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

Based on the experimental or quasi-experimental study you researched  for the library search assigned in your studies for this unit, address  the following:

• Determine whether the study is experimental or quasi-experimental; describe how you know.
• Describe the variables, both independent and dependent, used in the research.
• Describe the treatment conditions of the experimental group. If  the study is quasi-experimental, describe the different groups or  conditions that were compared.
• Describe the specific type of research design that was used, and  discuss why it is considered experimental or quasi-experimental.
• Evaluate the scientific merit of the selected design. How might  you have designed this study differently? Evaluate how well the  experimental approach and design helped the researcher answer the  research questions.
• List the persistent link for the article. Use the Persistent  Links and DOIs library guide, linked in the Resources, to learn how to  locate this information in the library databases.
• Cite all sources in APA style and provide an APA-formatted reference list at the end of your post.

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 jeremy_luallen@abtassoc.com

Jared Edgerton Jared_edgerton@abtassoc.com

Deirdre Rabideau Deirdre_rabideau@abtassoc.com

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

123

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 of the ban entirely; today that number has grown to14.6 Twenty-six states havemodified the

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. Thoughwe 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, andMinnesota.8 Given

that our interest is in analyzing the impact of the banwhen itwas 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

123

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

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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.

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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

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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 ðBanÞþqdðMÞþpXdijþlCdj 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 þlCndj 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

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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

chargedwithmultiple offenseswithvaryingdegreesof seriousness; (2)NCRPdataonly records

the top three,most serious offenses; (3)NCRPdata do not denotewhich 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.

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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.

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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