly probability of arrest in the crime category from the year 2006. Controls include age at the time of the lottery, number of bedrooms and a dummy indicating an arrest in the crime category in the 5 years prior to the lottery. Robust standard errors, clustered at the individual level, are presented in parentheses. Significance: * 10% level; ** 5% level; *** 1% level

35

Table 6: Effect of voucher service on crime - Subgroup analysis Criminal history

Gender

Past arrest (1)

No past arrest (2)

Males (3)

Females (4)

0.870*** (0.00773)

0.865*** (0.00428)

0.879*** (0.0131)

0.862*** (0.00453)

0.00214 (0.00357) 0.0281

0.00000763 (0.000868) 0

-0.00173 (0.00462) 0.0174

-0.000318 (0.000995) 0.0039

0.00262** (0.00129) 0.0037

0.000229 (0.000318) 0

0.00394* (0.00224) 0.0013

-0.0000570 (0.000320) 0.0005

0.000435 (0.00151) 0.0062

0.000170 (0.000288) 0

-0.00159 (0.00213) 0.006

0.000184 (0.000358) 0.0008

Pre-lottery Mean

0.00160 (0.00166) 0.0037

-0.000191 (0.000365) 0

-0.00151 (0.00155) 0.0007

0.000436 (0.000467) 0.0006

Observations Individuals Quarter FE Controls

15858 881 Yes Yes

65322 3629 Yes Yes

6732 374 Yes Yes

58446 3247 Yes Yes

Panel A: First stage Post Voucher Service Panel B: All arrests Post Voucher Service Pre-lottery Mean Panel C: Violent arrests Voucher Service Pre-lottery Mean Panel D: Drug arrests Post Voucher Service Pre-lottery Mean Panel E: Financial arrests Post Voucher Service

Notes: Each column within a panel represents a separate regression estimating ITT models within a subgroup. While panel A presents the first stage effects, panels B to E present the ITT effects on being arrested in the person-quarter for the particular crime category. Pre-lottery mean is the mean of quarterly probability of arrest in the crime category for the particular subgroup from the year 2006. Controls include age at the time of the lottery, number of bedrooms and a dummy indicating an arrest in the crime category in the 5 years prior to the lottery. Robust standard errors, clustered at the individual level, are presented in parentheses. Significance: * 10% level; ** 5% level; *** 1% level

36

Table 7: Placebo treatment test - Effects of voucher service on crime

Panel A: Actual estimates Treatment start date 2007 Q1

Panel B: Placebo estimates Treatment start date 2000 Q1 2000 Q2 2000 Q3 2000 Q4 2001 Q1 2001 Q2 2001 Q3 2001 Q4 2002 Q1 2002 Q2

Observations Individuals Quarter FE Controls

All arrests (1)

Violent (2)

Drug (3)

Financial (4)

0.000395 (0.000990)

0.000690* (0.000359)

0.000215 (0.000376)

0.000155 (0.000439)

0.0000648 (0.000729) 0.000485 (0.000718) 0.00107 (0.000706) 0.000204 (0.000708) 0.000148 (0.000718) 0.000119 (0.000683) -0.000239 (0.000705) 0.000632 (0.000677) 0.0000204 (0.000700) -0.000369 (0.000687)

-0.000228 (0.000334) -0.000242 (0.000325) 0.000134 (0.000321) -0.0000340 (0.000293) -0.000130 (0.000265) 0.000121 (0.000269) -0.000162 (0.000272) 0.00000947 (0.000251) -0.000349 (0.000287) -0.000132 (0.000266)

-0.0000533 (0.000304) 0.0000826 (0.000289) 0.0000732 (0.000304) 0.0000321 (0.000320) -0.000519 (0.000329) -0.000236 (0.000268) -0.000145 (0.000289) 0.0000496 (0.000307) -0.000125 (0.000291) -0.000278 (0.000294)

-0.00000819 (0.000293) 0.000426 (0.000293) 0.000541* (0.000296) 0.000205 (0.000299) 0.000175 (0.000323) 0.000163 (0.000308) 0.0000576 (0.000335) 0.0000563 (0.000314) 0.0000578 (0.000271) -0.000218 (0.000295)

