Psychology
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Quasi-Experimental.pdf
ORIGINAL PAPER
A Quasi-Experimental Evaluation of the Impact of Public Assistance on Prisoner Recidivism
Jeremy Luallen1 • Jared Edgerton1 • Deirdre Rabideau1
Published online: 12 May 2017 � Springer Science+Business Media New York 2017
Abstract Introduction The Welfare Act of 1996 banned welfare and food stamp eligibility for felony drug offenders and gave states the ability to modify their use of the law. Today,
many states are revisiting their use of this ban, searching for ways to decrease the size of
their prison populations; however, there are no empirical assessments of how this ban has
affected prison populations and recidivism among drug offenders. Moreover, there are no
causal investigations whatsoever to demonstrate whether welfare or food stamp benefits
impact recidivism at all.
Objective This paper provides the first empirical examination of the causal relationship between recidivism and welfare and food stamp benefits
Methods Using a survival-based estimation, we estimated the impact of benefits on the recidivism of drug-offending populations using data from the National Corrections
Reporting Program. We modeled this impact using a difference-in-difference estimator
within a regression discontinuity framework.
Results Results of this analysis are conclusive; we find no evidence that drug offending populations as a group were adversely or positively impacted by the ban overall. Results
apply to both male and female populations and are robust to several sensitivity tests.
Results also suggest the possibility that impacts significantly vary over time-at-risk, despite
a zero net effect.
Conclusion Overall, we show that the initial passage of the drug felony ban had no measurable large-scale impacts on recidivism among male or female drug offenders. We
conclude that the state initiatives to remove or modify the ban, regardless of whether they
& Jeremy Luallen [email protected]
Jared Edgerton [email protected]
Deirdre Rabideau [email protected]
1 Abt Associates, 55 Wheeler St., Cambridge, MA 02451, USA
123
J Quant Criminol (2018) 34:741–773 https://doi.org/10.1007/s10940-017-9353-x
improve lives of individual offenders, will likely have no appreciable impact on prison
systems.
Keywords Welfare � Food stamps � Drugs � Ban � Prison � Recidivism
Introduction
In response to the growing financial and social pressures of mass incarceration, policy-
makers are evaluating policies and practices in the criminal justice system and searching
for ways to reduce correctional burden while protecting the public interest. One policy that
has drawn recent attention is the drug felony ban on food stamp benefits (now called the
Supplemental Nutrition Assistance Program or SNAP) and cash assistance (known as
Temporary Assistance to Needy Families or TANF). Originally introduced in 1996 as part
of the Personal Responsibility and Work Opportunity Reconciliation Act (PRWORA), this
ban completely denied SNAP and TANF eligibility for ‘‘individual(s) convicted (under
federal or state law) of any offense which is classified as a felony… and which has as an element the possession, use, or distribution of a controlled substance.’’
At the time it was passed, proponents of the ban criticized drug felons for receiving
public benefits despite having broken the nation’s drug laws and argued for denial of
benefits on the basis of moral and social principles (Godsoe 1998; Allard 2002). 1 In years
since, critics of the ban have argued that denying benefits creates a net harm to society,
worsening outcomes for needy populations and especially for women and children (Mauer
and McCalmont 2013; Godsoe 1998; Allard 2002; Eadler 2011). Importantly, the original
law gave states the ability to opt out or modify their use of the ban through legislative
reforms.
This feature is important because it suggests why legislators still care about the ban
today; states across the country are increasingly viewing removal of the ban as a way to
reduce the number of drug offenders returning to prison after they are released. For
example in 2014 and 2015, Missouri and California (respectively) enacted new laws that
completely or partially removed the SNAP ban for convicted drug felons. Similarly, in
2015 the Alabama legislature passed a prison reform bill that allows drug felons to start
receiving benefits in 2016 (Edgemon 2015). These illustrations are telling—the high costs
of prisons and changes in social and political attitudes towards the ban are driving its re-
examination.
Despite the political rhetoric surrounding the use of the ban, there is no direct empirical
evidence to support or reject whether states can measurably affect prisoner recidivism or
the size of prison populations through their use of the ban. In fact, there does not appear to
be any causal evidence whatsoever to demonstrate that the receipt of TANF or SNAP
benefits does or does not have an impact on an individual’s propensity to return to prison.
This paper investigates the relationship between receipt of public assistance (specifi-
cally, in the form of SNAP and TANF benefits) and recidivism by examining how the
enactment of the drug felony ban impacted recidivism rates for drug offending populations.
Using individual-level prison records from the National Corrections Reporting Program
(NCRP) across six states, we estimated the impact of the ban’s 1996 implementation on
1 In fact, the ban itself was a relatively obscure provision in a much larger piece of legislation. Congres-
sional records show that the ban provision saw \2 min of total debate (Mauer 2002; Petersilia 2003).
742 J Quant Criminol (2018) 34:741–773
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rates of returning to prison. We defined a return to prison as a return for any reason
(conviction or revocation) and for any type of crime. 2 Impacts were identified using
difference-in-difference estimation within a regression discontinuity framework, and were
estimated through survival-based regression modeling techniques (i.e., proportional haz-
ards models) described in subsequent sections.
Overall we find no strong evidence to support the claim that recidivism rates or the size
of prison populations has been materially influenced by the drug felony ban. Among both
male and female prison populations, the estimated pooled impact of the ban is not sta-
tistically different from zero (with point estimates very near zero). Across states, estimates
are more variable; however, for both male and female prisoners, state estimates provide no
consistent depiction of how these populations are affected by policy changes.
Results are also extremely robust to alternative model specifications. We test the sen-
sitivity of our results to more flexible time trends and alternative parametric specifications
and find no meaningful changes to baseline results. This implies that changes to drug
felony ban implementation cannot materially influence the size of prison populations in the
aggregate.
We discuss potential explanations for this null finding later in the paper. One of those
possible explanations, which we explore empirically, is that impacts may be heterogonous
with respect to time-at-risk. If true, then local average treatment effects could be zero while
treatment effects within the sample vary. We tested this by stratifying estimates by time-at-
risk (using 6- and 18-month intervals). From this test we find evidence suggesting that
denying benefits may in fact improve short-term outcomes while worsening long-term
outcomes. At the very least, we see this evidence as motivation for future study.
The remainder of this paper is organized as follows. First, we present a background
discussion on the role of public assistance in re-entry and features of the drug felony ban.
Next, we describe the data we use for this analysis and our methods for identifying
impacts, followed by a presentation of results. We conclude with a discussion of the
limitations of our analysis and closing remarks.
Background
Offender Re-Entry, Economic Challenges and Use of Welfare
There is a large body of research devoted to understanding how offender outcomes are
shaped by the economic challenges they face after prison (e.g., Western et al. 2014; Travis
2005; Petersilia 2003). The reason is that offenders, like other low-income populations, are
economically disadvantaged and in need of services that can mitigate barriers to successful
re-entry. Employment is one of the most oft-studied outcomes (e.g., Kling 2006; Bushway
et al. 2007; Stoll and Bushway 2008), though other economic considerations such as
housing, court-imposed sanctions (fines, restitution and fees), use of public assistance and
demand for health services also receive significant attention in the literature (e.g., Sheely
and Kneipp 2015; Lindquist et al. 2009; Evans 2014; Geller and Curtis 2011).
2 Since the NCRP does not capture alternative measures of recidivism (e.g., rearrest, reconviction, incar-
ceration in jail, etc), we could not explore alternative definitions in our analysis. However, return to prison is a useful and important measure (e.g., Hunt and Dumville 2016; Langen and Levin 2002; Durose et al. 2014). It is often used as a metric for evaluating programs, assessing trends and gauging impacts for other correctional issues of interest, often in concert with other metrics such as rearrest or reconviction (e.g., Bales et al. 2005; Spivak and Damphousse 2006; Steurer and Smith 2003).
J Quant Criminol (2018) 34:741–773 743
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Two specific public assistance programs, SNAP and TANF, provide significant supports
to low-income households and families in general, though their use among offending
populations in particular is unclear. On a national scale, benefits paid by SNAP each month
in FY2014 averaged roughly 5.8 billion dollars over 46 million individuals, or $125 per
person per month (US Department of Agriculture 2017). For TANF, FY2014 benefits paid
each month averaged $2.6 billion dollars (including both federal and required state
spending) over 3.9 million recipients, or around $667 a month (US Department of Health
and Human Services 2016). This level of support suggests that both programs may provide
an important level of assistance to offenders as they re-enter the community. In addition to
simple subsidy support, TANF assistance can also include a variety of services that may
further promote successful reintegration such as job training, counseling and crisis
management.
Despite its likely importance to offenders, receipt of public assistance and its impact on
re-offending in the post-release period is an issue we know surprisingly little about. This is
not because the issue is unimportant or has been overlooked. Rather, there is a fundamental
lack of data sufficient to study the issue. Few data sources exist which tie together welfare
receipt and longitudinal outcomes with incarceration, criminal history, and other criminal
measures (Sheely and Kneipp 2015; Butcher and LaLonde 2006; Holtfreter et al. 2004).
Even the most basic statistics are difficult to find. For example, we were unable to locate
any national estimates of how many released offenders receive public assistance including
SNAP or TANF. 3 Overall, the limit to our knowledge at present appears to be this: likely
somewhere between 25 and 40% of female prisoners are eligible for SNAP and/or TANF
after release; for males this number is likely between 10 and 20% (Lindquist et al. 2009;
Lattimore et al. 2009; Ekstrand 2005; Allard 2002; Butcher and LaLonde 2006; Hirsch
1999). These estimates are both crude and imprecise. They are also evolving as we learn
more. For example, a recent longitudinal study of prisoners released in Boston suggests the
likelihood of receiving benefits increases significantly over time, and that welfare receipt in
the post-incarceration period may be as high as 70% (Western et al. 2014).
