Damon M. Petrich, Travis C. Pratt, Cheryl Lero Jonson,
and Francis T. Cullen

Custodial Sanctions
and Reoffending:
A Meta-Analytic Review

ABSTRACT

Beginning in the 1970s, the United States began an experiment in mass imprisonment. Supporters argued that harsh punishments such as imprisonment reduce crime by deterring inmates from reoffending. Skeptics argued that imprisonment may have a criminogenic effect. The skeptics were right. Previous
narrative reviews and meta-analyses concluded that the overall effect of imprisonment is null. Based on a much larger meta-analysis of 116 studies, the current
analysis shows that custodial sanctions have no effect on reoffending or slightly
increase it when compared with the effects of noncustodial sanctions such as
probation. This finding is robust regardless of variations in methodological rigor,
types of sanctions examined, and sociodemographic characteristics of samples.
All sophisticated assessments of the research have independently reached the
same conclusion. The null effect of custodial compared with noncustodial sanctions
is considered a “criminological fact.” Incarceration cannot be justified on the
grounds it affords public safety by decreasing recidivism. Prisons are unlikely to

Damon M. Petrich is a criminal justice PhD candidate at the University of Cincinnati;
Travis C. Pratt is research director for the Harris County Community Supervision and
Corrections Department and a research fellow at the University of Cincinnati Corrections
Institute; Cheryl Lero Jonson is associate professor of criminal justice at Xavier University;
Francis T. Cullen is Distinguished Research Professor Emeritus of Criminal Justice and
senior research associate at the University of Cincinnati.
Electronically published September 22, 2021
Crime and Justice, volume 50, 2021.
q 2021 The University of Chicago. All rights reserved. Published by The University of Chicago Press.
https://doi.org/10.1086/715100

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reduce reoffending unless they can be transformed into people-changing institutions on the basis of available evidence on what works organizationally to reform offenders.

After a nearly 600 percent increase in the rate of imprisonment in the
United States between 1972 and 2007 (Pager 2007; Nellis and King 2009),
this trend is slowly beginning to reverse, with rates declining by an average
of 1.2 percent per year between 2008 and 2018 (Maruschak and Minton
2020). Still, the latest nationwide data compiled by the Bureau of Justice
Statistics (Maruschak and Minton 2020) show that 2,123,100 Americans
were held in federal or state prisons and local jails as of December 2018.
Even with declines over the past decade, the United States maintains its
dubious title as the world leader in imprisonment with approximately
655 prisoners per 100,000 citizens, followed by El Salvador (604) and Turkmenistan (526). The imprisonment rates of other culturally comparable
countries, such as Canada (114), the United Kingdom (140), and Australia (172), are but a fraction of America’s (World Prison Brief 2018).
Taken together, government agencies in the United States spend approximately $80 billion per year on corrections (National Academy of Sciences
2014), with average incarceration costs of around $30,000 per inmate per
year (PEW Center on the States 2009; Vera Institute 2017).
Scholars have produced myriad works over the past three decades that
attempt to account for the meteoric growth of incarceration in the United
States (see, e.g., Garland 2001; Zimring 2001; Tonry 2004, 2007, 2009;
Gottschalk 2006; Clear and Frost 2014; Enns 2016; Pfaff 2017, 2020;
Muhammad 2019). Within these works, a diverse range of factors have
been proposed as holding explanatory value: increased rates of crime beginning in the 1960s; beliefs that rehabilitation programs for offenders
do not work; the resurgence of conservative ideals such as individual responsibility, commonsense law and order, and absolutist conceptions of right and
wrong; racial resentment and the use of crime policy to protect against minority encroachment on White social and economic advantage; mass media
sensationalism of rare yet high-profile correctional system failures; increases
in fear of crime and expansions of victims’ advocacy groups; the existence of
conflictual, two-party political systems; and democratic rather than meritocratic selection of prosecutors and judges. Any one of these factors is unlikely
to be a sufficient explanation, some factors hold more merit than others, and
many factors may have interacted to nourish the nation’s protracted experiment in mass incarceration (Tonry 2004; Pfaff 2020).

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Regardless of the motivating rationales and causes, a host of legal and
policy changes between the mid-1970s and 1990s made sentences to imprisonment much more likely and longer. From the mid-1970s onward, states
such as California, Illinois, Indiana, and Maine introduced determinate sentencing reforms that severely limited or completely abolished the use of parole. Laws focused on creating mandatory minimum sentences also proliferated the country between the 1970s and 1990s. For example, Michigan
enacted the “650 Lifer Law” in 1978, which originally mandated life without parole if convicted of trafficking more than 650 grams of cocaine or heroin. Likewise, the 1984 federal Comprehensive Crime Control Act required
a five-year sentence enhancement for carrying a firearm during the commission of another drug or violent offense. In the 1990s, more than half of the
states passed some form of a three strikes or habitual offender law in attempts to target repeat offenders. In California, for instance, these laws required a life sentence for individuals convicted of a felony who had been
convicted of two or more felonies in the past. At the federal level, too, legislation such as the 1994 Violent Crime Control and Law Enforcement Act
provided states with additional funding for the construction of prisons, conditional on evidence that the state was sentencing more violent offenders to
prison and for longer (Zimring, Hawkins, and Kamin 2001; Spohn 2008;
Tonry 1996, 2009; National Academy of Sciences 2014; Pfaff 2017).
It is often overlooked that the escalation of punitive policies was detached from any empirical base of knowledge regarding the effects of imprisonment on crime. Rather, these measures were largely based on “blind
faith that a silver-bullet solution [could] magically solve the [crime] problem” (Mears and Cochran 2015, p. 58). Some theoretical discussion and research attempted to assess the notion that crime could be reduced by incapacitating active offenders via imprisonment (Shinnar and Shinnar 1975;
Blumstein, Cohen, and Nagin 1978; Spelman 1994, 2000). However, little
empirical work was done to assess the effects of custodial sanctions on postrelease reoffending (Mears and Cochran 2015). Based on our survey of this
literature, only 13 studies comparing the outcomes of those sentenced to
custodial and noncustodial sanctions were conducted prior to 1990, another
23 in the subsequent decade, and another 25 through to 2008. Many of these
early studies were of conspicuously poor methodological quality, often relying on bivariate assessments or on regression and exact matching models that
adjusted for only a handful of relevant confounders (Nagin, Cullen, and
Jonson 2009; Villettaz, Gillieron, and Killias 2015). In short, during the
times when the mass incarceration movement began and grew most rapidly,

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relatively little was known about the effect being imprisoned had on
reoffending.
Lacking an empirical foundation for their experiment with large-scale
imprisonment, politicians justified their efforts with the “common sense”
notion that people are rational actors and could therefore be deterred from
crime if punishments were severe enough (Garland 2001; Clear and Frost
2014). As imprisonment is commonly viewed as the ultimate loss of freedoms, social connection, and the like, increasing the likelihood of being
sent to prison and the length of prison terms was viewed as a uniquely effective way to deter offending. This view had some support among economists, political scientists, and other scholars (Becker 1968; Wilson 1975;
van den Haag 1977), though their support was generally based on theory
rather than empirical evidence. An alternative perspective, advanced by the
majority of sociologists and criminologists, was that imprisonment is more
likely to have criminogenic effects than to serve as an effective deterrent to
prisoners (e.g., Shaw 1930; Sutherland 1939; Sykes 1958; de Tocqueville
[1844] 1968; Braithwaite 1989). These scholars suggested that a variety
of factors associated with a custodial sentence increase reoffending, including close-quarters cohabitation with and learning from other inmates, the
strains of exposure to violence and loss of personal freedoms, the fraying of
ties to support networks, and the collateral consequences attached to a criminal
conviction such as barriers to employment and housing. Until fairly recently,
however, direct evidence showing the criminogenic effect of these conditions
has remained limited (see, e.g., Sampson and Laub 1993; Bayer, Hjalmarsson, and Pozen 2009; Listwan et al. 2013).
To have embarked on a decades-long experiment in mass incarceration
with scant empirical knowledge of the effect of prison on postrelease offending seems inexplicable in retrospect. On any given day, more than
two million people are held in correctional institutions in the United States
(Maruschak and Minton 2020). Ninety-five percent of inmates are eventually released, which means that approximately 600,000 individuals leave
prisons each year and another 10.7 million cycle through local jails (Carson
2020; Zeng 2020). With so many lives at stake—including both prisoners
and potential victims—correctional policy should be informed by research.
That is why a comprehensive review of the research on custodial sanctions
and reoffending is necessary. We provide that review. Prior narrative and
meta-analytic reviews have indicated that, compared with noncustodial
sanctions such as probation, sentencing individuals to terms of imprisonment generally has a null or criminogenic effect on reoffending (Nagin,

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Cullen, and Jonson 2009; Jonson 2010; Villettaz, Gillieron, and Killias
2015). However, these reviews are limited by factors such as small numbers
of primary studies to draw from, few studies of strong methodological rigor,
modeling strategies that could not account for multiple effect sizes nested
within individual studies, and limited or nonexistent analyses of factors that
might moderate the effects of custodial sanctions on reoffending.
The meta-analytic review presented in this essay overcomes these problems and builds on earlier work in four important ways. First, it includes
55 additional studies produced since the last comprehensive reviews were
made by Nagin, Cullen, and Jonson (2009) and Jonson (2010). Taken together, these more recent studies include 691 effect size estimates, many
from models that capitalize on natural experiments or use propensity score
methods. Second, we expanded our inclusion criteria beyond those of Villettaz, Gillieron, and Killias (2015) to include all studies comparing custodial and noncustodial sanctions, including those using bivariate and multivariate regression analyses. Third, we capitalize on advances in meta-analytic
techniques to use a multilevel modeling approach (Hox, Moerbeek, and
van der Schoot 2018). These methods allow individual effect sizes to be
weighted by their precision rather than sample size and allow for the inclusion of multiple effect sizes from within individual studies while accounting
for their statistical dependence. Fourth, given the large number of available
effect size estimates (N p 981) and a detailed coding scheme, we were able
to assess the influence of a broad range of potential moderators, including
the overall research design, covariates accounted for in statistical models,
types and lengths of sanctions examined, and sociodemographic characteristics of samples such as the age and gender distributions. Following
Nagin, Cullen, and Jonson (2009, p. 120), we “use the concept of reoffending
to refer to all criminal acts committed by a person following a legal sanction”—in this case, a custodial or noncustodial placement. As Section IV
shows, custodial sanctions have a null or criminogenic effect on reoffending
when compared with noncustodial sanctions such as probation. Although a
small number of factors moderate effect size estimates (e.g., research design,
type of reoffending measure), we find no conditions under which custody
reduces reoffending.
This subject is particularly timely given there are signs that America’s fixation on imprisonment is beginning to wane (Petersilia and Cullen 2015;
Tonry 2019; Butler et al. 2020). Data from the Bureau of Justice Statistics
show that prison and jail incarceration rates have declined by 15 percent
and 11 percent, respectively, since 2008 (Carson 2020; Zeng 2020). There