81180 4510 Yes Yes

81180 4510 Yes Yes

81180 4510 Yes Yes

81180 4510 Yes Yes

Notes: Each cell represents a separate regression estimating the ITT model. The actual estimates of effects on arrests within different crime categories are shown in Panel A. Panel B shows the estimates from placebo treatments. Each row in this panel presents estimates from a placebo exercise where the quarter indicated in first column was assigned to be the first quarter in the sample. Controls include age at the time of the lottery, number of bedrooms and a dummy indicating an arrest in the crime category in the 5 years prior to the lottery. Robust standard errors, clustered at the individual level, are presented in parentheses. Significance: * 10% level; ** 5% level; *** 1% level

37

Table 8: Test of differential attrition across lottery numbers Registration and voting in 2012 (1)

(2)

Panel A

Registered

Voted

Lottery number/1000

0.000520 (0.00102)

-0.0000686 (0.00103)

Panel B

Registered

Voted

Quarter of voucher service

0.000521 (0.00208)

-0.000601 (0.00211)

Observations

4510

4510

Each cell represents a separate regression estimating the ITT models. equation 4 with indicators for being registered and having voted in 2012 as the dependent variables in columns 1 and 2, respectively. Unit of observation is an individual. Panel A shows the coefficients for lottery number scaled down by 1000 and Panel B shows coefficients for the voucher service quarter. Robust standard errors are presented in parentheses. Significance: * 10% level; ** 5% level; *** 1% level

38

Figure 1: Lottery and voucher service processes (a) Lottery Process

(b) Voucher Service Process

Notes: Voucher service process began in 2007 right after the lottery, but very few vouchers were serviced. The bulk of vouchers were serviced starting from 2009. The last of the vouchers were serviced in 2012.

39

Figure 2: Heatmaps of application and voucher use addresses (a) Distribution of Application Addresses

(b) Distribution of Voucher Use Addresses

Notes: The heat maps are created in ArcMap using a point density operation that creates a grid over the map and then counts the number of address points within each grid cell. The outline indicates the boundaries of the police beats of the Houston Police Department.

40

Figure 3: Lease-up rates across lottery numbers

Notes: Each bubble represents the percentage of lease-up within bins of about 980 applicants.

41

Figure 4: Test of randomization - Distribution of pre-lottery characteristics (a) Criminal history

(b) Demographics

Notes: Each blue square and red dot represent the local average of the variable within lottery number bins of about 1090 applicants and 250 leasers respectively. Criminal history variables represent the probability of arrest in the crime category between 2002 and 2006 (5 years prior to the lottery).

42

Figure 5: Event study - Effect of voucher service on crime

43 Notes: This figure plots the divergence between the treated and yet to be treated leasers before and after voucher service (intention to treat). The estimates were generated from the ITT model with the treatment variable split up by time since voucher service. The red and green vertical lines indicate the beginning of the voucher service process and enrollment into the program respectively. The points to the left of the red line show the divergence in the pre-treatment period. The point in between the red and green lines represents the announcement effect, and the points to the right of the green line represent the effect of voucher service.

Figure 6: Placebo treatment test - Effect of voucher service on crime

44 Notes: We conducted 10 placebo treatment tests by applying treatment with different start dates in the pre-treatment period. The estimates from these tests of the effect of voucher service (ITT) on arrests in different crime categories are presented by the red lines. As a comparison, the actual estimated effect is shown by the blue lines.

Figure 7: Test for attrition - Likelihood of voter registration and voting in Houston in 2012 across lottery numbers

Notes: Each bubble represents the local percentage of recipients that were registered to vote and that voted in Houston in 2012 within bins of about 250 individuals.

45

APPENDIX Table A1: Classification of crimes into categories Category

Included crimes

Violent

Assault, Aggravated Assault, Arson, Kidnapping, Murder, Robbery, Sexual Assault

Drug

Alcohol related offenses, DUI, Manufacture, Possession or Sale of contraband products

Financial

Auto Theft, Burglary, Gambling, Robbery, Shoplifting, Theft, White Collar crimes (Forgery, Fraud etc.)