Despite the general lack of empirical data on SNAP/TANF participation and program
impacts for offending populations, there are many studies that have examined program
impacts on employment, household structure and household earnings, housing and food
security and health for participants more broadly (e.g., Blank 2002; Schoeni and Blank
2000; Lindner and Nichols 2012; Bitler 2014). Evidence from this literature suggests that
programs like SNAP and TANF can and do have positive impacts on the lives of indi-
viduals in many cases. In that case, it seems reasonable to assume that offending popu-
lations enjoy similar benefits from participation. For these reasons, scholars have argued
that ‘‘an offender’s eligibility to receive public assistance is critical to successful reinte-
gration’’ (Petersilia 2003).
SNAP, TANF and Recidivism: The Potential Impact of Denying Benefits
Despite the intuitive appeal of the argument, ‘‘benefits should improve offender outcomes
and thereby reduce recidivism,’’ there is no direct, causal evidence to support or refute this
claim. If benefits extend the affordability of basic needs and services like food, housing,
drug treatment, physical and mental heath services, etc. (Allard 2002; Mohan and Lower-
3 The closest source to a nationally representative picture we could locate comes from the Bureau of Justice
Statistics Inmate Survey, which provides limited information on welfare receipt before an arrest and during an offender’s childhood. This survey does not track offenders over time.
744 J Quant Criminol (2018) 34:741–773
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Basch 2014; Mauer and McCalmont 2013; Godsoe 1998), then providing benefits should
reduce the need for (and causes of) criminal behavior, thereby decreasing the likelihood of
reoffending (Petersilia 2003). At least some empirical research supports such associations
between poverty, state supports and recidivism (Holtfreter et al. 2004).
On the other hand, benefits may also be counterproductive as a means of reducing
recidivism, particularly in the case of drug offenders. One possibility is that benefits
provide drug users with additional purchasing power that allows them to substitute pur-
chases of other goods for more drugs (Johnson et al. 1985). If more income leads to greater
drug use, providing benefits may serve to increase recidivism rates among beneficiaries.
Alternatively, recipients may fraudulently trade their benefits for drugs or for cash used to
purchase drugs (Roebuck 2014; Statement of the Honorable Phyllis K. Fong Inspector
General 2012; Oregon Revised Statute §411.119 2005). 4 Receipt of benefits could also
reduce the pressures to engage in other prosocial behaviors during the post-release period,
e.g., consistent job-seeking or more frequent visitation with supervision officers.
Another consideration is that SNAP and TANF programs serve different (but over-
lapping) populations, such that their potential importance to offenders and ultimately
corrections systems should also vary along these dimensions. For example, the proportion
of adult males receiving SNAP (around 44% of adult participants) is much higher than for
TANF (around 15% of adult participants) (US Department of Agriculture 2017; US
Department of Health and Human Services 2016). This implies that changes pertaining to
SNAP are more likely to have the greatest impact on prisons, where males make up the
majority of inmates. Conversely, female prison populations would be more impacted by
restrictions to TANF. Such variations help to explain potential differences in impacts we
might find between men and women.
As another example, consider that nearly 20% of SNAP households are nondisabled,
childless adult households, while only 6% of TANF households are single-member
households. If offenders tend to be young individuals without children, then understanding
how SNAP benefits can affect outcomes becomes more relevant to understanding how the
ban may or may not affect change. Such nuances are critical to understanding how pro-
grams may (or may not) translate to the impacts we test for in our analysis.
Using the Ban as a Natural Experiment for Denying Benefits
The goal of this paper is to test these competing theories using state variation in imple-
mentation of the drug felony ban as a natural experiment. Specifically, our goal is to
determine whether changes to the drug felony ban led to material changes in the rate of
recidivism for the prison population of drug offenders. To do this, we tested the impact of
the ban by looking at differences in recidivism for offenders convicted before and after the
ban’s initial adoption. Earlier iterations of this paper also considered whether interim
changes (i.e., modifications) to the ban’s application impacted offender outcomes. How-
ever, because these changes occur on the basis of calendar date rather than conviction date,
the strength of our identification is arguably weaker and results are less informative. As a
result we have excluded these analyses from the paper. Nevertheless it can be noted that
results from these additional analyses were consistent with the findings of this paper.
4 In fact, there is explicit mention of trading benefits for drugs and the associated penalties in the SNAP
benefit application form in Louisiana. (http://www.dcfs.louisiana.gov/assets/docs/searchable/ EconomicStability/Applications/OFS4_4I.pdf).
J Quant Criminol (2018) 34:741–773 745
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Across 10 states where we tested impacts for men and women (16 tests altogether), none
showed significant changes resulting from ban modification.
Later sections describe the data and methods we used for this analysis in greater detail;
however, an important, upfront acknowledgement is that our data do not allow us to
identify individual eligibility (or receipt) of benefits for specific offenders. Thus we cannot
estimate the ban’s impact as it affected specifically those whose eligibility was altered or
denied by the ban. Instead, we estimate the impact of the ban as it was ‘‘assigned’’ (by its
passage) to all offenders, regardless of eligibility. In the parlance of statistical evaluation,
our estimated treatment effect is modeled using an ‘‘intent-to-treat’’ (ITT) framework,
rather than as an estimate of the ‘‘treatment on the treated’’ (TOT) (Angrist 2006). Nev-
ertheless our investigation does inform an important policy-level consideration: Can
removal or modification of the ban reduce the size of the prison population? Will it result
in savings for corrections agencies?
Such questions are even more important when considering whether the ban ever led to
actual changes in the practices it was meant to influence in the first place. For example,
Butcher and LaLonde (2006) show that in Cook County, Illinois, bans on TANF receipt did
not significantly affect attachment to the welfare system for drug felons. 5 Whatever the
reason, such a finding implies that removal of the ban will have no impact since, as it is
designed, it does not achieve its primary goal of denying benefits. In cases such as this, the
question of ‘‘do benefits matter?’’ is secondary to the policy concern, ‘‘does the ban work?’’
Our ITT analysis informs a question much like the latter—‘‘does the ban create meaningful
system-level change?’’
State Implementation of the Drug Felony Ban
Since the PRWORA became law, states have varied considerably in their response to the ban
and the timing of that response. Within 18 months of PRWORA enactment, 4 states had opted
out ofthe banentirely; today thatnumber has grown to14. 6 Twenty-sixstateshavemodifiedthe
ban to allow benefits, subject to additional requirements imposed on drug felons specifically.
Ten states have not altered their use of the ban at all. Though we could not confirm the status of
Wyoming’s laws, best indications are that Wyoming has a full ban in place.
States’ initial adoption of the ban can be classified as one of three types of changes: (1)
moving from no ban to a full ban, (2) moving from no ban to a partial ban, or (3) opting out
immediately. One state with available data opted out immediately: New York.
The meanings of full ban and no ban are clear: full ban implies total adoption of the
PRWORA provision (i.e., felony drug offenders are completely barred from receiving
SNAP or TANF benefits) and no ban implies no ban was in place (i.e., felony drug
offenders do not face special conditions). The meaning of partial ban is more ambiguous.
States with partial bans impose at least some special conditions for eligibility, and in
5 The analysis of Butcher and LaLonde raises an interesting question of whether state agencies are in fact
complying with the federal law. Though we cannot say with absolute certainty that every state complies, evidence gathered for this research (e.g., SNAP application forms asking about drug conviction status, and a conversation with a Massachusetts congressional representative) suggests that policies have resulted in operational changes at the agency level. (http://www.dcfs.louisiana.gov/assets/docs/searchable/ EconomicStability/Applications/OFS4_4I.pdf). 6 Gabor and Botsko (1998) report that 10 states opted out of the ban on food stamps in the year following
the PRWORA ban. Those results were based on a survey of states and only report responses for the food stamp portion of the ban. Our independent research has led us to conclude that only 4 states had fully opted out of both aspects of the ban (i.e. completely removed restrictions to both SNAP and TANF).
746 J Quant Criminol (2018) 34:741–773
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practice, these conditions can vary considerably across states. 7 For example in Iowa, drug
felons are only eligible for benefits if they participate in drug treatment. In Louisiana, drug
felons only become eligible one year after their release. In Florida, drug felons convicted of
possession are eligible, while those convicted of trafficking are not. Given the hetero-
geneity within states’ use of partial bans, we do not to attempt to tease out impacts of
various forms of partial restrictions. That is to say that we do not attempt to measure
differential impacts between, e.g., ‘‘random drug testing’’ and ‘‘required drug treatment.’’
Finally, it should be noted that while the PRWORA itself denied benefits to all
offenders for SNAP and TANF simultaneously, modifications have sometimes addressed
these programs separately, in both substance and timing. For example, Washington first
removed the ban on SNAP benefits in October 2004, then removed the ban on TANF
benefits almost a year later, in September 2005. Changes of this nature are the exception
rather than the rule; most states have modified both SNAP and TANF eligibility
requirements at the same time (Ekstrand 2005).
Data
For this study, we combined prison data, legislative data and county-level data compiled by
the US Census to construct a single analytic dataset. Prison data come from the National
Corrections Reporting Program (NCRP)—an annual data collection program (operated by
the Bureau of Justice Statistics) that collects prison admission and release data for indi-
vidual offenders in every state across the US These offender-level data include information
on offender characteristics such as sex, age and race, and sentence information such as
offense type, time spent in prison and sentence length.
Though NCRP data go back as far as 1983, known issues with data reliability make
much of the early data problematic (Rhodes et al. 2012; Neal and Rick 2014; Pfaff 2011).
More recently, NCRP data collection and assembly have been redesigned to provide more
reliable information (Rhodes et al. 2012). Data are now constructed as longitudinal, panel
datasets (called ‘‘term files’’) tracking individual offenders and their movements into and
out of prison over a given reporting period (Luallen et al. 2012). Reporting periods covered
in the NCRP data vary from state to state, with the most common window beginning in
January 2000 and extending to December 2014.
There are only six states in the NCRP with data extending back to 1996 where impact
estimates are possible: California, Florida, Georgia, Illinois, Michigan, and Minnesota. 8 Given
that our interest is in analyzing the impact of the ban when it was first passed in 1996, only these
states can provide an unbiased sample of offenders who entered prison during that time.
We also assembled legislative data on a state-by-state basis so that we could control for
state-level changes in ban use over time. We compiled this data using multiple sources.