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is also now bipartisan support for efforts to reform the criminal justice system. At the federal level, for example, the Second Chance Act and the First
Step Act were collaborative efforts by Democrats and Republicans and
signed into law by Presidents George W. Bush and Donald J. Trump
(Lattimore and Visher 2009; Cohen 2019). These acts have provided
funding to create and evaluate programs aimed to facilitate offenders’ reentry into their communities (e.g., education and employment assistance,
cognitive-behavioral treatment), develop risk assessment tools, investigate
sentencing reforms, and develop partnerships with community organizations (for a review of the effectiveness of these efforts, see Petrich et al.
2021). Efforts to reduce prison populations are also occurring at the state
level, with previously high-incarceration states such as Louisiana and
Mississippi exploring justice reinvestment policies and changes to sentencing guidelines (Gray 2011; Cohen 2017; PEW Charitable Trusts 2018).
Finally, there is an increasing amount of public support for and political
and media discourse about issues such as ban-the-box, problem-solving
courts, felon disenfranchisement, criminal record expungement, and rehabilitation ceremonies (e.g., Love and Schlussel 2019; Thielo et al. 2019;
Butler et al. 2020).
Two other considerations are germane. First, more attention is being
paid to the racial disparities that pervade the American criminal justice system, owing in large part to public outrage over recent tragic events such as
the killings of Eric Garner, George Floyd, and Breonna Taylor. Because of
the role of law enforcement in these high-profile killings, much ensuing
policy discussion has centered around proposals to defund the police in
one way or another, whether through complete abolishment or redirecting
funds toward social work, mental health, and substance abuse treatment
(Lowrey 2020; North 2020; Searcey 2020). But it is important also to consider that disparities exist beyond police-citizen interaction (Ba et al. 2021).
Influential books such as Michelle Alexander’s The New Jim Crow, documentary films such as 13th (DuVernay 2016), and myriad empirical analyses show that disparities in the correctional system are often large and have
long-term negative consequences for Black communities (Clear 2007; Kirk
2016). Studies have consistently shown that Black citizens, particularly
young males, are more likely than Whites to be placed in pretrial detention,
receive sentences of incarceration, and receive longer sentences (e.g., Bales
and Piquero 2012b; Wooldredge et al. 2015; Holmes, Feldmeyer, and
Kulig 2020; see also King and Light 2019). In light of these disparities, it
is important to think about how the mass application of a sanction that does

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little to reduce reoffending will negatively affect citizens and their communities. Outcomes commonly cited in the literature include the dissolution
of families, depression of local economies, and greater cynicism toward
the criminal justice system (Clear 2007; Western and Wildeman 2009; Kirk
2016). If sentences such as probation produce reoffending outcomes comparable to those of imprisonment and simultaneously alleviate collateral
consequences, the current public policy debates about criminal justice reform should take this into account.
Also germane are the effects of the coronavirus pandemic on prisoners,
their release, and crime; 37.7 million people in the United States had contracted COVID-19 as of August 23, 2021, of whom 628,285 died (“Coronavirus
in the U.S.” 2021). Given the close-quarters nature of the prison environment, it is not surprising—though disturbing—that 661,000 inmates and
employees in America’s jails and prisons have been infected and another
2,990 have died (“Coronavirus in the U.S.” 2021). These are much greater
rates of infection than in the population-at-large. For example, a report by
Schwartzapfel, Park, and Demillo in December 2020 showed that the rate of
infection among US prisoners was four times greater than among the general population. In some states, for example Kansas, infection rates among
prisoners were as much as eight times larger. In response to these troubling
numbers, many state and local legislators have taken actions that led to the
release of small numbers of inmates who were close to their scheduled discharge dates (Porter 2021; Prison Policy Initiative 2021). However, although
prison and jail populations dropped by 9 percent and 24 percent, respectively, between 2019 and 2020 (Kang-Brown, Montagnet, and Heiss 2021),
most of these changes appear to be the result of reduced admissions rather
than increased releases (Widra and Wagner 2020). The reoffending outcomes of those released from incarceration remain to be seen. Our own review of the literature on custodial sanctions shows that those sentenced to
custody are equally as likely to reoffend as those who remain on community
supervision. This raises concerns about the small number of releases in the
midst of battling a virus that spreads rapidly in confined, close-quarters
spaces (Vose, Cullen, and Lee 2020).
Against the backdrop of declines in prison populations over the past decade, growing support for exploring alternatives to incarceration, concerns
over racial disparities, and the close-quarters confinement of large numbers
of inmates during a pandemic, there is need for a comprehensive empirical
understanding of the role of incarceration in reducing reoffending and promoting public safety. Here is how this essay, which addresses that need, is

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organized. Section I examines two competing perspectives on the effects of
incarceration. The deterrence perspective holds that punishment via imprisonment changes the decision-making processes of offenders and diminishes their desire to reoffend. The criminogenic perspective holds that
offenders are exposed to a range of experiences during and after imprisonment that make reoffending more likely. Section II discusses the current
state of research examining these perspectives, including reasons for heterogeneity in findings and the shortcomings of prior literature reviews.
Section III describes the methods used to conduct our review, including
strategies to cull the literature for studies comparing the effects of custodial
and noncustodial sanctions, how effect sizes and methodological variations
were coded, and statistical methods used to analyze the data. Section IV
reports the results of the meta-analytic review. Compared with noncustodial sanctions, custodial sanctions have a null to slightly criminogenic effect
on reoffending. The robustness of this overall effect is shown through
moderator analyses that assess whether effect sizes vary by methodological,
sanction-related, and other characteristics of the studies examined. Based
on our findings and prior reviews, Section V concludes that the null effects
of custodial sanction on reoffending should be considered a “criminological fact.” We conclude by exploring the implications of this finding for correctional policy in the United States.

I. Competing Perspectives on Imprisonment
In this section we examine the competing individual deterrence and criminalization perspectives on the effects of imprisonment on inmates’ subsequent criminality. Theoretical and “common sense” arguments that the experience of imprisonment should reduce prisoners’ subsequent offending
have never been strongly supported by the specialist literatures.
A. Incarceration as a Specific Deterrent
The notion that offenders are rational, calculating individuals who can
be deterred from future offending by increasing the severity of punishments gained widespread support among politicians and citizens between
the 1970s and 1990s, particularly in the United States (Garland 2001; Clear
and Frost 2014; Pratt 2019). The theoretical logic is that individuals engage
in crime because it furthers their self-interest (Clarke and Cornish 2001;
Chalfin and McCrary 2017). Faced with an opportunity to engage in criminal

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activity, the offender can choose either to commit the crime and receive its
benefits or not commit the crime and receive no benefit. Passing up the
chance to commit a crime is both risk- and reward-free, while seizing the
criminal opportunity carries both a reward and a risk of potential apprehension. Thus, the choice comes down to a cost-benefit analysis of the magnitude of the potential benefits of the act weighed against a combined function
of the certainty of apprehension and the severity of the expected punishment
(Becker 1968). Following this logic, the threat of incarceration provides
some level of deterrence to the population at large (i.e., general deterrence),
and the experience of incarceration for individual offenders is sufficiently
aversive that the expected utility of future criminal involvement is overshadowed by its costs (i.e., specific deterrence). Furthermore, to the extent
that deprivations imbued by incarceration are perceived as more severe
than those of a noncustodial sanction, incarceration should exert a greater
specific deterrent effect than sanctions such as probation (Nagin, Cullen,
and Jonson 2009).
Despite the intuitive appeal of the notion that harsher punishments will
deter criminal behavior, there are several logical and empirical reasons to
be skeptical. Three are most salient. First, rates of reoffending for those
sentenced to incarceration are high (Beck and Shipley 1989; Langan and
Levin 2002; Alper, Durose, and Markman 2018). In an important analysis,
Langan and Levin (2002) showed that 67.5 percent of prisoners are rearrested within three years of release. More recent data report a similar
68.5 percent rearrest rate of prisoners after three years and an 83 percent
rate within nine years (Alper, Durose, and Markman 2018). Advocates of
deterrence rarely discuss the failure rate of imprisonment in discouraging
reoffending among released prisoners.
Second, Becker’s (1968) influential model of deterrence posits that
both certainty and severity of punishment are required for any particular
sanction to deter behavior.1 According to this model, the probable deterrent effect of a sanction that is severe yet highly unlikely to occur is limited
(Nagin 2013; Chalfin and McCrary 2017). This is precisely the situation for

1
Early writings by Beccaria and Bentham also stressed the importance of the celerity (i.e.,
swiftness) of the sanction. This is often overlooked. Beccaria ([1764] 1986, p. 36) noted, for
example, that “the more promptly and the more closely punishment follows upon the commission of a crime, the more just and useful it will be.” Available evidence on sanction celerity is
not abundant and results are mixed, but it suggests that delaying punishment—even by just a
little—erodes its potential deterrent effect regardless of how certain or severe it may be (for a
review, see Pratt and Turanovic 2018).