Unclassified

Minor traffic offenses, Carrying/Discharging prohibited weapons, Criminal Mischief, Criminal Trespassing, Evading arrest, Indecent behavior/exposure, Prostitution related arrests

46

Table A2: Intent to treat estimates with controls and leads

Panel A: All Arrests Post Voucher Service

(1)

(2)

(3)

0.000431 (0.00100)

0.000395 (0.000990)

0.000516 (0.00114) 0.000231 (0.00122) 0.000184 (0.00106)

0.000701* (0.000361)

0.000690* (0.000359)

0.000898** (0.000403) 0.000741* (0.000430) -0.000125 (0.000365)

0.000168 (0.000379)

0.000215 (0.000376)

0.000633 (0.000435) 0.000952* (0.000554) 0.000432 (0.000469)

0.000189 (0.000442)

0.000155 (0.000439)

0.000465 (0.000480) 0.000489 (0.000478) 0.000597 (0.000496)

81180 4510 Yes No

81180 4510 Yes Yes

81180 4510 Yes Yes

Announcement effect Lead Panel B: Violent Arrests Post Voucher Service Announcement effect Lead Panel C: Drug Arrests Post Voucher Service Announcement effect Lead Panel D: Financial Arrests Post Voucher Service Announcement effect Lead

Observations Individuals Quarter FE Controls

Notes: Each column within a panel represents a separate regression estimating ITT models. In column 3, indicators for 1-2 quarters before voucher service (announcement effect) and 3-4 quarters before voucher service (leads testing for pre-treatment trends) are included. The dependent variables in Panels A to D are dummy variables indicating an arrest in the person-quarter for any offense, violent offense, drug related offense, and financially motivated offense respectively. Controls include age at the time of the lottery, number of bedrooms and a dummy indicating an arrest in the crime category in the 5 years prior to the lottery. Robust standard errors, clustered at the individual level, are presented in parentheses. Significance: * 10% level; ** 5% level; *** 1% level

47

Table A3: Intent to treat estimates with controls for neighborhood characteristics

Panel A: All Arrests Post Voucher Service Panel B: Violent Arrests Post Voucher Service Panel C: Drug arrests Post Voucher Service Panel D: Financial arrests Post Voucher Service

Observations Individuals Quarter FE Main Controls Census Tract Controls Dummy for missing Census Tract Controls Crime Controls Dummy for missing Crime Controls

(1)

(2)

(3)

0.000395 (0.000990)

0.000405 (0.000989)

0.000506 (0.000993)

0.000690* (0.000359)

0.000684* (0.000359)

0.000699* (0.000364)

0.000215 (0.000376)

0.000228 (0.000375)

0.000266 (0.000375)

0.000155 (0.000439)

0.000152 (0.000439)

0.000195 (0.000446)

81180 4510 Yes Yes No

81180 4510 Yes Yes Yes

81180 4510 Yes Yes Yes

No

Yes

Yes

No No

No No

Yes Yes

Notes: Each column within a panel represents a separate regression estimating ITT models with a different set of control variables. Main controls include age at the time of the lottery, number of bedrooms and a dummy indicating arrest in the crime category in the 5 years prior to the lottery. Census Tract controls include percent black, unemployment rate, median household income, and poverty rate for the census tract of the individual’s application address. Crime controls include annual rates for overall crime, violent, and property crimes per 1000 people in the police division of the individual’s application address. We include dummy variables indicating whether the demographic or crime controls are missing. The dependent variables in Panels A to D are dummy variables indicating an arrest in the person-quarter for any offense, violent offense, drug related offense, and financially motivated offense respectively. Robust standard errors, clustered at the individual level, are presented in parentheses. Significance: * 10% level; ** 5% level; *** 1% level

48

Table A4: Effects of voucher service on crime - For individuals registered to vote in 2012

Panel A: All Arrests Post Voucher Service Panel B: Violent Arrests Post Voucher Service Panel C: Drug Arrests Post Voucher Service Panel D: Financial Arrests Post Voucher Service

Observations Individuals Quarter FE Controls

(1)

(2)

0.000890 (0.00126)

0.000909 (0.00125)

0.000671 (0.000450)

0.000656 (0.000447)

0.000294 (0.000507)

0.000368 (0.000504)

0.000645 (0.000556)

0.000640 (0.000554)

56754 3153 Yes No

56754 3153 Yes Yes

Notes: Each column within a panel represents a separate regression estimating ITT models for the subset of leasers that were registered to vote in 2012 in Houston. The dependent variables in Panels A to D are dummy variables indicating an arrest in the person-quarter for any offense, violent offense, drug related offense, and financially motivated offense respectively. Controls include age at the time of the lottery, number of bedrooms and a dummy indicating an arrest in the crime category in the 5 years prior to the lottery. Robust standard errors, clustered at the individual level, are presented in parentheses.

49