One source was the ‘‘State Options Reports’’ published by the Food and Nutrition Service
(FNS) (US Department of Agriculture 2016). These survey-based reports provide high-
7 Broadly, states adopt three types of partial reforms: (1) requirements for offenders to participate in or
complete treatment before receiving benefits; (2) allowance for drug offenders who committed less serious crimes to access benefits; and (3) allowance for offenders to receive benefits after a probationary period following release. 8 New York has data back going back to 1994, but opted out immediately after the ban was passed. We
separately tested our pooled estimation with and without New York and found no difference in findings between models.
J Quant Criminol (2018) 34:741–773 747
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level summaries of each state’s policies regarding the drug ban and modifications thereof.
They extend back to 2002 and are typically published once every one to two years. We
augmented these reports with independent web searches and queries in a legal database
(Westlaw). In a number of cases our search results conflicted with the FNS reports. 9 In
those cases, we disregarded the FNS survey data in favor of source documents.
Table 1 below provides a summary of relevant state laws and NCRP reporting windows
for all 50 states. Though our sample used only a subset of these states, the complete
table provides a useful resource for researchers. It does not document every legal change that
has occurred over time; rather, it describes major policy shifts as defined earlier in this paper.
Finally, we supplemented these data with county-level information compiled by the US
Census Bureau. These data include county-level descriptions of population density, eco-
nomic conditions (such as poverty rates and household income), education level and SNAP
participation rates. Most of these data are made available through Census’s USA counties
data products, though some information (including rates of SNAP recipiency) is reported
as part of Census’s intercensal estimates.
Method
To estimate the impact of the ban, we combined two popular inferential methods for
estimating causal effects: regression discontinuity (RD) design and difference-in-differ-
ences (DiD) estimation. Our use of RD design provides defensible measures of causal
impacts by minimizing observed and unobserved differences between comparison groups.
Our use of second-differencing (DiD) strengthens the credibility of these results by con-
trolling for other possible coincident, exogenous shocks that may also have impacted
recidivism but were not the result of the ban. We explain our use of each.
The motivation for our quasi-experimental approach is straightforward. Consider first a
simple approach that estimates ban impacts as the unadjusted pre-post comparison between
treated and untreated groups (in this case, average outcomes before vs. after the ban). In
order for estimates to be unbiased, before and after groups must be characteristically
equivalent with respect to measures correlated with the outcome. That condition is unlikely
to hold without adjustment; however, even with adjusted comparisons one cannot reject
that possibility that unobserved group differences correlated with the outcome still exist.
The problem worsens when unobserved differences are changing (or trending) in the pre
and post periods. Quasi-experimental methods can overcome such limitations and, in the
context of our analysis, we use RD to do this.
RD designs operate under a simple premise: unbiased treatment effects can be identified
when the probability of treatment is a discontinuous function of one or more underlying
measures (Imbens and Lemieux 2008; Cameron and Trivedi 2005), also called forcing
variables. Discontinuities occur at specific thresholds (or cutoffs), such that treatment
assignment depends (discontinuously) on whether individuals fall above or below the
cutoff. By extension, when individuals have imprecise control over the assignment to
treatment, treatment–control comparisons in a local neighborhood around the cutoff can be
analyzed like randomized experiments (Lee and Lemieux 2010). That is to say that nearby
9 Apparent confusion by states as to what is meant by ‘‘ban modification’’ has led to reporting error in the
State Options Report, and subsequently, confusion in the literature as to what states have adopted what policies and when. For example, although Iowa imposes some drug rehabilitation services (or other requirements) for former drug felons, FNS reports show it has opted out since 2006.
748 J Quant Criminol (2018) 34:741–773
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Table 1 (a) List of ban modification statutes and enactment dates identified for analysis, (b) dates and statutes ban modifications used in analysis
State Modification 1 Modification 2 NCRP
Type Date Bill/law Type Date Bill/law Start End
(a)
Alabama None NA – NA NA – 2007 2014
Alaska None NA – NA NA – 2005 2013
Arizona None NA – NA NA – 2000 2014
Arkansas Partial 4/1/97 Ark. Code Ann. § 20-76-409 H.B.1295
NA NA – – –
California Partial 7/1/05 AB 1796/Cal. Welf. and Inst. Code § 18901.3
Opted- out
4/1/ 15
AB 1468 § 49 1992 2014
Colorado Partial 7/1/97 Colo. Rev. Stat. §§ 26-2-305, 26-2-706
NA NA – 2000 2014
Connecticut Partial 6/18/97 PA 97-2/Conn. Gen. Stat. § 17b-112d
NA NA – – –
Delaware Partial 7/17/03 HB 263/Del. Code Ann. tit. 31, § 605
Opted- out
7/1/ 11
SB 12/31 Del. C. § 512
2009 2014
Florida Partial 5/30/97 Fla. Stat. Ann. ch. 414.095
NA NA – 1996 2014
Georgia None NA – NA NA – 1971 2014
Hawaii Opted- out
6/16/97 HB No. 480/Haw. Rev. Stat. § 346-53.3
NA NA – – –
Idaho Partial 7/1/00 HB 627/Idaho Code § 56-202
NA NA – 2008 2012
Illinois Partial 7/1/97 730 Ill. Comp. Stat 5/1-10
NA NA – 1989 2013
Indiana Partial 7/1/05 SB 523/Ind. Code § 12-20-16-6
NA NA – 2002 2014
Iowa Partial 1/11/97 HF 20/Iowa Code § 239B.5
NA NA – 2006 2014
Kansas Partial 7/1/06 HB 2861/SB 243 NA NA – 2011 2014
Kentucky Partial 7/15/98 Ky. Acts ch. 427, sec. 12/KRS § 205.2005
NA NA – 2000 2013
Louisiana Partial 7/1/97 No. 1351/LSA- R.S. 46:233.2
NA NA – – –
Maine Opted- out
4/2/02 H.P. 1665 L.D. 2170/Me. Rev. Stat. Ann. tit. 22, §§ 3104(14), 3762(17)
NA NA – 2012 2014
Maryland Partial 7/1/00 Md. Ann. Code 88A, §§ 50A, 65
Opted- out
10/ 1/ 07
Acts 2007, c. 3, §8
2000 2012
J Quant Criminol (2018) 34:741–773 749
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Table 1 continued
State Modification 1 Modification 2 NCRP
Type Date Bill/law Type Date Bill/law Start End
Massachusetts Partial 12/1/01 2001 MA. Adv. Legis. Serv. 177, § 4400-1000
NA NA – 2010 2014
Michigan Partial 8/18/97 1997 Mich. Pub. Acts 109, § 622
NA NA – 1989 2013
Minnesota Partial 7/1/97 SF 1/MN. Stat. § 256D.024
NA NA – 1994 2014
Mississippi None NA – NA NA – 2004 2014
Missouri Partial 8/28/14 SB 680/MO. Stat. § 208.247
NA NA – 2000 2014
Montana Partial 7/1/05 SB 29/MT. Stat. 53-4-231
NA NA – 2010 2014
Nebraska Partial 5/13/03 LB 667/Neb. Rev.Stat. § 68-1017.02
NA NA – 2000 2014
Nevada Partial 1/1/98 Nev. Rev. Stat § 422.29316
NA NA – 2008 2014
(b)
New Hampshire
Opted- out
8/1/97 N.H. Rev. Stat. Ann. § 167:81-a
NA NA – 2011 2014
New Jersey Partial 11/1/96 No. 15/N.J. Stat. Ann. § 44:10-48
Opted- out
11/ 1/ 09
No. 4197/N.J. Stat. Ann. § 44:10-48.1
2003 2013
New Mexico Opted- out
5/15/02 HB 11/N.M. Stat. Ann. § 27-2B- 11(c’)
NA NA – 2010 2014
New York Opted- out
8/1/97 N.Y. Laws § 121436
NA NA – 1994 2014
North Carolina
Partial 7/1/97 N.C. Gen. Stat. § 108A-25.2
NA NA – 1999 2014
North Dakota None NA – NA NA – 2002 2014
Ohio Opted- out
10/16/09 HB 1/Ohio Rev. Code Ann. § 5101.84
NA NA – 2009 2013
Oklahoma Opted- out
6/13/97 HB 2170/1997 Okla. Sess. Law Serv. Ch. 414
NA NA – 2000 2014
Oregon Opted- out
7/1/97 Or. Rev. Stat. § 411.119 Ch. 581 S.B. No. 825
Partial 8/ 16/ 05
Ch. 706 H.B No. 2485 OR ST 411.119
2001 2013
Pennsylvania Partial 12/23/03 HB 44/62 Pa. Stat. § 405.1(i)
NA NA – 2001 2014
750 J Quant Criminol (2018) 34:741–773
123
the cutoff, groups are assumed to be characteristically equivalent along observed and
unobserved measures.
For our analysis, we used this logic of RD design to identify ban impacts. In this case,
treatment is identified on the basis of conviction date—felons convicted on or before
August 22, 1996 were eligible for benefits upon release and those convicted after were not.
The date of conviction acts as the forcing variable and the discontinuity is estimated as the
average difference in outcomes for offenders convicted just before and just after August
22. 10
We used prison admission date as a proxy for conviction date because we do not
observe actual date of conviction. 11
Table 1 continued
State Modification 1 Modification 2 NCRP
Type Date Bill/law Type Date Bill/law Start End
Rhode Island Opted- out
7/1/04 Family Independence Act Amendment/ R.I. Gen. Laws §§ 40-5.1-8, 40-6-8
NA NA – 2004 2014
South Carolina
None NA – NA NA – 2000 2014
South Dakota Opted- out
3/5/09 HB1123/SDCL § 28-12-3
NA NA – 2000 2012
Tennessee Partial 5/14/02 Tenn. Code Ann. §§ 71-3-154, 71-5-308
NA NA – 2000 2014
Texas None NA – NA NA – 2005 2014
Utah Partial 7/4/97 Utah Code Ann. § 35A-3-311
NA NA – 2000 2014
Vermont Opted- out
Unknown 1997 Vt. Laws 61, § 131
NA NA – – –
Virginia Partial 3/22/05 § 63.2-505.2 NA NA – – –
Washington Partial 10/1/98 HB 3901/Wash. Rev. Code § 74.08.025
Opted- out
9/1/ 05
SB 6411/Wash. Rev. Code § 74.08.025
2000 2014
West Virginia None NA – NA NA – 2006 2014
Wisconsin Partial 10/1/97 Wis. Stat. §§ 49.79, 49.145, 49.148
NA NA – 2000 2014
Wyoming None NA – NA NA – 2006 2014
10 A large number of studies have used date/time as an assignment variable modeled within an RD
framework. Table 5 in Lee and Lemieux (2010) provides a nice summary of many such studies. Because time is the forcing variable, our approach can also be described as an ‘‘event study’’—language more common to various social science disciplines. 11
We argue that prison admission is a good proxy for date of conviction. Prior to conviction, most offenders are housed in jails rather than prisons. After conviction, most offenders are moved to prison quickly.