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incarceration as a source of deterrence: before an individual is sentenced to
prison, the crime must be reported, the incident investigated, the correct
offender apprehended, charges filed, the prosecution’s arguments accepted
by the judge or jury, and the sentence chosen must be a period of incarceration. As Durlauf and Nagin (2011) point out, “none of these successive
stages in processing through the criminal justice system is certain” (p. 16).
Stated another way, because the vast majority of criminal events do not result
in imprisonment (Sellin 1931; Coleman and Moynihan 1996; Mosher,
Miethe, and Phillips 2002), the deterrent effect of possible time behind bars
relies primarily upon severity. This reliance on the threat of a severe yet unlikely term of imprisonment is problematic; existing reviews of the literature suggest preventive strategies focused on increasing the certainty of
punishment are much more effective (e.g., problem-oriented policing such
as Operation Ceasefire; see Durlauf and Nagin 2011; Chalfin and McCrary
2017; Braga, Weisburd, and Turchan 2018).
Although similar arguments about the uncertainty of noncustodial alternatives such as probation or community-based treatment could be made,
the data are clear that probation is a far more likely outcome of a conviction
than incarceration (National Academy of Sciences 2014). To be sure, rates
of reoffending for offenders sentenced to probation are also high, with between 30 and 40 percent rearrested within three years (Petersilia 2002;
Texas Legislative Board 2019). However, the groups of offenders sentenced to prison versus probation are likely to be quite different in terms
of criminal history, offense seriousness, and other characteristics. Adequate
tests of the efficacy of custodial sanctions in reducing reoffending need to
take account of factors that influence selection into the “treatment” of receiving a custodial sentence.
Third, the deterrent value of custodial sanctions assumes that offenders
perceive such sanctions as being more severe than noncustodial sanctions;
however, existing research suggests this is not always the case. Many offenders would rather serve shorter prison terms (e.g., 1 year) than lengthier
community-based punishments with intensive conditions (Petersilia 1990;
Crouch 1993; Moore, May, and Wood 2008). Furthermore, individual differences among offenders and specific aspects of sentences appear to influence the perceived severity of incarceration. Work by Raaijmakers et al.
(2017) and Crank and Brezina (2013) indicates that inmates with a greater
level of commitment to a criminal lifestyle (e.g., “Committing crime is
pretty much a permanent way of life”) perceive prison time as being less
difficult than those with low levels of commitment. Raaijmakers et al. (2017)

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also find that the subjectively experienced severity of incarceration decreases
over the course of incarceration. The impact of custody might lose its sting
for inmates strongly committed to criminality or who simply grow accustomed over time to spending time inside prison walls.

B. Incarceration as a Criminogenic Experience
Whereas deterrence theorists reduce incarceration to a price tag that
affects calculations about crime’s costs and benefits, other scholars—especially sociologists—see time in prison as a lengthy social experience that can
have criminogenic effects. Cullen, Jonson, and Nagin (2011, p. 535) observe, for example, that inmates regularly “associate with other offenders,
endure the pains of imprisonment, risk physical victimization, are cut off
from family and prosocial contacts on the outside, and face stigmatization.”
Thus, although prisons are intended to deter future offending, this perspective holds that incarceration exposes individuals to criminogenic risk factors
and distances them from protective factors, thus increasing the prospect of
reoffending upon release.
First, as places where offenders live together in a “society of captives”
(Sykes 1958), the prison has long been referred to as a “school of crime”
(Bentham [1789] 1970) or “house of corruption” (Shaw 1930) because of
the likelihood that techniques of and motivations for crime are transmitted
between inmates. The principles of social learning theory, when applied to
the prison context (Sutherland 1939; Akers 2009), suggest that as inmates
are exposed to a large group of antisocial peers and cut off from any prosocial
peers on the outside, they increasingly come into contact with pro-criminal
attitudes (e.g., the “convict code”; see Irwin and Cressey 1962; Mears et al.
2013); learn from and imitate others’ behavior in order to adjust to prison life
and offending in general; and receive social and tangible reinforcements for
adhering to prison culture. Several studies indicate an important role for peer
effects in prisoners’ postrelease offending (e.g., Bayer, Hjalmarsson, and
Pozen 2009; Ouss 2011; Damm and Gorinas 2016). In their examination
of peer effects among juvenile offenders, Bayer and colleagues (2009) find
that an inmate’s exposure to a greater proportion of inmates with the same
conviction offense increases reoffending within that particular crime category. To illustrate, for an individual committed for aggravated assault, increases in the proportion of fellow inmates convicted of aggravated assault
were associated with higher odds of the focal inmate committing another
assault upon release. Subsequent work examining cell-level interactions

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offers similar conclusions, and additionally shows that peer effects are more
evident for skill-intensive offenses (e.g., theft, drug-dealing) than for violent
crimes (Ouss 2011; Damm and Gorinas 2016; cf. Harris, Nakamura, and
Bucklen 2018).
Second, inmates are often exposed to the types of adverse events hypothesized to increase psychological strain and criminal coping. Agnew’s
(1992) general strain theory (GST) posits that failure to achieve positively
valued goals, removal of positive stimuli, and introduction of negative stimuli often lead to criminal behavior because they cause negative emotional
states (e.g., anger, depression) and pressure to cope with those states. The personal and social resources of the individual, such as self-efficacy, self-control,
socioeconomic status, and social control, moderate the association between
the negative emotions experienced and the coping strategy chosen—
whether prosocial or antisocial (Agnew 2001, 2013; Thaxton and Agnew
2018; Hoffman 2019). Blevins and colleagues (2010) argue that these propositions are highly relevant to common experiences within prison walls. For
example, positively valued goals that may be blocked during incarceration
include failure to obtain work assignments or having visitation privileges revoked; positive stimuli that are removed include a sense of autonomy, personal identity, heterosexual relationships, and privacy, among others (Sykes
1958; Toch 1977; Crewe 2011); and prison crowding, increased victimization, exposure to violence, and the requirements of psychological assessments and rehabilitation programs represent the introduction of negative
stimuli (Wolff et al. 2007; Crewe 2011; Zweig et al. 2015). Furthermore, it
is well established that many inmates possess pre-prison or confinementinduced characteristics that potentially reduce the likelihood of prosocial
coping, including low self-control (Hochstetler and DeLisi 2005), a commitment to the “code of the streets” (Mears et al. 2013), and infrequent contact
with the outside world (Cochran et al. 2015).
To date, only a handful of studies have directly tested the applicability of
GST in predicting the antisocial outcomes of inmates (Morris et al. 2012;
Listwan et al. 2013; Zweig et al. 2015). Listwan et al. (2013) collected data
on prisoners recently released from incarceration to test how in-prison experiences related to rearrest and recommittal over a 2.5-year follow-up period. Their analyses indicated that negative prison environments (e.g., inmates were more afraid of being assaulted, threatened) were associated with
increased odds of both rearrest and recommittal, and direct victimization
by other inmates was associated with higher odds of recommittal. Zweig
et al. (2015) similarly examined the effects of in-prison victimization on

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self-reported offending over a 15-month follow-up using data from the Serious and Violent Offender Reentry Initiative. In accordance with GST,
they showed that victimization while incarcerated had both direct and indirect (through hostility) effects on measures of any crime and violent
crime after release, and both direct and indirect (through depressive symptoms) effects on drug use.
Third, incarceration has been hypothesized to increase reoffending
through the labeling effect of a criminal record and associated collateral
consequences. The classic labeling theory argument is that stigmatizing
societal reactions are internalized and that this deviant identity ensnares individuals in a criminal trajectory (Lemert 1951; Chambliss 1973). A related
hypothesis is that having a conviction or imprisonment record stabilizes
offending by weakening social bonds with family and limiting opportunities for employment, education, and housing (Uggen and Stewart 2015;
Kirk and Wakefield 2018).
The strongest evidence for labeling theory is found in studies that prospectively compare the reoffending outcomes of individuals who have had
contact with the criminal justice system against the outcomes of those who
avoid system contact. These studies tend to find that arrests, court appearances, convictions, and other forms of system contact are associated with an
increased risk of subsequent involvement in criminal behavior (e.g., Bernburg, Krohn, and Rivera 2006; Chiricos et al. 2007; Lopes et al. 2012; Petitclerc et al. 2013; Petrosino, Turpin-Petrosino, and Guckeberg 2013; Liberman, Kirk, and Kim 2014; Wiley and Esbensen 2016; Motz et al. 2020). For
example, Wiley and Esbensen (2016; see also Wiley, Slocum, and Esbensen 2013) used propensity score techniques to examine the effects of police
contact among participants in the Gang Resistance Education and Training
program. Matching on a range of relevant confounders (e.g., demographics,
risk-seeking, prior delinquency, peer delinquency), Wiley and Esbensen
showed that individuals who were stopped by police or arrested subsequently
engaged in more frequent delinquency than those who had no police contact.
Participants who were arrested also engaged in more subsequent delinquent
behavior than those who were only stopped and questioned. Liberman, Kirk,
and Kim (2014) also used propensity score matching (PSM) to investigate
the influence of arrests during adolescence on subsequent delinquency for
participants surveyed in the Project on Human Development in Chicago
Neighborhoods. With propensity scores based on a robust set of 79 covariates, Liberman and colleagues found that being arrested was associated with
increases in the subsequent variety of offending and higher odds of rearrest.

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Another recent study conducted by Motz et al. (2020) capitalized on data
from both fraternal and identical twins collected during the Environmental
Risk Longitudinal Twin Study. After adjusting for a range of relevant covariates and genetic confounding, Motz et al. found that being arrested, having an antisocial behavior order issued by the court, and receiving an official
criminal record each increased the likelihood of subsequent involvement in
delinquency.
Prior research thus confirms labeling theory’s hypothesis that criminal
justice system contact increases criminal behavior. Evidence for the intervening mechanisms set forth by the theory is less clear. To date, there
have been few empirical assessments of whether arrest, conviction, or imprisonment actually cause the changes in offenders’ identities that are the
focal point of labeling theory. The handful of studies have produced mixed
findings on whether formal intervention leads to the adoption of a criminal
identity ( Jensen 1972; Ageton and Elliott 1974; Hepburn 1977; Brownfield and Thompson 2008; Wiley, Slocum, and Esbensen 2013). These
studies are also limited by the use of cross-sectional data that cannot account for temporal ordering and/or inadequate measurement of identity.
For example, Hepburn (1977) analyzed cross-sectional data from police
records and surveys with a sample of 145 adolescent males to determine
the effect of formal labeling on identity. Delinquent identity was captured
by a single survey item asking participants how often they thought of
themselves as delinquent. Hepburn (1977) found no significant association
between contact with the police and delinquent identification after accounting for socioeconomic status and self-reported delinquency. More
recently, Wiley, Slocum, and Esbensen (2013) used longitudinal data from
middle-schoolers involved in the Gang Resistance Education and Training
study to evaluate the labeling effects of police contact. Deviant identity was
not directly measured. Rather, the authors used items tapping attitudes (e.g.,
degree of guilt about attacking something with a weapon) and beliefs (e.g.,
“It’s okay to steal something if that’s the only way you could ever get it”)
about delinquency, which they argue precede the adoption of a deviant identity. After matching participants using propensity score techniques, Wiley
and colleagues found that individuals who were arrested subsequently had
more crime-supportive attitudes and beliefs about crime than individuals
who had no contact or were only stopped by police.
Numerous studies have examined whether official labeling has negative effects on other intermediate outcomes such as social and economic
opportunities. In examining employment, for example, experimental data

Custodial Sanctions and Reoffending

000

consistently indicate that employers are significantly less likely to call back
or hire individuals who have criminal records than those without (e.g.,
Pager 2003; Decker et al. 2015; DeWitt and Denver 2020). Pager (2003)
found that, among otherwise identical candidates, individuals with a criminal record are less likely to receive callbacks from employers than those
without a record. This effect was further moderated by race: White candidates with a criminal record were more likely to receive a job callback
than Black candidates without a record. Available evidence from surveys
and interviews with employers suggests their hesitancy about hiring exoffenders stems from concerns over financial or reputational damage
and worker unreliability (Holzer, Raphael, and Stoll 2002; Fahey, Roberts,
and Engel 2006; Goodstein and Petrich 2019).
The results from studies isolating the effects of incarceration on individual offenders’ postrelease employment tend to be mixed, with some
showing that employment outcomes are worse following incarceration
(e.g., Sampson and Laub 1993; Western and Pettit 2005; Apel and Sweeten
2010) and others finding null effects of incarceration on employment (e.g.,
Kling 2006; Loeffler 2013; Verbruggen 2016). In general, though, studies
finding null effects tend to be more recent and made use of more sophisticated analytical techniques (e.g., natural experiments, PSM) to account for
confounder imbalances between incarcerated and nonincarcerated groups.
Loeffler (2013; see also Kling 2006), for example, used an instrumental variable approach to analyze data on over 20,000 offenders in Cook County,
Illinois. After instrumenting on random judge assignment, he showed that
being sentenced to incarceration has no discernible effect on employment
over a five-year follow-up period. In their analyses of the National Longitudinal Survey of Youth, 1997, Apel and Sweeten (2010) use both fixed effects regression models and PSM to examine the impact of incarceration on
employment. With both analytical techniques, they find that incarceration
does lead to unemployment. However, their data also show that this unemployment was due to formerly incarcerated participants not actively looking
for work as opposed to difficulties in obtaining a job, per se. These findings
suggest that although labor market opportunities may be available, former
prisoners may lack the motivation to seek them out (Visher, Debus-Sherrill,
and Yahner 2011).
To summarize, proponents of the mass incarceration movement claim
that the experience of imprisonment is so aversive that it deters offenders
from engaging in future offending. There are several reasons, however,
to expect that any deterrent effect is overshadowed by the criminogenic

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D. M. Petrich et al.

features of imprisonment and its collateral consequences. Prisoners are
surrounded by other prisoners, and they can engage in a mutual exchange
of knowledge and motivation for criminal behavior. They also risk being
victimized by other prisoners and feel the strains of being cut off from family, employment, and other ties to conventional society. The mark of a
criminal record is a major hurdle to finding employment and, accordingly,
to securing housing, providing for their own and their families’ basic needs,
and permanently desisting from crime. Thus, ample grounds exist to expect
that imprisoning offenders has limited or iatrogenic effects on reoffending.

II. The State of Research on Custodial Sanctions
and Reoffending
Prior research examining the effects of custodial sanctions has produced
discrepant findings. Some studies find that terms of incarceration reduce
reoffending when compared to noncustodial sanctions such as probation,
community service, and other community punishments (e.g., Jones and
Ross 1997b; Hjalmarsson 2009; Bucklen 2014; Bhuller et al. 2016). By
contrast, a larger body of research reports that custodial sanctions either
have no effect (e.g., Loeffler 2013; Harding et al. 2017; Mitchell et al.
2017) or increase reoffending (e.g., Aizer and Doyle 2015; Gilman, Hill,
and Hawkins 2015; Mears and Cochran 2018). Conducting a metaanalytic review is a means of assessing what effect these studies reveal when
taken together as a whole. Prior to presenting the systematic analysis, we
discuss several likely reasons for the heterogeneity in effect estimates in
prior research, including variations in methodological characteristics, the
types and lengths of sanctions, and other aspects of studies such as the
age and gender distributions of their samples. We conclude by considering
the results of prior systematic reviews of the literature on custodial sanctions, the shortcomings of those reviews, and advances in the research over
the past decade that motivated this meta-analytic review.
A. Sources of Heterogeneity in Findings
There are three prominent, potential sources of the heterogeneity in
findings on the effects of custodial sanctions. Given their theoretical salience, these factors were included in moderator analyses in our metaanalysis. First, large discrepancies exist in the methodological quality
of studies examining the influence of custodial sanctions on reoffending.

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Although the randomized controlled trial (RCT) is considered the gold
standard for reaching estimates of the causal effect of interventions (Shadish,
Cook, and Campbell 2002), the practical and ethical realities of randomly
assigning offenders to prison versus probation make RCT-based evaluations
rare. Only five such studies have been conducted to date (Bergman 1976;
Schneider 1986; Barton and Butts 1990; Killias, Aebi, and Ribeaud 2000;
Killias et al. 2010). Among them, the Killias et al. (2000, 2010) studies rely
on the same data and, together with the Schneider (1986) study, examine the
effect of two weeks or less of incarceration. The Barton and Butts (1990)
RCT examines a longer period of incarceration (mean p 12.8 months),
while the amount of time is unspecified in Bergman (1976); both use data
that are over 30 years old.
In light of the difficulties with conducting RCTs, the vast majority of
prior research has used observational data coupled with varying levels of
analytical rigor to determine the effects of custodial sanctions. At one end
of the spectrum are analyses that employ neither matching procedures nor
statistical controls to account for nonrandom treatment assignment. This
limitation often characterizes reports from state and federal departments of
correction. For example, McAlister, Officer, and Sanchagrin (2019) reported
the three-year recidivism rates for biannual cohorts of offenders released
from prison or placed on probation in Oregon between 1998 and 2016.
Not surprisingly, the majority of effect size estimates from this and similar
reports point to a large criminogenic effect of prison, likely because people
sentenced to prison tend to differ substantially from people sentenced to
probation. For example, compared with offenders sentenced to noncustodial sanctions, those sentenced to custody tend to have longer criminal
records and more serious conviction offenses, thus signaling a greater risk
for reoffending (Sweeten and Apel 2007; Wermink et al. 2010; Aizer and
Doyle 2015).
Other studies improve estimates by using regression-based techniques
to control for relevant covariates or quasi-experimental methods such as
exact matching, PSM, or instrumental variable analysis. Nagin, Cullen,
and Jonson (2009; see also Bales and Piquero 2012a; Gaes, Bales, and
Scaggs 2016) have previously reviewed the potential problems associated
with regression-based analyses of prison effects (e.g., imprecision of specifying age effects, linearity assumption, over-parameterization), urging researchers to opt instead for quasi-experimental designs. Even among these
methodologies, however, there is variability in model specification that can
be consequential for effect size estimates. For example, Bales and Piquero

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D. M. Petrich et al.

(2012a) show that the sizes of estimates from both exact matching and PSM
are sensitive to the theoretical constructs that matching procedures account
for. Similarly, Gaes, Bales, and Scaggs (2016) illustrate that, despite matching
on the same set of covariates, radius matching, coarsened exact matching,
and exact matching techniques yield substantially different estimates in
terms of size, directionality, and statistical significance.
Beyond these differences in research design and model specification,
the primary studies included in our analysis differ on several other methodological characteristics that might affect estimates of the effects of custody on reoffending. The size of the samples used in individual statistical
models ranged from less than 100 (e.g., Wheeler and Hissong 1988a;
Steiner and Giacomazzi 2007; Sirén and Savolainen 2013) to more than
500,000 (e.g., Mueller-Smith 2014; Gaes et al. 2016). This variation in
sample size influences the confidence accorded the effect sizes reported
by individual studies, with smaller samples being more prone to imprecision (Dattalo 2008; Barnes et al. 2020). Primary studies likewise differ
in how reoffending is measured. Depending on the data available to researchers, reoffending can be captured by indicators of rearrests, reincarceration, violations of community supervision orders, or new charges or
convictions. The period of time during which these forms of reoffending
are measured also varies between studies, ranging from as little as six months
(e.g., Scarpitti and Stephenson 1968) to as much as 15 years (e.g., Gilman,
Hill, and Hawkins 2015).
Second, there is also considerable heterogeneity in characteristics of
the custodial and noncustodial sanctions assessed (Nagin, Cullen, and
Jonson 2009; Villettaz, Gillieron, and Killias 2015). One of the central arguments made by proponents of imprisonment is that sanctions that are
more severe will be more likely to deter reoffending (Becker 1968; Wilson
1975). Thus, to the extent that the conditions and lengths of custodial
sanctions differ, estimates of the effectiveness of incarceration may vary
as well. Deterrence theorists would predict, for example, that the custodial
deterrent effect of prison would likely be larger than that of shock incarceration, and that longer sentences would yield larger deterrent effects
than shorter ones. The studies included in our sample examine a range
of custodial sanctions, including prison, jail, juvenile detention, residential
treatment, boot camp, and shock incarceration. On the noncustodial side,
comparison groups were sentenced to regular probation, intensive probation, electronic monitoring, community service or fines, fully suspended
sentences, dismissals, and nonresidential treatment.