J Quant Criminol (2018) 34:741–773 751
123
To be credible, RD analysis requires some assumptions be met. One assumption
(mentioned above) is that individuals do not have precise control over their treatment
status. In this case, it is to say that offenders (as well as prosecutors, defenders and judges)
do not precisely control the timing of conviction. Where this assumption is not met,
systematic selection in the timing of drug convictions can threaten validity. Given the
power that attorneys and judges possess, we cannot dismiss that possibility that gaming of
conviction dates can occur; however, we argue it is unlikely that prosecutorial or sen-
tencing practices were manipulated to systematically favor some drug offenders over
others.
To test whether there is any evidence that manipulation in convictions around the date
of the cutoff (August 22) occurred, we borrow from an empirical test offered in Jacob et al.
(2012). Specifically, we construct two local linear regressions, one to the left of the cutoff
and one to the right, that model the percent of sampled drug offenders admitted during each
week (as the dependent variable) over time (as the independent variable). We then test
whether the intercepts just to the left and just to the right are statistically different from one
another. Estimated intercepts and their differences before and after the cutoff are reported
in Table 2 for both men and women using a 6-month window of drug offender admissions.
Overall these results confirm there is no evidence of systematic manipulation in convic-
tions around the cutoff.
Another assumption of our RD design is that no other changes occurred simultaneously
with the timing of the ban that affected recidivism for reasons other than the ban itself.
Though we were not able to find any evidence that such a change took place, we cannot
directly prove or disprove this condition exists. Instead, we overcome this limitation by
incorporating DiD estimation as part of our identification strategy. Specifically, we com-
pared changes around the ban for drug offenders (a group affected by the ban) to similar
changes around the ban for nondrug offenders (a group not affected by the ban). In the
language of difference-in-differences, estimated impacts within groups (before vs. after)
are first differences, and differences in impacts across groups (drug vs. nondrug) are second
differences.
The strength of the DiD estimator is that it zeros out bias (in estimated first differences)
resulting from unobserved changes also affecting recidivism and closely coinciding with
the ban. To accomplish this, DiD identification assumes a constant bias among compared
groups such that any unobservable bias impacts groups equally in the absence of treatment
(Lechner 2010; Angrist et al. 2009). Thus our application assumes that factors affecting
changes in recidivism around the time of, but not as a result of, the ban affect drug and
nondrug offenders equally. Traditional DiD models also assume that groups follow similar
trends absent the treatment (or ‘‘constant trends’’); however, because our impacts are
estimated as discontinuous jumps (i.e., using RD), assumptions about constant trends are
not necessary.
Using this framework, we examined the data in two ways. First, we generated graphical
illustrations depicting observed prison return rates for offenders convicted just before and
after the ban. Descriptive graphics of this kind are commonly used in regression discon-
tinuity analyses because they can provide useful insights about the nature of the impact
being estimated and the strength of the identification. Second, we estimated DiD impacts
using Cox-proportional hazards models—models that are well known to the literature on
survival estimation (Cameron and Trivedi 2005; Klein and Moeschberger 2003; Allison
2010). We present the equations and discuss the details of our model specification below.
Equations (1) and (2) estimate the probability of reincarceration for offenders released
from prison as a function of time at risk. Risk of reincarceration begins on the day an
752 J Quant Criminol (2018) 34:741–773
123
offender exits prison, and offenders are followed until a known event occurs or until the
end of the data window, at which point the data are right-hand censored. Offenders are
followed for as long as the NCRP data currently allow—until December 31, 2014 in most
cases.
Both equations share the same specification but are estimated on different samples (drug
and nondrug offenders). For drug offenders, we estimate:
kdij t Tij;Pre; Tij;Post; Ban; M; Xij; Cj � �
� �
¼ kd0ðtÞe ðb1Tij;Preþb2Tij;Postþsd ðBanÞþqdðMÞþpXdijþlC
d j Þ ð1Þ
Similarly, for nondrug offenders we estimate:
kndij t Tij;Pre; Tij;Post; Ban; M; Xij; Cj � �
� �
¼ knd0 ðtÞe ða1Tij;Preþa2Tij;Postþsnd ðBanÞþqnd ðMÞþdXndij þlC
nd j Þ ð2Þ
In both equations,
kijðtÞ is the probability of return to prison for the ith offender from the jth county as a function of time (t) since release from prison; superscript d denotes drug offenders;
superscript nd denotes nondrug offenders.
k0ðtÞ is the baseline hazard function common to all offenders, also a function of time since release; again superscript d indicates drug offenders; nd denotes nondrug
offenders.
t is time since prison release, beginning at zero and increasing by one each day an
offender is at liberty.
Tij;Pre is the number of days before PRWORA enactment, based on prison admission
date for the ith offender from the jth county. Admissions after enactment have a value of
zero.
Table 2 Estimated proportion of sample admitted (weekly) to prison around the cutoff (august 22nd)
Men Women
Left Right Difference Left Right Difference
Pooled 0.019** (0.001)
0.021** (0.001)
-0.001 (0.002)
0.017** (0.002)
0.019** (0.002)
-0.002 (0.002)
CA 0.020** (0.001)
0.021** (0.001)
-0.001 (0.002)
0.018** (0.002)
0.021** (0.002)
-0.002 (0.002)
FL 0.020** (0.002)
0.021** (0.002)
-0.002 (0.002)
0.017** (0.003)
0.016** (0.003)
0.001 (0.004)
GA 0.017** (0.002)
0.017** (0.002)
0.000 (0.002)
0.016** (0.005)
0.014** (0.004)
0.002 (0.006)
IL 0.019** (0.002)
0.021** (0.001)
-0.002 (0.002)
0.016** (0.003)
0.019** (0.003)
-0.002 (0.004)
MI 0.016** (0.002)
0.023** (0.002)
-0.007* (0.003)
0.016** (0.005)
0.026** (0.005)
-0.010 (0.006)
MN 0.019** (0.004)
0.020** (0.004)
0.000 (0.005)
0.044** (0.015)
0.046** (0.009)
-0.002 (0.018)
Standard errors are reported in parentheses. Stars denote p-values for statistical tests of differences from zero: * indicates a value of 0.05; ** indicates a value \0.01. Numbers are subject to rounding error
J Quant Criminol (2018) 34:741–773 753
123
Tij;Post is the number of days after PRWORA enactment, based on prison admission date
for the ith offender from the jth county. Admissions before enactment have a value of
zero.
Ban is an indicator variable equal to 1 if an offender was admitted to prison after
PRWORA.
M is a time-varying covariate for ban modification. It is specified as an indicator variable
equal to 1 if an offender is at liberty to fail in a period where a modified ban has been
introduced. This variable will only take on a value of 1 if the modified ban was
introduced more than a year after PRWORA. Modified bans introduced within a year of
PRWORA are characterized as part of the impact of the initial change.
Xij is a vector of individual characteristics for the ith offender from the jth county
including age at the time of release from prison, time served in prison and year of
release.
Cj is a vector of county-level characteristics for the ith offender from county j, including
percentage of households in poverty, median household income, local unemployment,
adult population density and high school education.
For these equations: (b1 and b2) and (a1 and a2) capture the time trends in outcomes before and after the ban for drug offenders and nondrug offenders respectively; sd and snd
represent the treatment effect of the ban (i.e., the first difference) for drug offenders and
nondrug offenders respectively; qd and qnd represent the average difference in outcomes for drug and nondrug offenders in the modified period; and p, d and l capture other baseline differences in offender and community characteristics.
Equation (3) estimates the overall impact of the ban as the difference between estimated
treatment effects between groups. For this equation, sd and snd are defined as before and the second difference, Ds, describes the impact of the ban itself.
Ds ¼ ŝd � ŝnd ð3Þ
There are other practical considerations for our estimation. The first is how to identify/label
offenders as drug offenders subject to the ban. This is challenging because (1) offenders can be
chargedwithmultipleoffenseswithvaryingdegreesofseriousness;(2)NCRPdataonlyrecords
the top three, most serious offenses; (3) NCRP datado not denote which conviction offenses are
felonies and which are misdemeanors, a criterion for the application of the ban; and (4) drug
crime admissions can be for revocations (where no new conviction occurs), rather than for new
crimes that are subject to the ban (because a conviction does occur).
Given these limitations, we identify (a) drug offender status based on offense type for
the first two convicted sentences; and (b) admission status based on the type of admission
labeled in the NCRP, i.e., restricting the sample to new court commitments only. 12 We also
conducted a sensitivity analysis that defined a drug offender using the first offense only and
found results were substantively unchanged. Drug offender status is also carried forward so
that, once observed, an offender is labeled a drug offender even when readmitted for a
nondrug offense. Nondrug offenders are defined as offenders with no prior conviction for a
drug offense.
12 \15% of offenders in our analytic sample are convicted of more than two offenses and, of these, \2% have nondrug offenses for their first two offenses and a drug-related offense for their third offense. Since we cannot know whether this third offense is a felony or misdemeanor, we treat these cases as nondrug offenders.
754 J Quant Criminol (2018) 34:741–773
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A second consideration is determining the optimal size of the interval around the cutoff.
Larger intervals provide bigger samples for analysis and improve statistical power, but
increase the potential for omitted variable bias, especially from poorly specified trends.