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Beyond the types of sanctions examined, there is also variability in the
literature in the specific combinations of sentences that are examined and
the durations of custody. For example, both Gilman, Hill, and Hawkins
(2015) and Wermink et al. (2010) examine the impact of short-term incarceration (i.e., less than 60 days) on reoffending. However, Gilman et al.
do so with a sample of juveniles compared with others who were arrested
but not incarcerated, whereas Wermink et al. compare short-term custody
with community service within a sample of adults. Some analysts working
with large data sets collapse multiple types of sanctions into singular “custodial” and “noncustodial” categories. In their analyses of 330,971 offenders
in Florida, for example, Mitchell et al. (2017) combined those who had
served time in prison with jail inmates and those who had served regular
probation with those on intensive probation. Using a larger data set from
Florida, Mears and Cochran (2018) chose to disaggregate these groupings
for increased specificity in effect estimates. Most of the existing research on
the effects of custody does not report the mean length of time participants
served behind bars. However, among those that do, there is also considerable variation. The majority examine custodial sanctions of between one
and six months (e.g., Killias et al. 2000; Wodahl, Boman, and Garland 2015),
but some consider sentences of less than one month, between six months
and a year (e.g., Abrams 2010; Freiburger and Iannacchione 2011; Robert
et al. 2017), or two years or more (e.g., Harding et al. 2017).
Third, samples differ on a range of sociodemographic factors that allow researchers to test the generality of the effects of custody. Deterrence
theory is general in its prescriptions about punishment and criminal behavior: custody should exert more of a deterrent effect than noncustodial sanctions regardless of the age and gender of the offender and the country and
the time of incarceration. We included studies produced between 1965 and
2019 and that used data collected in 15 different countries. Within this group
of studies, there is much diversity in the age and gender distributions of
samples. For example, most prior research is based upon mixed-gender
samples, and analysts generally do not conduct supplemental analyses to
determine whether incarceration works differently for males and females
(e.g., Wermink et al. 2010; Bales and Piquero 2012a; Mears and Cochran
2018). However, some researchers investigated sanction effects exclusively
among males (e.g., Cochran, Mears, and Bales 2014; Jolliffe and Hedderman 2015), exclusively among females (e.g., Hedderman and Jolliffe 2015),
or in analyses stratified by gender (e.g., Mitchell et al. 2017; Caudy, Skubak
Tillyer, and Tillyer 2018). Another source of heterogeneity is the age

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composition of samples. The majority of research uses samples composed
solely of adults (e.g., Jones and Ross 1997a, 1997b; Mears, Cochran, and
Bales 2012; Harding et al. 2017). However, 25 studies included in our analysis focus exclusively on juvenile offenders (e.g., Sweeten and Apel 2007;
Aizer and Doyle 2015; Gilman, Hill, and Hawkins 2015).
Although deterrence theory suggests general effects of custody on reoffending when compared with noncustodial sanctions, other theory and
research point to important differences between individuals and contexts
that might lead to heterogeneity in the effectiveness of custody. With regard to gender differences, for example, scholars have argued that women
tend to struggle more than men with adapting to prison life because of
higher rates of mental health and drug use problems, histories of abuse
and trauma, and the strains of family separation (Slotboom et al. 2011;
Mahmood et al. 2012; Kruttschnitt et al. 2013). These gendered differences could conceivably lead to divergent effects of custody on reoffending.
Likewise, because of the neural, psychological, and social plasticity inherent
to adolescence (Laub and Sampson 2003; Somerville, Jones, and Casey 2010;
Sullivan 2020), sentencing juveniles to imprisonment may have a greater
effect—for better or for worse—than for adults. The empirical issue remains as to whether sample characteristics such as gender and age moderate sanctioning effects.

B. Prior Reviews of the Literature
Considering the variability in characteristics of the samples, sanctions,
and designs of prior research, individual studies are limited in their ability to reach a meaningful conclusion about the efficacy of custodial sanctions in reducing reoffending. Accordingly, several groups of scholars
have attempted to make sense of this literature through meta-analytic
and narrative reviews. Five such reviews have been conducted, each concluding that custodial sanctions have either a null or criminogenic effect
on reoffending.
First, in a report to the Solicitor General of Canada, Smith, Goggin, and
Gendreau (2002) meta-analyzed the effects of custodial sanctions by drawing on 104 effect sizes garnered from 31 studies. The mean phi coefficients
in their analyses were between .07 and .00 (unweighted and weighted by
sample size, respectively), indicating a small criminogenic or null effect
of custodial sanctions on reoffending. Smith and colleagues examined only

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000

a small number of potential moderators. However, these analyses indicated
that criminogenic effects were larger in studies of juveniles than adults
(weighted f p .08 vs. .03) and in studies of strong compared to weaker
methodological quality (weighted f p .08 vs. 2.01). The modeling strategy used did not explicitly account for the statistical dependence of multiple effect sizes drawn from some individual studies. Nonetheless, sensitivity analyses showed that the mean effect size estimate remained the
same when multiple, overlapping effect sizes from individual studies were
excluded.
Second, Nagin, Cullen, and Jonson (2009) conducted a systematic narrative review of the literature on custodial sanctions and reoffending that
was published in Crime and Justice. They chose not to meta-analyze the
available research on custodial sanctions because of the between-study heterogeneity in sample characteristics, sanctions being examined, and the
quality of those studies. Results of 55 studies were examined, including five
RCTs, 12 matching studies, and 31 regression-based studies; the remaining
seven were an assortment of natural experiments, inverse probability of
treatment-weighted analyses, and other designs. The main conclusion was
that incarceration seems to have a null or criminogenic effect on subsequent
offending. However, Nagin, Cullen, and Jonson (2009) pointed out that
much of the research then available was methodologically inadequate. Studies that properly accounted for selection into sentences of imprisonment,
such as natural experiments and propensity-score-based analyses, were in
short supply. Accordingly, they urged substantial improvements in methodological rigor, noting that “as studies on the impact of imprisonment on
reoffending become more plentiful and of a higher quality, the application
of meta-analysis to the extant body of evidence would be useful” (Nagin,
Cullen, and Jonson 2009, p. 143).
Third, Jonson (2010) meta-analyzed 177 effect size estimates from
57 studies, finding a small criminogenic effect of custodial sanctions
(mean r p .144). In contrast to Smith, Goggin, and Gendreau (2002), Jonson’s (2010) moderation analyses showed that effect sizes were larger in
samples comprised exclusively of adults and that methodological quality
was not a significant moderator. Furthermore, effect size estimates varied
by the types of both custodial and noncustodial sanctions served and the
gender composition of the samples examined. For example, studies that examined prison or shock probation (e.g., six-month prison sentence, plus
probation) as the custodial sanction found larger criminogenic effects of
custody than studies that examined jail, juvenile detention, and boot camp.

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Although the larger number of effect sizes and methodological moderators
Jonson examined constituted an improvement over Smith and colleagues’
(2002) work, the modeling technique she used did not take into account
the statistical dependence of effect sizes, nor were sensitivity analyses
conducted to examine the influence of such dependence on mean effect
size estimates.
Fourth, in the most recent meta-analytic review, Villettaz, Gillieron, and
Killias (2015) provided an update to an earlier Campbell Review (Villettaz,
Killias, and Zoder 2006) by examining sanction effects among 14 studies.
Focusing solely on the results from RCTs and natural experiments (k p 5),
custodial sanctions had a null effect on reconviction relative to noncustodial
sanctions (mean odds-ratio [OR] p .946, p 1 .05). Among quasi-experimental
studies (k p 9), a small but criminogenic effect of custodial sanctions was
observed (mean OR p .684, p ! .001). A limitation of this work is that
Villettaz and colleagues (2015, p. 42) made the choice to include only a single
effect size from each study, noting that “given the fact that the overall results
favoured the null hypothesis, the strongest effect sizes have been used as a
conservative way to minimize the chance of obtaining a non-significant
outcome.” Because of the restrictive inclusion criteria adopted by Villettaz,
Gillieron, and Killias (2015), the selection of one effect size per study, and
the small number of studies, no moderator analyses were conducted.
Fifth, Loeffler and Nagin (2021) reviewed a subset of studies investigating the effect of incarceration on reoffending. In addition to studies comparing custodial to noncustodial sanctions, they included examinations of
the effects of pretrial detention and the length of custodial sanctions. Their
narrative review focused solely on the results of natural experiments—
namely, those that use random judge assignment for instrumental variable
analysis or regression discontinuity designs to capitalize on discontinuities
created by sentencing guidelines. These natural experiment designs are
powerful in their ability to approximate the random and even distribution
of confounders that is the hallmark feature of RCTs. Considering the
findings from 19 such studies, Loeffler and Nagin (2021) conclude that,
“with only two exceptions, . . . post-conviction imprisonment has no effect
on reoffending or exacerbates it.” Given the similarity of their conclusion
with those of prior reviews, they also note that concerns about lack of control for unobserved characteristics of offenders in standard regression and
matching studies were likely exaggerated (see, e.g., Nagin, Cullen, and
Jonson 2009; Aizer and Doyle 2015; Villettaz, Gillieron, and Killias 2015;
Mitchell et al. 2017).

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C. The Current Review
Against the theoretical, empirical, and methodological backdrop laid
out thus far, our aim was to conduct an updated meta-analytic review
of research comparing the effects of custodial and noncustodial sanctions
on reoffending. We expand upon prior work in three important ways.
First, this is the first comprehensive meta-analytic review of the literature
in over a decade (i.e., since Jonson 2010). Although the review by Villettaz,
Gillieron, and Killias (2015) was published six years ago, their analyses
were limited by a restrictive set of inclusion criteria and by the selection
of only one effect size from each of the 14 studies included (e.g., one from
among 36 effect sizes reported in Bales and Piquero 2012a). In addition to
including 22 quasi-experimental studies published since Villetaz and colleagues (2015), we relaxed the inclusion criteria to allow regression-based,
exact matching, and unadjusted comparisons of individuals sentenced to
custodial and noncustodial sanctions. Doing this allowed us to take stock
of the entire body of research, comprising 981 effect size estimates drawn
from 116 studies. Of these, approximately two-thirds (655) were drawn
from 55 studies released since 2010.
Second, in contrast to past reviews, the large sample of effect size
estimates and detailed coding of studies enabled us to examine whether
variations in research methods, sanctions, and sociodemographic characteristics (e.g., age and gender distributions, country) moderate effect size
estimates. Including studies with wide variability in methodological rigor
increases the heterogeneity of effect sizes. Some scholars suggest that analyzing studies with such differences is akin to comparing apples and
oranges (e.g., Eysenck 1984; Sharpe 1997), and that their inclusion in
a meta-analysis may bias mean effect size estimates. These critics favor conducting meta-analyses on a relatively homogenous—which typically means
small—set of studies with only the highest methodological rigor. Other prominent meta-analysts, however, contend that all studies on a topic should
be included (e.g., Smith, Glass, and Miller 1980; Glass 2015; Turanovic
and Pratt 2021). As Glass (2015; see also Greenland 1994) notes, “all studies
differ, and the interesting questions to ask about them concern how their
results vary across the factors we conceive of as important” (p. 225).2

2
Glass (2015) also comments that he is “staunchly committed to the idea that meta-analyses
must deal with all studies—with good or bad and indifferent studies—and that their results are
only properly understood in the context of each other, not after having been censored by some
a priori set of prejudices” (p. 229).

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Restricting a review to a small subset of studies eliminates the possibility of
discerning which moderators affect the size and direction of the effect
sizes.
Treating the differences between studies as an empirical matter to be
investigated has important implications for both theory and methodological choices. At the theoretical level, it is worth exploring, for example,
whether the deterrence hypothesis finds support only in studies with very
low methodological quality. Examining variations in effect size estimates
across a range of methodological moderators can also provide guidance
for future research aiming to produce more reliable estimates of sanction
effects. To these ends, we explicitly coded for a large number of characteristics such as within- and between-study differences in the overall research
designs employed (e.g., natural experiment, RCT, PSM, regression-based),
variables controlled for or matched on (e.g., age, sentence length, prior
record), the types of sanctions served (e.g., jail, prison, probation, intensive
probation), and sample demographics (e.g., gender and age composition).
Doing so with a large, comprehensive sample of primary studies and effect
size estimates means that heterogeneity is an advantage, allowing for the explicit identification of factors that do or do not moderate effect sizes.
Third, we capitalize on improvements made in meta-analytic modeling techniques since the studies by Smith, Goggin, and Gendreau (2002)
and Jonson (2010)—namely, multilevel modeling (MLM; see Borenstein
et al. 2009; Hox, Moerbeek, and van der Schoot 2018). One advantage
of the MLM approach is that greater weight is assigned to effect size estimates that are more reliable by explicitly accounting for their standard
errors (discussed further in Section III). This approach results in greater precision when estimating mean effect sizes than earlier techniques, such as
weighting effect sizes solely by sample size (i.e., the practice used in both
Smith, Goggin, and Gendreau [2002] and Jonson [2010]; see Pratt et al.
[2014] for further elaboration). The MLM approach also allows for the inclusion of multiple effect sizes from each study by accounting for the dependence of observations. Prior meta-analytic reviews conducted without
MLM have not accounted for such dependence (Smith, Goggin, and Gendreau 2002; Jonson 2010). Furthermore, although Villettaz, Gillieron, and
Killias (2015) used MLM, they chose to include a single effect size from
each study in their models. Both the failure to account for the dependence
of observations within studies and the researchers’ decisions to include specific effect sizes can bias meta-analytic results (Becker 2000; Pratt and
Cullen 2000). The approach we use alleviates both concerns, providing

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the most comprehensive estimate to date of the effect of custodial sanctions
on reoffending.

III. Methods for Assessing Custodial Sanctioning Studies
In this section, we outline the methods used to conduct our meta-analysis.
We describe the multiple techniques that were used to cull the literature,
the criteria for including studies, and how effect size estimates were calculated from statistical models within each study. We also discuss the methodological, sanction, and sample characteristics that were coded for each individual effect size estimate and used to test for the possibility of effect
moderation. We conclude with an explanation of the MLM framework
that was used to meta-analyze the sample of effect size estimates, arrive
at mean effect sizes, and conduct moderation analyses.
A. Sample
Our sample is composed of studies produced through May 2019. They
were systematically gathered in four ways. First, all prior issues of topranking criminology and criminal justice journals were reviewed for studies
that compared the reoffending outcomes of groups sentenced to custodial
versus noncustodial sanctions.3 Second, extensive searches of electronic
databases (i.e., ProQuest Criminal Justice [including dissertations]; EBSCO
Criminal Justice Abstracts with Full Text; PsycINFO [including dissertations]; Google Scholar; and JSTOR Economics) were conducted with
combinations of search terms that captured both the sanction type (i.e.,
“prison,” “imprison∗,” “incarcerat∗,” “boot camp,” and “custodial”) and
outcomes of interest (i.e., “recidivism,” “reoffend∗,” “rearrest,” “reincarcerate∗,”
and “reconvict∗”). Third, the reference lists of studies located through the
first two steps and of prior reviews (i.e., Smith, Goggin, and Gendreau 2002;
Nagin, Cullen, and Jonson 2009; Jonson 2010; Villettaz, Gillieron, and

3
These journals included: Australian and New Zealand Journal of Criminology, British
Journal of Criminology, Crime & Delinquency, Criminal Justice and Behavior, Criminology,
Criminology & Criminal Justice, Criminology & Public Policy, European Journal of Criminology,
International Journal of Offender Therapy and Comparative Criminology, Journal of Contemporary Criminal Justice, Journal of Criminal Justice, Journal of Developmental and Life-Course
Criminology, Journal of Experimental Criminology, Journal of Offender Rehabilitation, Journal
of Quantitative Criminology, Journal of Research in Crime and Delinquency, Justice Quarterly,
Nordic Journal of Criminology, Punishment and Society, Prison Journal, and Youth Violence
and Juvenile Justice.

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D. M. Petrich et al.

Killias 2015) were examined for studies not already captured. Fourth, state
and federal correctional agencies’ websites were searched for unpublished
comparisons of postsanction outcomes for custodial and noncustodial
groups.
The satisfaction of three criteria was required for a study’s inclusion in
the meta-analysis. First, the study must have included a group of offenders
sentenced to time in a custodial setting and a comparison group given an
alternative, noncustodial sanction. Second, the study must have included
some measure of postsanction criminal behavior (e.g., rearrest, technical
violation). Third, the study must also have included sufficient information
to calculate the common effect size used in our analyses. These inclusion
criteria are quite broad, although intentionally so; as described in further
detail below, this allowed us to code for between- and within-study variations in a variety of sample, sanction, and methodological characteristics
that potentially moderate effect sizes.
The literature search and subsequent evaluation of whether the collected studies met the inclusion criteria produced the analytic sample.
It consists of 981 effect sizes calculated from 116 studies that represent
approximately 4.5 million individual offenders in 15 different countries.4
The number of effect sizes exceeds the number of studies because the
majority of studies included more than one statistical model from which
an effect size could be calculated. As an example, Bales and Piquero’s (2012a)
comparison of groups sentenced to prison and intensive probation measured new felony convictions at one, two, and three years; included models
that used six increasingly stringent groups of statistical controls; and modeled the effects of sanctions on reconviction, net of controls, using logistic
regression, precision matching, and PSM. Taken together, the Bales and
Piquero study alone thus yielded 36 effect size estimates.
Including multiple effect sizes from individual studies was done for
two reasons. First, as pointed out elsewhere (e.g., Becker 2000; Pratt and
Cullen 2000; Weisz et al. 2017), choosing a single effect size or averaging
across effect sizes within a study can introduce researcher (e.g., picking the
effect size showing the greatest criminogenic effect of custodial sanctions)
or statistical bias (e.g., artificially reducing between-effect variance). Second, doing so also results in the loss of valuable within- and between-study

4
This figure is approximate given that some studies report the outcomes of multiple release cohorts that may include some of the same individuals.

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information that can be used to explore the characteristics of studies that
moderate effect sizes. Although including multiple effect sizes per study
raises concerns over violating the assumption of statistical independence,
as described in detail below, the multilevel modeling approach used in
the current study adjusted for such dependence.

B. Effect Size Estimate
The effect size estimate in the current study represents the magnitude
of the association between receiving a custodial (as compared to a noncustodial) sanction and subsequent reoffending. Effect sizes were calculated using the standardized correlation coefficient (i.e., r). The r coefficient was chosen because its interpretation is generally more intuitive
than other test statistics typically employed as meta-analytic effect size
estimates (e.g., Cohen’s d ), and other test statistics are easily converted
into r coefficients. Specifically, t-ratios from linear
models (e.g., ordinary
pffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffi
least squares) were converted using r p t= t2 1 n 2 2, while z-ratios
from nonlinear
models (e.g., logistic and Cox regression) were converted
pffiffiffiffiffiffiffiffiffiffiffiffiffi
using r p z= z2 1 n (Rosenthal 1994; Vartanian, Schwartz, and Bronwell 2007). Odds ratios were converted by taking their natural logarithm,
converting to Cohen’s d, and then converting to r (Borenstein et al. 2009).
Given the coding of sanction group membership (i.e., 0 p noncustodial; 1 p custodial), positive r coefficients signify that being sentenced to
a custodial sanction is associated with an increased likelihood of reoffending
relative to people sentenced to a noncustodial sanction. Negative r coefficients signify that a custodial sentence is associated with reductions in
reoffending. For analytical purposes, effect size estimates were converted
to z(r) scores using Fisher’s r to z transformation (i.e., z p 0.5 ∗ ln(1 1
r/1 2 r); see Borenstein et al. 2009). As Pratt et al. (2014; see also Blalock
1972) note, the sampling distribution of the z(r) score is assumed to approach normality, while the distribution of r is not. For the multilevel linear modeling approach that was used, a normal distribution of effect size
estimates is required for unbiased tests of statistical significance, accurate
mean effect size estimates, and tests of their moderation.
We recognize concerns over the potential drawbacks of effect sizes
drawn from both bivariate and multivariate models. The main concern
with bivariate models stems from failing to account for confounds, while
in multivariate models, study-to-study differences in the confounds that
are accounted for may be large (see discussion in Pratt et al. 2014). These

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D. M. Petrich et al.

issues were addressed in two ways. First, we coded for whether effect
sizes were drawn from bivariate or multivariate equations and separated
out calculations of mean effect sizes accordingly. Second, we also coded
for variations in methodological, sanction, and sociodemographic characteristics in the primary studies. These study characteristics are discussed
next.