Conversely, smaller intervals provide the most robust identification but may be too
imprecise to reject the null even where true impacts exist. To achieve a balance in light of
these tradeoffs, we report estimates across multiple intervals around the cutoff. Specifi-
cally, we estimate and compare impacts from four samples of offenders convicted (±)
6 months, 1, 2, and 3 years around the cutoff. This allows us to better judge the overall
strength and robustness of our findings.
Tables 3 and 4 report the size of each sample and observed returns to prison for male
and female populations (respectively) in each state and for the pooled sample. Drug and
nondrug offenders are reported separately. Overall these tables show that most samples are
sufficiently sized to detect moderate to large differences in most cases, and small differ-
ences in at least some states (particularly in California, Florida, Georgia, Illinois and the
pooled sample). 13
A third consideration is how to estimate impacts on the pooled sample of states.
Specifically, estimates can be weighted so that they represent (a) the average impact across
individuals or (b) the average impact across states. Each statistic says something different
and, without a specific application in mind, it is not clear which one is more interesting
from a policy perspective. Estimates giving equal weight to individuals will naturally over
represent larger states (such as California) and, in turn, idiosyncratic patterns of practice;
however, they will be more precise than estimates weighing states equally. Our solution for
this paper is to report both sets of pooled estimates: those weighting individuals equally
(shown in Tables 5 and 6) and those weighting states equally (shown in Table 7).
A fourth concern is how to best specify time trends in estimation. More flexible time
trends modeled using higher-order polynomials may provide better fits to the data (relative
to simple linear trends), but can suffer from overfitting and run a greater risk of introducing
bias as a result (Gelman and Imbens 2014). To address this concern, we (1) visually
inspected the data to determine the best approach, and (2) tested the sensitivity of our
results to alternative specifications. Based on the results of our inspections (presented in
‘‘Graphical Analyses’’), we adopted an approach using simple linear trends to model the
discontinuity, and tested the robustness of these models against quadratic and third-order
specifications of time trends.
Finally, an important consideration for estimation is that admission cohorts in two
states, Florida and Minnesota, do not extend a full three years (i.e., 36 months) back from
August 22, 1996. In Florida, admission cohorts begin January 1, 1996 (6 months before)
and in Minnesota they begin January 1, 1994 (30 months before).
The implication for this design is that cohorts of offenders are not evenly observed in
the data. Offenders admitted before the start of a term file window are only observed when
released during a term file year. In the case of Florida, offenders convicted January 1, 1995
are only observed if they served at least one full year in prison (i.e., released sometime
after January 1, 1996). Those serving 364 days (i.e., released December 31, 1995) are
unobserved and thus omitted from the sample.
13 For reference, computations of detectable effects performed in Stata (using the stpower command) show
that sample sizes of 200, 500, 3,000, and 10,000 can detect minimum differences in recidivism rates of roughly 0.40, 0.25, 0.10, and 0.05 respectively. These computations assume a two-sided test of a Cox model where the standard deviation of the Ban/Mod covariate is 0.5, power is 0.8, and alpha is 0.05.
J Quant Criminol (2018) 34:741–773 755
123
Given that term file windows in all states overlap the ban implementation date, uneven
sample selection is not a fundamental threat to our identification strategy; however, bias
may still result if trends in observed recidivism leading up to the ban are not adequately
controlled for. As before, graphical illustrations (shown in the ‘‘Appendix’’) provide a
Table 3 Sample sizes for drug offenders and returns to prison in each state
Sex Sample N Pooled CA FL GA IL MI MN
Men 6-month Total 32,417 16,331 4778 3032 6692 1226 358
Returning 18,204 8811 2652 1620 4340 578 203
1-year Total 65,617 33,138 9569 6077 13,673 2445 715
Returning 36,856 17,816 5392 3262 8849 1141 396
2-year Total 129,815 65,346 18,426 11,999 27,519 4981 1544
Returning 72,932 35,191 10,427 6398 17,728 2338 850
3-year Total 192,928 95,231 28,113 18,454 41,222 7473 2435
Returning 108,534 51,328 16,062 9770 26,557 3470 1347
Women 6-month Total 4474 2468 579 383 885 115 44
Returning 2325 1357 247 156 503 44 18
1-year Total 9201 5053 1269 718 1809 251 101
Returning 4789 2796 529 297 1035 95 37
2-year Total 17,907 9796 2415 1442 3449 565 240
Returning 9233 5416 998 577 1941 211 90
3-year Total 26,270 14,216 3656 2177 5063 817 341
Returning 13,427 7738 1536 857 2852 307 137
Table 4 Sample sizes for nondrug offenders and returns to prison in each state
Sex Sample N Pooled CA FL GA IL MI MN
Men 6-month Total 100,984 58,888 13,057 8063 11,839 6574 2563
Returning 65,702 42,447 6528 4122 7591 3389 1625
1-year Total 205,374 120,294 26,102 16,885 23,877 13,076 5140
Returning 133,638 86,610 13,173 8711 15,319 6603 3222
2-year Total 405,179 238,304 48,778 33,277 48,561 26,097 10,162
Returning 264,425 171,992 24,547 17,107 31,242 13,143 6394
3-year Total 599,597 351,432 69,568 51,234 73,000 39,173 15,190
Returning 390,753 253,498 34,984 26,206 46,938 19,665 9462
Women 6-month Total 8940 5218 958 1003 1110 481 170
Returning 5133 3388 354 452 638 216 85
1-year Total 17,992 10,541 1962 1917 2276 932 364
Returning 10,370 6891 732 840 1332 398 177
2-year Total 35,423 20,829 3659 3693 4611 1883 748
Returning 20,467 13,689 1341 1574 2700 804 359
3-year Total 52,024 30,469 5226 5524 6787 2912 1106
Returning 29,920 19,912 1929 2342 3972 1252 513
756 J Quant Criminol (2018) 34:741–773
123
T a b le
5 E st im
a te d im
p a c ts
a m o n g w o m e n u si n g p o o le d sa m p le
W in d o w
a ro u n d c u to ff
6 -m
o n th
1 -y e a r
2 -y e a r
3 -y e a r
D ru g
N o n d ru g
D ru g
N o n d ru g
D ru g
N o n d ru g
D ru g
N o n d ru g
B a n
1 .0 1 1
0 .0 8 8
0 .9 9 5
0 .0 5 7
0 .9 9 6
0 .0 6 0
1 .0 1 3
0 .0 4 1
1 .0 1 7
0 .0 4 3
1 .0 1 0
0 .0 2 9
0 .9 6 4
0 .0 3 3
0 .9 9 1
0 .0 2 3
M o d ifi c a ti o n
0 .3 2 5 * * *
0 .0 5 5
0 .2 9 6 * * *
0 .0 3 6
0 .3 3 0 * * *
0 .0 3 9
0 .3 6 6 * * *
0 .0 3 0
0 .3 7 3 * * *
0 .0 3 0
0 .3 9 7 * * *
0 .0 2 2
0 .3 8 9 * * *
0 .0 2 5
0 .4 2 1 * * *
0 .0 1 9
% in
P o v e rt y
1 .0 0 7
0 .0 1 4
0 .9 9 9
0 .0 0 8
1 .0 0 1
0 .0 1 0
0 .9 9 6
0 .0 0 6
1 .0 0 6
0 .0 0 7
0 .9 9 1 *
0 .0 0 4
1 .0 0 0
0 .0 0 6
0 .9 9 2 *
0 .0 0 4
M e d ia n in c o m e
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
U n e m p lo y m e n t
1 .0 2 8 *
0 .0 1 5
1 .0 4 5 * * *
0 .0 0 9
1 .0 1 6
0 .0 1 0
1 .0 4 3 * * *
0 .0 0 7
1 .0 2 6 * * *
0 .0 0 7
1 .0 4 4 * * *
0 .0 0 5
1 .0 2 7 * * *
0 .0 0 6
1 .0 4 0 * * *
0 .0 0 4
P o p u la ti o n d e n si ty
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0 *
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
P e rc e n t o f H S e d u c a te d a d u lt s
1 .0 2 4 * *
0 .0 0 8
1 .0 1 2 * *
0 .0 0 4
1 .0 1 4 * *
0 .0 0 5
1 .0 1 2 * * *
0 .0 0 3
1 .0 1 3 * * *
0 .0 0 4
1 .0 1 3 * * *
0 .0 0 2
1 .0 1 2 * * *
0 .0 0 3
1 .0 1 3 * * *
0 .0 0 2
A g e a t re le a se
0 .9 7 3 * * *
0 .0 0 3
0 .9 8 4 * * *
0 .0 0 2
0 .9 7 4 * * *
0 .0 0 2
0 .9 8 3 * * *
0 .0 0 1
0 .9 7 6 * * *
0 .0 0 1
0 .9 8 4 * * *
\ 0 .0 0 1
0 .9 7 5 * * *
0 .0 0 1
0 .9 8 3 * * *
\ 0 .0 0 1
T im