C. Moderators of Effect Size
The primary goal of a meta-analysis is to determine an overall mean
effect size. In our analysis, this overall effect tells whether primary studies
tend to find that incarceration reduces reoffending relative to noncustodial sanctions. Another question that meta-analyses can address is whether
the size and direction of effect sizes vary significantly based on characteristics of individual studies and statistical models (Hall and Rosenthal 1991;
Borenstein et al. 2009). These moderation analyses are particularly important when there is heterogeneity among primary studies. As discussed in
Section II, the literature on the effectiveness of custodial sanctions is replete with discrepant findings. We also described potential reasons for such
heterogeneity, including variations in the research designs used by the original researchers (e.g., regression, PSM, natural experiment; the specific covariates adjusted for), the sanctions served by participants (e.g., type and
length of sanction), and other sociodemographic characteristics germane
to the generality of custody’s effects on reoffending (e.g., demographic distributions, country, time period). A large, heterogeneous sample of effect
sizes permitted us to code for and analyze whether effect sizes were indeed
moderated by those characteristics. As detailed in Section IV, the vast majority of these characteristics were not statistically significant moderators. In
other words, regardless of the type of study design, sanction, or sample, incarceration has a null or criminogenic effect on reoffending. Below we detail
how these characteristics were coded for each individual effect size in the
sample.
1. Research Design. Several aspects of research design and model specification were coded for each effect size included. We included a categorical
indicator for the overall study design, the statistical model used to calculate
each effect size, or both. The types of designs coded for included those in
which no control or matching variables were used (49.3 percent), multivariate regression models (14.8 percent), basic matching techniques (e.g., exact
matching; 3.8 percent), propensity score matching or inverse probability of

Custodial Sanctions and Reoffending

000

treatment weighting (24.2 percent), natural experiments (e.g., using random judge assignment as an instrumental variable; 7.0 percent), and RCTs
(0.9 percent). Publication type distinguishes studies released as peer-reviewed
journal articles (50.0 percent), state or local reports (34.8 percent), federal
reports (5.9 percent), theses or dissertations (1.7 percent), book chapters
(1.0 percent), or any other type of document (e.g., unpublished working
papers; 6.6 percent). The total sample size was also coded for each effect size.
Categories included fewer than 100 offenders (2.5 percent), 100 to 499
(21.4 percent), 500 to 999 (11.2 percent), 1,000 to 4,999 (13.9 percent),
5,000 to 9,999 (15.3 percent), 10,000 to 49,999 (25.8 percent), 50,000 to
99,999 (5.8 percent), and greater than 100,000 offenders (4.2 percent).
Reoffending measure captures the type of reoffending by which custodial
and noncustodial groups were compared. These include new convictions
(42.7 percent), arrests or charges (30.1 percent), reincarceration (22.6 percent), technical violations (1.6 percent), mixed measures (0.3 percent), and
other types of reoffending (e.g., self-reported offending; 2.7 percent).
Length of follow-up reflects the amount of time samples were tracked for
subsequent reoffending incidents: one year or less (25.3 percent), more
than one to two years (21.5 percent), more than two to three years (35.8 percent), more than three to four years (4.3 percent), or greater than four years
(13.1 percent). Finally, for each effect size, dichotomous indicators for a
wide range of possible confounds were coded, with scores of 1 indicating
the focal characteristic was either matched on prior to analysis or statistically controlled for in the analysis, and scores of 0 indicating the focal
characteristics were neither matched on nor controlled for. The characteristics coded for included age, gender, marital status, employment status,
education level, socioeconomic status, race or ethnicity, type of conviction
offense, age at first offense, prior record, substance abuse, mental health
problems, risk level, and length of sentence.
2. Sanction Characteristics. The types of noncustodial and custodial
sentences served by samples were also coded. In terms of noncustodial sanction type, the majority of effect sizes were derived from samples sentenced to
probation (54.0 percent), followed by intensive probation (15.2 percent),
community service or fines (7.5 percent), suspended sentences or dismissals
(6.0 percent), electronic monitoring or house arrest (3.1 percent), or an explicitly treatment-focused noncustodial sanction (e.g., community-based
drug treatment; 1.7 percent). Approximately 13 percent of effect sizes were
calculated from studies in which the type of noncustodial sanction was categorized as “Other,” capturing both unspecified noncustodial sanctions

000

D. M. Petrich et al.

and low-frequency sanctions (e.g., restorative justice). For the custodial sanction type variable, the majority of effect sizes came from studies in which the
custodial group was sentenced to prison (63.7 percent), followed by juvenile detention (10.8 percent), jail (8.7 percent), boot camp or shock incarceration (3.8 percent), or a secure residential facility (0.9 percent). A further
12.1 percent were coded as “Other,” which indicates unspecified or mixed
sanction types (e.g., where the custodial sample was sentenced to either
prison or jail). The time in custody moderator variable reflects the mean
length of time that offenders in each sample spent in a custodial setting.
The majority of effect sizes were drawn from studies that did not report
the mean length of time in custody (73.8 percent). The remaining studies
reported an average length of incarceration of less than one month (1.4 percent), between one month and less than six months (7.2 percent), between
six months and less than one year in custody (12.8 percent), between one
year and less than two years (2.0 percent), or two or more years (2.7 percent).
3. Sociodemographic Characteristics. Several other characteristics relevant to the generality of custody’s effects on reoffending were coded. For
age composition, most samples were exclusively comprised of adults (66.3 percent), followed by samples that were exclusively juvenile (16.2 percent),
more than 80 percent adult (2.7 percent), or more than 80 percent juvenile
(0.5 percent). A further 14.3 percent of effect sizes came from studies that
did not report the age composition of their samples. For gender composition,
the majority of samples were either exclusively male (15.9 percent) or comprised of more than 80 percent males (33.5 percent), followed by those that
were a “mixed group” (i.e., less than 80 percent male; 13.4 percent), or exclusively female (3.1 percent). A further 34.2 percent of effect sizes were derived from studies in which gender composition was unreported. Publication
decade taps the decade during which the study was published (1960s p 2.0 percent; 1970s p 0.5 percent; 1980s p 3.8 percent; 1990s p 14.2 percent;
2000s p 13.2 percent; 2010s p 66.3 percent). Study location refers to the
country from which the sample was drawn, including the United States
(78.3 percent), Canada (1.3 percent), the United Kingdom (5.3 percent),
Australia (3.4 percent), Nordic countries (i.e., Denmark, Finland, and
Norway; 4.6 percent), the Netherlands (3.8 percent), or some other country
(3.3 percent).
D. Analytic Plan
Once effect sizes and moderating characteristics from each study were
coded, meta-analytic procedures were used to synthesize information across

Custodial Sanctions and Reoffending

000

studies. Specifically, we employed the MLM procedures described by Hox,
Moerbeek, and van der Schoot (2018) and used in other recent meta-analyses
(e.g., Pratt et al. 2014; Pyrooz et al. 2016; Myers et al. 2020) to estimate the
mean effects of custodial versus noncustodial sanctions on reoffending. A
two-level MLM framework was appropriate given that effect size estimates
are nested; that is, Level 1 of the data corresponds to individual statistical
models producing each effect size (N p 981), while Level 2 corresponds to
the studies from which (often multiple) effect sizes were drawn (k p 116).
At Level 1, then, effect sizes within studies often share the same samples
and methods of data collection, while assessing different outcomes and with
different model specifications. Without accounting for this hierarchical nature of the data, the assumptions of the statistical independence of observations and uncorrelated error are violated (Snijders and Bosker 2012), thus
increasing the likelihood of biased tests of statistical significance because
of artificially deflated standard errors and narrow confidence intervals (Kreft
and de Leeuw 1998). However, the MLM framework resolved these issues
and accounted for both within- and between-study sources of dependence
through the inclusion of a unique random effect for each organizational unit
(Pratt et al. 2014; Turanovic et al. 2021). Calculation of the intraclass correlation coefficient for the full analytic sample provides further evidence of
the necessity to account for both sources of variation; 47.8 percent of the
variance in effect size estimates was within studies (j2 p .0065, p ! .001),
while 52.2 percent was between studies (j2 p .0071, p ! .001).
Another issue with hierarchical meta-analytic data is that a portion of
the variance of Level 1 effect size estimates is assumed to be known (Hox
and de Leeuw 2003). Explicitly accounting for this variance is crucial given
that effect size estimates are drawn from other studies that vary in precision
(e.g., because of differences in sample size or model specification).
To do
pffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffiffi
so, we calculated standard errors for each effect size using j p 1=(n 2 3)
for bivariate effect size estimates and j p Fisher’s z(r)/(b/SE) for multivariate effect size estimates (Lipsey and Wilson 2001). These effect size
standard errors were incorporated into the random part of the Level 1
equation (StataCorp 2013; Hox, Moerbeek, and van der Schoot 2018; see
also Pratt et al. 2014; Pyrooz et al. 2016; Myers et al. 2020), thus enabling
effect size estimates to be weighted by their precision and models to account
for within-study variation beyond what is implied by their known variance.
With these considerations in mind, the analyses presented below proceeded in four stages. First, we estimated the overall mean effect of custodial sanctions (compared with noncustodial sanctions) on reoffending. We

000

D. M. Petrich et al.

examined these mean effect sizes across the entire sample of 981 effect size
estimates, as well as when looking only at estimates derived from bivariate
or multivariate models. Second, we conducted a series of bivariate moderator analyses to determine whether the overall mean effect of custodial
sanctions on reoffending was robust across variations in characteristics of
individual studies and statistical models. All bivariate moderator analyses
were conducted by entering only the focal moderator variable into the regression equation. Third, we examined the influence of significant moderators from the previous step when considered together in a multivariate
meta-regression model, both with the full sample and restricted to effect
sizes from multivariate models. Fourth, we examined whether effect sizes
differed between studies that met a set of methodological “best-case” criteria and those studies that did not meet those strict criteria. All analyses were
conducted in Stata 15 using the -meglm- command with maximum likelihood estimation.