e -s e rv e d
1 .0 0 0 * *
\ 0 .0 0 1
0 .9 9 9 * * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
0 .9 9 9 * * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
R e le a se
y e a r
1 .0 5 3
(0 .0 4 5 )
1 .0 5 3
(0 .0 4 5 )
1 .0 0 3
(0 .0 2 9 )
1 .0 0 3
(0 .0 2 9 )
1 .0 2 4
(0 .0 2 1 )
1 .0 2 4
(0 .0 2 1 )
1 .0 1 4
(0 .0 1 7 )
1 .0 1 4
(0 .0 1 7 )
P re -t re n d
0 .9 9 9
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0 * *
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
P o st -T re n d
1 .0 0 0
1 .0 0 0
1 .0 0 0
1 .0 0 0
1 .0 0 0
1 .0 0 0
1 .0 0 0
1 .0 0 0
J Quant Criminol (2018) 34:741–773 757
123
T a b le
5 c o n ti n u e d
W in d o w
a ro u n d c u to ff
6 -m
o n th
1 -y e a r
2 -y e a r
3 -y e a r
D ru g
N o n d ru g
D ru g
N o n d ru g
D ru g
N o n d ru g
D ru g
N o n d ru g
S ta te
F ix e d E ff e c ts
Y e s
Y e s
Y e s
Y e s
Y e s
Y e s
Y e s
Y e s
N 1 3 ,1 7 7
2 6 ,7 3 3
5 2 ,4 9 0
7 6 ,8 1 8
E st im
a te d D iD
B a n Im
p a c t (D )
0 .0 1 6
- 0 .0 1 7
0 .0 0 7
- 0 .0 2 8
0 .1 0 5
0 .0 7 3
0 .0 5 1
0 .0 4 2
T h is ta b le re p o rt s c o e ffi c ie n ts a s d e sc ri b e d in
E q s. (4 )– (6 ), c o n v e rt e d in to
h a z a rd
ra ti o s. S ta n d a rd
e rr o rs a re
re p o rt e d in
p a re n th e se s. S ta rs d e n o te p v a lu e s fo r st a ti st ic a l te st s o f
d if fe re n c e s fr o m
z e ro : * in d ic a te s a v a lu e o f 0 .0 5 ; * * in d ic a te s a v a lu e o f 0 .0 1 ; * * * in d ic a te s a v a lu e o f 0 .0 0 1 . N u m b e rs
a re
su b je c t to
ro u n d in g e rr o r
758 J Quant Criminol (2018) 34:741–773
123
T a b le
6 E st im
a te d im
p a c ts
a m o n g m e n u si n g p o o le d sa m p le
W in d o w
A ro u n d C u to ff
6 -m
o n th
1 -y e a r
2 -y e a r
3 -y e a r
D ru g
N o n d ru g
D ru g
N o n d ru g
D ru g
N o n d ru g
D ru g
N o n d ru g
B a n
1 .0 1 3
0 .0 3 1
0 .9 7 8
0 .0 1 6
0 .9 9 6
0 .0 2 1
0 .9 9 7
0 .0 1 1
0 .9 7 6
0 .0 1 5
0 .9 9 8
0 .0 0 8
0 .9 6 7 * *
0 .0 1 2
0 .9 8 5 *
0 .0 0 6
M o d ifi c a ti o n
0 .3 8 2 * * *
0 .0 2 0
0 .4 0 8 * * *
0 .0 1 3
0 .3 9 6 * * *
0 .0 1 5
0 .4 1 3 * * *
0 .0 0 9
0 .3 8 4 * * *
0 .0 1 0
0 .4 3 1 * * *
0 .0 0 6
0 .3 9 7 * * *
0 .0 0 8
0 .4 4 0 * * *
0 .0 0 5
% in
P o v e rt y
0 .9 7 7 * * *
0 .0 0 4
0 .9 9 3 * *
0 .0 0 2
0 .9 8 9 * * *
0 .0 0 3
0 .9 9 4 * * *
0 .0 0 2
0 .9 8 9 * * *
0 .0 0 2
0 .9 9 3 * * *
0 .0 0 1
0 .9 8 9 * * *
0 .0 0 2
0 .9 9 1 * * *
\ 0 .0 0 1
M e d ia n in c o m e
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
U n e m p lo y m e n t
1 .0 2 5 * * *
0 .0 0 5
1 .0 3 7 * * *
0 .0 0 3
1 .0 2 2 * * *
0 .0 0 4
1 .0 3 5 * * *
0 .0 0 2
1 .0 2 1 * * *
0 .0 0 3
1 .0 3 3 * * *
0 .0 0 1
1 .0 1 9 * * *
0 .0 0 2
1 .0 3 0 * * *
0 .0 0 1 1
P o p u la ti o n d e n si ty
1 .0 0 0 * *
\ 0 .0 0 1
1 .0 0 0 * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 * *
\ 0 .0 0 1
P e rc e n t o f H S e d u c a te d a d u lt s
1 .0 1 3 * * *
0 .0 0 2
1 .0 2 0 * * *
0 .0 0 1
1 .0 1 3 * * *
0 .0 0 2
1 .0 2 0 * * *
\ 0 .0 0 1
1 .0 1 0 * * *
0 .0 0 1
1 .0 1 8 * * *
\ 0 .0 0 1
1 .0 0 9 * * *
\ 0 .0 0 1
1 .0 1 6 * * *
\ 0 .0 0 1
A g e a t re le a se
0 .9 8 7 * * *
\ 0 .0 0 1
0 .9 9 1 * * *
\ 0 .0 0 1
0 .9 8 7 * * *
0 .0 0 1
0 .9 9 0 * * *
\ 0 .0 0 1
0 .9 8 7 * * *
\ 0 .0 0 1
0 .9 9 0 * * *
\ 0 .0 0 1
0 .9 8 6 * * *
1 .0 0 0
0 .9 9 0 * * *
\ 0 .0 0 1
T im
e -s e rv e d
1 .0 0 0 *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
R e le a se
y e a r
1 .0 3 4 * *
(0 .0 1 3 )
1 .0 3 4 * *
(0 .0 1 3 )
1 .0 2 1 * *
(0 .0 0 9 )
1 .0 2 1 * *
(0 .0 0 9 )
1 .0 1 6 * *
(0 .0 0 6 )
1 .0 1 6 * *
(0 .0 0 6 )
1 .0 1 3 * *
(0 .0 0 5 )
1 .0 1 3 * *
(0 .0 0 5 )
P re -t re n d
1 .0 0 0 * *
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0 * *
\ 0 .0 0 1
1 .0 0 0 * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
P o st -t re n d
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0 *
\ 0 .0 0 1
1 .0 0 0
\ 0 .0 0 1
1 .0 0 0 * * *
\ 0 .0 0 1
1 .0 0 0 *
\ 0 .0 0 1
J Quant Criminol (2018) 34:741–773 759
123
T a b le
6 c o n ti n u e d
W in d o w
A ro u n d C u to ff
6 -m
o n th
1 -y e a r
2 -y e a r
3 -y e a r
D ru g
N o n d ru g
D ru g
N o n d ru g
D ru g
N o n d ru g
D ru g
N o n d ru g
S ta te
fi x e d e ff e c ts
1 .0 1 3
0 .9 7 8
0 .9 9 6
0 .9 9 7
0 .9 7 6
0 .9 9 8
0 .9 6 7 * *
0 .9 8 5 *
N 1 2 9 ,2 7 3
2 6 2 ,7 3 6
5 1 8 ,7 9 1
7 6 7 ,0 5 9
E st im
a te d D iD
B a n Im
p a c t (D )
0 .0 3 6
- 0 .0 0 1
- 0 .0 2 2
- 0 .0 1 8
0 .0 3 4
0 .0 2 4
0 .0 1 7
0 .0 1 4
T h is ta b le re p o rt s c o e ffi c ie n ts a s d e sc ri b e d in
E q s. (4 )– (6 ), c o n v e rt e d in to
h a z a rd
ra ti o s. S ta n d a rd
e rr o rs a re
re p o rt e d in
p a re n th e se s. S ta rs d e n o te p v a lu e s fo r st a ti st ic a l te st s o f
d if fe re n c e s fr o m
z e ro : * in d ic a te s a v a lu e o f 0 .0 5 ; * * in d ic a te s a v a lu e o f 0 .0 1 ; * * * in d ic a te s a v a lu e o f 0 .0 0 1 . N u m b e rs
a re
su b je c t to
ro u n d in g e rr o r
760 J Quant Criminol (2018) 34:741–773
123
convenient shorthand to assess differences in recidivism among these ‘‘selected sample’’
periods. Based on the depictions for Florida and Minnesota, we argue that the impact of
sample selection appears to be minimal. 14
We conclude that the potential for significant
bias in this case is negligible and that our use of a linear trend in pre-periods is a likely
sufficient control.
Results
Graphical Analyses
As described earlier, we conducted graphical analyses in advance of formal estimation for
the pooled sample as well as for each state. Because the output is lengthy, we present only
the results for the pooled sample in the main body of the paper; however, full results are
available in the ‘‘Appendix’’. Figure 1 shows illustrations for the pooled sample. Figures in
the ‘‘Appendix’’ are identically constructed.
Figure 1 shows four graphs. All four graphs depict changes in recidivism, centered on
the timing of (conviction around) the initial ban. The x-axis of each graph denotes the
month of the prison admission and the y-axis denotes the percent of offenders returning to
prison within a 3-year period after release. For each set of illustrations, the top two
illustrations show changes for men and the bottom two show changes for women.
Table 7 Estimated impacts of the initial ban
Women Men
6-month 1-year 2-year 3-year 6-month 1-year 2-year 3-year
CA -0.200 -0.135 -0.059 -0.081 -0.013 -0.058 -0.059* -0.054**
0.130 0.091 0.064 0.053 0.047 0.033 0.023 0.019
FL 0.553 0.254 -0.013 -0.122 0.099 0.159 0.194* 0.179
0.358 0.331 0.404 0.524 0.098 0.084 0.086 0.095
GA 0.636 0.196 0.049 0.212 0.007 -0.061 -0.077 -0.090
0.414 0.279 0.193 0.157 0.120 0.084 0.059 0.048
IL 0.142 0.134 0.020 -0.226 0.127 0.053 0.006 0.072
0.239 0.170 0.118 0.180 0.076 0.054 0.038 0.048
MI 1.099 0.862 0.501 0.237 -0.135 -0.096 -0.096 -0.102
0.757 0.493 0.331 0.265 0.190 0.129 0.090 0.074
MN 1.069 -0.019 0.158 0.543 -0.400 -0.212 -0.093 -0.303
1.187 0.732 0.489 1.23 0.303 0.210 0.150 0.192
State-average 0.550 0.215 0.109 0.116 -0.053 -0.036 -0.065 -0.038
0.627 0.409 0.307 0.565 0.163 0.115 0.085 0.097
This table reports DiD estimates described in Eq. (3) as differences in hazard ratios. Standard errors are reported in parentheses. Stars denote p values for statistical tests of differences from zero: * indicates a value of 0.05; ** indicates a value of 0.01; *** indicates a value of 0.001. Numbers are subject to rounding error
14 We also conducted empirical tests of impacts excluding Florida and Minnesota. Results from these tests
did not change the core findings of this paper.
J Quant Criminol (2018) 34:741–773 761
123
Illustrations on the left show changes for drug offenders and those on the right show
changes for nondrug offenders.
Each graph contains two sets of data points (diamond plots and triangle plots) and linear
trend lines on either side of the discontinuity for visualization. Comparisons at the dis-
continuities (i.e., first differences s and q) are derived from shift in these trends at (x = 0). Measures of the impact (i.e., second differences Ds and Dq) are derived from differencing the changes between rows (the top row reports results for drug offenders subject to the bans
and the bottom row reports results for nondrug offenders).
Figure 1 shows some interesting patterns. For male drug offenders (top left), a casual
interpretation of this picture is that, relative to nondrug offenders (top right), the ban may
have caused a small (but perhaps significant) decrease in the rate of 3-year recidivism.
However, the picture also shows that a linear trend does not necessarily provide the best fit
for these data. Changes over the interval between (±) 18 months recidivism remain flat;
changes on the ends ([18 months and\-18 months) appear to drive the slope of the line. A quadratic estimation of the trend (on the left and right) provides a better visual
approximation of the data and a near equivalent statistical fit. 15
Under that specification,
the apparent impact of the ban (as a decrease in recidivism around the discontinuity) all but
disappears.
For women, rate of recidivism over this entire period is more variable and shows
arguably little to no change, especially for nondrug offenders. There do not seem to be any
discernable differences in patterns of change between drug and nondrug groups across pre-
and post-ban periods.
Similar graphs for individual states (depicting data summarized monthly rather than
weekly, shown in the ‘‘Appendix’’) also show consistent patterns of no effect either
obvious or systematic. Patterns of recidivism between pre and post periods appear to
Pooled Sample (Men) NondrugDrug
Pooled Sample (Women) NondrugDrug
0.14
0.16
0.18
0.2
0.22
0.24
0.26
-36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36
Months to Ban
Pr op
or ti
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
0.14
0.16
0.18
0.2
0.22
0.24
0.26
-36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36
Months to Ban
Pr op
or ti
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
0.1 0.12 0.14 0.16 0.18 0.2
0.22 0.24
-36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36
Months to Ban
Pr op
or ti
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
0.1 0.12 0.14 0.16 0.18 0.2
0.22 0.24
-36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36
Months to Ban
Pr op
or ti
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
Fig. 1 Illustrations of the proportion drug and nondrug offenders returning to prison within 3 years of release, based on prison admission date centered at Aug 22, 1996
15 The difference in the sum of the squared residuals between these competing trends is \0.0001.
762 J Quant Criminol (2018) 34:741–773
123
unfold similarly for drug and nondrug offenders and for men and women. In sum, it
appears that the introduction of the ban did not have a substantive impact on rates of
recidivism for drug offenders either absolutely, or relative to nondrug offenders.
Estimated Impact of the Initial Ban
Tables 5 and 6 summarize the main results of our estimations for women and men
respectively. Each table reports results from the full set of regressions for the pooled
sample including estimated coefficients for individual- and county-level control variables
as well as estimates of sd, snd and Ds described in Eqs. (1)–(3). For ease of interpretation, estimated coefficients have been converted to hazard ratios. Standard errors and statistical
significant (based on p-values) are also reported in these tables.
Overall these tables show that there is no strong evidence to support the hypothesis that
the restriction or denial of benefits for drug offenders, male or female, has led to material
impacts in the rate at which offending populations are returning to prison overall. Among
women drug offenders (in Table 5), the change in relative risk attributable to the ban is
between 0.01 and -0.04. For nondrug offenders estimates are similarly small, between
0.01 and -0.01. Both sets of estimates are robust to the use of both small and large samples
around the cutoff and arguably quite stable. Finally, point estimates of the DiD estimator
(the last row in each table) show that estimated differences in the ban’s impact across
groups are not statistically different from zero (between 0.02 and -0.03) for any of the four
samples tested.
Table 6 shows results for men. It shows that among male drug offenders, the estimated
change in relative risk after the ban is between 0.01 and -0.03. For nondrug offenders
estimates are between 0.00 and -0.02. As with women, DiD estimates are quite small
(between, 0.04 and -0.02) and no estimates are statistically different from zero.
Finally, given that states themselves are quite heterogeneous in terms of their policies
and practices governing correctional populations, we separately estimate and report
impacts for individual states. Table 7 summarizes the results of these estimations. Like
Tables 5 and 6, Table 7 reports the DiD estimates from each exercise and for multiple
samples. It does not report coefficients estimated from individual covariates. 16
Overall, Table 7 shows results that are consistent with the general findings from the
pooled sample. Where samples are small, estimates are highly variable and no consistent
findings emerge. Where samples are large, estimates are generally much closer to zero and
most states do not show statistically or substantively significant impacts on recidivism.
Some exceptions do exist, primarily in California where the largest sample shows a -0.054
decrease in the relative risk for male drug offenders as compared to nondrug offenders.
Additional Tests of the Impact
In addition to the main results above, we conducted additional tests to provide greater
context for the results. First, we explored possible associations between the time spent at
risk and the impact of restricting benefits. Specifically, we tested whether the ban’s impact
varies over time-at-risk by separately estimating the average impact of the ban over various
segments: (1) during the first 6 months following release, (2) between 6 and 18 months
following release, and (3) more than 18 months following release.
16 Results are available upon request.
J Quant Criminol (2018) 34:741–773 763
123
Given that the risk of returning to prison naturally diminishes over time (Langen and
Levin 2002; Durose et al. 2014), it may be that denying benefits has the greatest impact
early in the re-entry period. On the other hand, it may be that benefits impact an offender’s
ability to address more long-term challenges, especially if it takes time for offenders to
begin receiving benefits. If so, then denying benefits may imply consequences later in the
re-entry period. In either case, significant, heterogeneous impacts may exist even where the
average effect implied is not different from zero.
Table 8 reports DiD estimates of the ban’s impact over time-at-risk and across sampling
windows, using the pooled sample only. Overall this table suggests some provocative
patterns. For both men and women, point estimates of impacts on the relative risk for drug
offenders are negative in the first six months after release, though for women, these
estimates are not statistically different from zero. However, after 18 months following
release, these patterns reverse—point estimates for both men and women are most often
positive, suggesting recidivism worsens for drug offenders during this period. Again these
patterns are not statistically different from zero; however, they suggest a real possibility
that impacts are heterogeneous over time.
From a behavioral perspective, it may not be unreasonable to expect that denying SNAP
and TANF benefits has differential impacts in the short run vs. the long run. Consider the
following example. If the fear of losing social supports causes short-run behaviors (e.g.,
more aggressive job searching) among risky offenders to change, the near-term impact of
the ban may be beneficial (i.e., by reducing recidivism). At the same time, if the long-term
loss of support among less risky offenders creates ongoing hardship, then the net effect
over the long term may be detrimental (i.e., by increasing recidivism).
Results from this table do not validate such stories; however, they do provide an
impetus for further investigation. Given the inherent limitations in our ITT analysis, we
argue that the results from this table are best interpreted as an exploratory exercise and that
future investigation should consider the possibility, nature, and causes of heterogeneous
impacts of the ban’s application.
We performed a second exploratory test of impacts to examine whether there is any
evidence to suggest that our null finding (an ITT estimate) would be nonzero if it were
estimated as a TOT estimate. This test exploits county-level variation in SNAP partici-
pation (as measured in 1995) to compare impacts, but requires two strong (and untestable)
assumptions. The first assumption is that offenders coming from counties with higher rates
of SNAP participation are themselves more likely to be SNAP/TANF recipients. If
Table 8 Estimated impacts of the initial ban
Women Men
6-month 1-year 2-year 3-year 6-month 1-year 2-year 3-year
0–6 Months -0.046 0.010 -0.010 -0.103 -0.017 -0.076* -0.085*** -0.101***
0.135 0.093 0.067 0.056 0.046 0.032 0.023 0.019
6–18 Months -0.065 -0.030 -0.009 -0.031 0.075 0.020 -0.022 -0.008
0.124 0.087 0.061 0.050 0.042 0.029 0.021 0.017
18? Months 0.113 -0.024 0.038 0.027 0.042 0.040 0.029 0.037*
0.122 0.086 0.061 0.050 0.040 0.028 0.020 0.016
This table reports DiD estimates described in Eq. (3) as differences in hazard ratios. Standard errors are reported in parentheses. Stars denote p values for statistical tests of differences from zero: * indicates a value of 0.05; ** indicates a value of 0.01; *** indicates a value of 0.001. Numbers are subject to rounding error
764 J Quant Criminol (2018) 34:741–773
123
offenders coming from high-participation areas are more often themselves recipients of
SNAP and/or TANF, then ITT estimates in counties with higher participation come closer
to TOT estimates while ITT estimates in low-participation areas are more biased toward
zero, since these areas include a higher proportion of noneligible nonparticipants. We
looked to see if any such patterns exist.
This test requires information about each offender’s county of residence; however, the
NCRP does not currently report this information. Instead we relied on the reported county
of conviction (an available measure) as a proxy for residence. Thus our test requires a
second assumption—offenders are likely to be convicted in the counties in which they
reside. While there is no test for this in the NCRP data, there is a known body of literature
that supports the argument that offenders often commit crimes near the communities where
they live (e.g., Eck and Weisburd 2015; Cohen and Felson 1979; Brantingham and
Brantingham 1993, 1995).
Based on these conditions, we examined whether estimated impacts in high-SNAP
concentration counties are larger than in low-concentration counties. Specifically, esti-
mates from the pooled regression are grouped into deciles, so that the lowest decile (the
1st) represents the 10% of counties with the lowest proportion of SNAP households (\6% of households), and the highest decile (the 10th) represents the 10% of counties with the
highest proportion ([30% of households). Results are reported in Fig. 2. Figure 2 shows the estimated (DiD) impact of the drug felony ban, by SNAP household
concentration, for both men and women using the 3-year sample (results are not sensitive to
our sample selection). Overall this figure shows that among both men and women there are no
discernable patterns of differences in impacts across counties. In terms of magnitude, average
impacts among the bottom 20% of counties are\0.01 different from the top 20% of counties. Overall, the test is weak but suggests no aggregate impacts resulting from the ban.
The third test is a general sensitivity test of our results to alternative specifications that
model time trends as higher-order polynomials rather than simple linear trends. Specifi-
cally, we tested a quadratic and third-order specification of time trends in addition to the
linear arguments shown in earlier regression equations (i.e., three specifications). We did
this because more flexible time trends can provide better fits to the data, though some
-0.5
-0.4
-0.3
-0.2
-0.1
0
0.1
0.2
0.3
0.4
1st 2nd 3rd 4th 5th 6th 7th 8th 9th 10th 1st 2nd 3rd 4th 5th 6th 7th 8th 9th 10th
A ve
ra ge
(D iD
) E st
im at
es
Women Men
Fig. 2 Average (DiD) Ban impacts across counties in the pooled sample, by SNAP household concentration and sex
J Quant Criminol (2018) 34:741–773 765
123
literature also argues that higher-order approximations run a greater risk of introducing
bias (Gelman and Imbens 2014).
Overall we find that our main results are extremely robust to these alternative specifi-
cations. Of the 56 additional tests we conducted for men (across pooled and state samples),
1 test (2%) yielded significant DiD estimates at a p value\0.05. For women, 56 additional tests yielded 2 significant DiD estimates (4% of tests) at a p value\0.05. Given that with so many tests we would expect at least some findings by chance even where no true effects
exist, these results reinforce the main finding of no effect.
Finally we tested the sensitivity of our results to our use of the Cox model. While the Cox
model allows for flexible estimation of the hazard function, it requires a strong assumption
about the proportionality of hazards across measures. By contrast, a less flexible parametric
survival model does not impose proportionality. As such, we compared our results from the
Cox estimation to a similarly estimated set of parametric survival models that impose a
gamma distribution for the survival function. In cases where the model under a gamma
distribution could not be estimated, we substituted a Weibull distribution instead. Overall we
found that our conclusions are robust to the use of this alternative specification.
Discussion
For the last 20 years, most states have imposed some form of special restrictions on drug
felons seeking SNAP and TANF benefits. It seems now though that the social and political
tone of the public conversation is at a critical point. Nearly half a century of steady and
persistent prison population growth is forcing lawmakers to reconsider the merits of long-
standing policies, including the drug felony ban. And despite the political rhetoric, there
have been no confirmatory tests of whether and how manifestations of these laws have
resulted in tangible differences to prison systems. Without that evidence, it is impossible
for policymakers to understand the consequences of actions taken to expand or reduce
access to benefits for offenders.
This paper uses a rigorous quasi-experimental approach together with longitudinal
prison data and state data on ban adoptions to test competing theories. Results of this
analysis are conclusive: neither the denial nor the expansion of SNAP or TANF benefits to
drug offenders will adversely or positively impact the size of drug offender populations in
state prisons. These results appear to extend to both men and women and to all observed
variations of state policies.
The obvious question stemming from this analysis is: ‘‘Why don’t welfare laws seem to
matter in this context?’’ There are several potential answers. First, it may be that there are
too few offenders receiving benefits to substantively impact prisons and that low rates of
recipiency are masking true impacts at the individual level. Our ITT framework is infor-
mative, but it does not identify impacts for the subset of eligible offenders.
Second, it may be true that the benefits denied to drug offenders under these laws simply
are not significant enough to differentially impact recidivism in a meaningful way. Con-
sider, for example, that the disqualification of an individual from TANF does not disqualify
the entire household from benefits. In cases where a drug felon’s household continues to
receive benefits, the ban acts to reduce, but not eliminate, benefits. These partial household
benefits mitigate the denial of benefits to the individual. Similarly, the PRWORA does not
ban drug felons from receiving nonassistance benefits from TANF, including many benefits
that we might consider critical to successful re-entry, e.g., services such as counseling, job
766 J Quant Criminol (2018) 34:741–773
123
retention and employment-related services that do not provide basic income support. To
the extent that these services have an impact, the ban has less overall influence.
Another possibility is that true heterogeneous impacts among offender subgroups are
not observed when estimating the local average treatment effect. We partly explore this
possibility in the paper; however, other unexplored offender subgroups may provide
additional context. For example, it may be that the impact of the ban is heterogeneous with
respect to an offenders’ age, race or family size. A deeper examination of possible
heterogeneity may reveal new insights.
There are other limitations to our analysis which have implications for the impacts we
estimate, some of which might be addressed in the future with improvements to the data or
extensions of analyses. For example, identification of offenders in the data is not error-free
and has implications for analysis. First, although most offenders in prisons are felons,
NCRP data do not allow us to separate misdemeanants from felons and control for them in
analysis. To the extent that misdemeanants are part of the sample, impact estimates are
biased toward a null finding.
Second, our labeling of offenders as drug or nondrug offenders is not perfect. Since we
cannot observe every offender’s complete incarceration history in every state, we cannot
avoid misclassifying at least some drug offenders as nondrug offenders. Third, our iden-
tification of new crimes based on prison admission codes is imperfect. Discretion in the
judicial process and variable sentencing structures across states obscure the meaning of
these codes (Gaes et al. 2016). 17
Within the constraints of the NCRP, there may be no
solution to this problem; however, the integration of new information such as arrest records
may help resolve the issue. Similarly, discretion and uncertainty in the use and application
of charging offenses makes a more granular investigation of patterns in outcomes relatively
uninformative. Arrests records may provide illumination.
Finally, one area that future investigators should explore more closely is whether and how
ban modifications have impacted offender outcomes such as recidivism. The identification
strategy we present in this paper is not adequate for such an investigation. Credible estimates
require more first-hand knowledge (and data) about real-world implementation of modified
policies and practices. For example, it is important to know whether offenders released prior
to the ban’s modification retrospectively seek out benefits for which they have become
eligible. Do state agencies actively pursue such cases? How? Answers to such questions are
critical to proper sample selection. We leave this exercise to future research.
Overall, there is no doubt that this analysis answers important questions. Will ban
removal help to alleviate the problem of mass incarceration? The answer appears to be no.
Is there a behavioral basis for denying benefits to drug offenders while providing benefits
to nondrug offenders and violent offenders? The answer again appears to be no. However,
the answers to these questions also inspire other, yet unresolved questions. What should
states do next? Should ban removal be encouraged or discouraged? The answers to these
questions are subject to debate; however, that debate should be informed by future research
that more closely examines how individuals are directly impacted by the receipt of welfare.
Fortunately, BJS is at present undertaking an effort to expand the use of NCRP records by
merging them with other offender-level information including welfare use. Use of new data
from that effort will undoubtedly lead to novel insights along this line of inquiry.
17 This paper proposes one alternative construction for a ‘‘new crime’’ using a time-based rule that classifies
all prison admissions as new crimes when no release from prison has been observed within the prior year. We test the sensitivity of our results to this classification rule (as well as a 3-year variant of this rule) and find no discernable difference in our findings.
J Quant Criminol (2018) 34:741–773 767
123
Acknowledgements This work was supported by Grant Nos. 2010-BJ-CX-K067 and 2015-R2-CX-K135 awarded by the Bureau of Justice Statistics, Office of Justice Programs, US Department of Justice. For this work, Thomas Rich served as Project Director along with Principal Investigators William Rhodes and Gerry Gaes. Points of view in this document are those of the authors and do not represent the official position of the US Department of Justice. The authors are responsible for any errors in the paper.
Appendix
See Fig. 3.
CALIFORNIA Pooled Sample (Men)
Drug Nondrug
Pooled Sample (Women) Drug Nondrug
0.1
0.15
0.2
0.25
0.3
0.35
-36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36
Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
0.1
0.15
0.2
0.25
0.3
0.35
-36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36
Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
0.1
0.15
0.2
0.25
0.3
0.35
-36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36 Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
0.1
0.15
0.2
0.25
0.3
0.35
-36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36
Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
FLORIDA Pooled Sample (Men) Drug Nondrug
Pooled Sample (Women) Drug Nondrug
0
0.05
0.1
0.15
0.2
0.25
-40 -20 0 20 40 Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
0
0.05
0.1
0.15
0.2
0.25
-40 -20 0 20 40 Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
0
0.05
0.1
0.15
0.2
0.25
-40 -20 0 20 40 Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
0
0.05
0.1
0.15
0.2
0.25
-40 -20 0 20 40 Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
Fig. 3 State-by-state illustrations of the proportion drug and nondrug offenders returning to prison within 3 years of release, based on prison admission date centered at Aug 22, 1996
768 J Quant Criminol (2018) 34:741–773
123
GEORGIA Pooled Sample (Men) Drug Nondrug
Pooled Sample (Women) Drug Nondrug
0
0.05
0.1
0.15
0.2
0.25
-40 -20 0 20 40 Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
0
0.05
0.1
0.15
0.2
0.25
-40 -20 0 20 40 Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
0
0.05
0.1
0.15
0.2
0.25
-40 -20 0 20 40 Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
0
0.05
0.1
0.15
0.2
0.25
-40 -20 0 20 40 Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
ILLINOIS Pooled Sample (Men)
Drug Nondrug
Pooled Sample (Women) Drug Nondrug
0
0.05
0.1
0.15
0.2
0.25
-36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36 Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
0
0.05
0.1
0.15
0.2
0.25
-36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36 Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
0
0.05
0.1
0.15
0.2
0.25
-36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36 Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
0
0.05
0.1
0.15
0.2
0.25
-36 -30 -24 -18 -12 -6 0 6 12 18 24 30 36 Months to Ban
Pr op
or �
on
Re tu
rn in
g w
it hi
n 3
Ye ar
s
Fig. 3 continued
J Quant Criminol (2018) 34:741–773 769
123
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Reproduced with permission of copyright owner. Further reproduction prohibited without permission.
- A Quasi-Experimental Evaluation of the Impact of Public Assistance on Prisoner Recidivism
- Abstract
- Introduction
- Objective
- Methods
- Results
- Conclusion
- Introduction
- Background
- Offender Re-Entry, Economic Challenges and Use of Welfare
- SNAP, TANF and Recidivism: The Potential Impact of Denying Benefits
- Using the Ban as a Natural Experiment for Denying Benefits
- State Implementation of the Drug Felony Ban
- Data
- Method
- Results
- Graphical Analyses
- Estimated Impact of the Initial Ban
- Additional Tests of the Impact
- Discussion
- Acknowledgements
- Appendix
- References