IV. Assessing the Effects of Custodial Sanctions:
A Meta-Analysis
This section presents the results of our meta-analysis of research comparing the outcomes of offenders sentenced to custodial versus noncustodial
sanctions. Part A describes findings regarding the overall mean effect of
custodial sanctions in the entire sample of effect size estimates. We also
present average effect sizes broken down by the type of research design
used to generate each effect size. These analyses reveal that, on average,
sentencing offenders to custodial sanctions has either null or criminogenic
effects on reoffending. Part B discusses findings on whether the effects of
custodial sanctions vary significantly by the statistical models or research
designs used in primary studies, the sanctions examined, and other demographic characteristics. As we show, although there is some evidence of
moderation, the null or criminogenic effects of imprisonment persist regardless of all these characteristics.
A. Overall Strength of Effects
The first objective of the meta-analytic review was to determine the
overall mean effects of custodial sanctions on reoffending. These effects
are reported in table 1. Estimates were obtained from unconditional
models—that is, models in which no other predictors were entered into

Custodial Sanctions and Reoffending

000

TABLE 1
Mean Estimates for the Effect of Custodial Sanctions on Recidivism
Model Estimation
Full sample (981)
No controls/matching (484)
Multivariate (497)

Mean ESE
∗∗∗

.079
.098∗∗∗
.067∗∗∗

95 Percent CI

Min

Max

ICC

.061 to .096
.069 to .127
.048 to .086

2.319
2.319
2.271

.572
.572
.484

.522
.478
.745

NOTE.—Number of effect sizes are in parentheses. CI p confidence interval; ESE p
effect size estimate; ICC p intraclass correlation coefficient.
∗

p ! .05.
p ! .01.

∗∗

∗∗∗

p ! .001 (two-tailed test).

the equations. However, given the variance-known, multilevel framework used in the analyses, effect sizes that are more precise received a larger
weight (see Pratt et al. 2014; Hox, Moerbeek, and van der Schoot 2018).
Values in the “Mean ES” column in the table can be interpreted as the average correlation between a custodial sentence and reoffending. Considering the full sample of 981 effect size estimates drawn from 116 primary
studies, table 1 shows that the mean correlation between a custodial sentence and reoffending was .079. This effect size means that, on average,
being sentenced to custody increases reoffending.
The size of this criminogenic effect is small when compared against predictors of crime that have been meta-analyzed previously. For example,
Bonta and Andrews (2017) found that the average correlation between adhering to the principles of effective correctional treatment and reoffending
is 2.260. Other studies have likewise shown that self-control (mean correlation p .257; Pratt and Cullen 2000), gang membership (mean correlation p .227; Pyrooz et al. 2016), and peer influence (mean correlation p
.321; Gallupe, McLevey, and Brown 2019) have much stronger effects on
crime than sentencing individuals to terms of imprisonment. Although the
effect of custodial sanctions on reoffending is smaller than these other
predictors of crime, it may nonetheless be substantively important. A mean
correlation of approximately .080 translates into an 8 percentage point difference in reoffending between those sentenced to custodial and noncustodial sanctions (Bonta and Andrews 2017; see also Randolph and Edmondson
2005). Thus, assuming that 46 percent of the comparison (noncustodial)
group reoffended, the percent reoffending in the custodial sanction group
would be 54 percent. When extrapolated to a group the size of the incarcerated

000

D. M. Petrich et al.

population in the United States, this difference is meaningful. At the very
least, from a policy perspective, this finding indicates that custodial sanctions do not reduce recidivism.
Table 1 also reports mean effect sizes when broken down by whether
primary studies relied on bivariate or multivariate analyses. Unsurprisingly, the largest criminogenic effects were observed in bivariate models
that did not make use of any statistical controls or match participants on a
set of covariates. In other words, no attempts were made in these analyses
to account for the preexisting differences between individuals sentenced
to custody and those sentenced to a noncustodial sanction such as probation. The mean correlation between a sentence of custody and reoffending
in these bivariate models was .098. In multivariate models (e.g., multiple
regression, matching, propensity score analysis), however, the mean correlation was approximately .067. Although this effect size is approximately
32 percent smaller than that observed in bivariate models, multivariate
models still point to a small but statistically significant criminogenic effect of imprisonment on reoffending.
B. Robustness of Effects
The key takeaway from the results presented thus far is that, on average, custodial sanctions appear to have a small criminogenic effect on reoffending. However, given that this finding represents an average effect
across many different studies and statistical models, it is important to determine whether there are conditions under which the overall finding
changes. It is possible, for example, that imprisonment acts as a deterrent
for juvenile offenders but is criminogenic for adult offenders, or that prisons
in the United States are far more criminogenic than prisons in European
countries. Likewise, it has been suggested that studies with poor methodological quality may produce vastly different findings than studies of strong
methodological quality (Nagin, Cullen, and Jonson 2009; Villettaz, Gillieron, and Killias 2015). In light of these possibilities, we followed the
common practice of conducting meta-analytic moderation analyses (see,
e.g., Pratt et al. 2014; Pyrooz et al. 2016; Gallupe et al. 2019). These analyses tested whether the overall mean effect of custody was indeed sensitive
to study-to-study variations in methodological quality, the sanctions examined, and the sociodemographic characteristics of samples.
The moderator analyses proceeded in three phases, each of which is discussed further below. First, we separately examined the influence of each
moderator variable on effect size estimates. The goal of this phase was to

Custodial Sanctions and Reoffending

000

determine which characteristics of studies predict variation in effect size
estimates when examined at the bivariate level. Second, statistically significant moderators of effect sizes were included together in two different
meta-regression models. The purpose of this phase was to test whether
moderators maintained a significant influence on effect size estimates after
controlling for the influences of the other moderators. In the first model,
these meta-regression tests were conducted on the full sample of effect sizes
(N p 981), while the second was restricted to effect sizes that came from
multivariate models that accounted for the differences between offenders
sentenced to custody and those to noncustodial settings (N p 497). Third,
we examined whether effect sizes from an even smaller pool of high-quality
studies (N p 226) differed significantly from those that did not meet rigorous standards (N p 755). The results presented below indicate that,
through each of the successive analytic phases, fewer characteristics of studies
emerge as statistically significant moderators of effect size estimates. Although there are some characteristics that maintain a significant moderating
effect through all phases, the ultimate finding is that imprisonment has a null
or slight criminogenic effect on reoffending regardless of variations in methodological quality, the sanctions evaluated, and sociodemographic characteristics of the samples. In other words, we find no conditions under which
custody tends to reduce reoffending.
1. Bivariate Moderator Analyses. In the first set of moderation analyses,
the effect of each study characteristic on effect sizes was assessed separately.
These analyses were conducted with the entire sample of 981 effect size
estimates. Findings from these models are presented in tables 2–4. The
intercepts in these tables are interpreted as the mean effect size estimate
when the moderator is set at its reference category—the category listed first
for each variable. Estimates displayed in the coefficient columns should likewise be interpreted as the change in effect size when the moderator variable
is moved from the reference category to another category of interest. For
example, inspection of the publication type variable in table 2 shows that
the mean effect size estimate for studies published in peer-reviewed journals
(the reference category) was .066. The positive coefficient for studies released in a state or local reports indicates a larger criminogenic effect (i.e.,
.066 1 .040 p .106), although the difference between effect sizes in peerreviewed journals and state or local reports was not statistically significant.
The results in tables 2–4 suggest that some methodological, sanction,
and sociodemographic characteristics do moderate effect sizes. However,
despite variation away from the overall mean effects reported in table 1,

TABLE 2
Bivariate Moderator Analyses for the Impacts of Methodological
Characteristics on Effect Size Estimates
Moderator Variable
Study design:
No controls/matching (484)
Multivariate regression (145)
Basic matching (37)
PSM/IPTW (237)
Natural experiment (69)
RCT (9)
Publication type:
Peer-reviewed article (501)
State/local report (334)
Federal report (57)
Thesis/dissertation (16)
Book chapter (10)
Other (63)
Sample size:
100 to 499 (210)
!100 (24)
500 to 999 (110)
1,000 to 4,999 (136)
5,000 to 9,999 (150)
10,000 to 49,999 (253)
50,000 to 99,999 (57)
1100,000 (41)
Recidivism measure:
Arrest/charge (291)
Conviction (426)
Reincarceration (219)
Technical violation (15)
Other (27)
Length of follow-up:
≤1 year (245)
11 year to ≤2 years (206)
1 2 years to ≤ 3 years (347)
13 years to ≤4 years (44)
14 years (133)
Statistical controls/matching variables:
Age (419)
Gender (394)
Marital status (67)
Employment status (79)
Education (140)
Socioeconomic status (65)
Race/ethnicity (349)
Conviction offense (313)

Coefficient

SE

z-Value

Intercept
.102∗∗∗

2.054
2.020
2.007
2.107
2.047

.015
.029
.014
.024
.054

23.59∗∗∗
2.69
2.54
24.51∗∗∗
2.87
.066∗∗∗

.040
.047
2.033
.159
.020

.024
.038
.050
.064
.040

1.67
1.26
2.66
2.49∗
.52
.086∗∗∗

.003
2.000
2.012
2.003
2.008
2.064
2.066

.038
.014
.017
.022
.017
.024
.023

.08
2.01
2.69
2.16
2.46
22.73∗∗
22.86∗∗
.091∗∗∗

2.023
2.024
.048
2.009

.009
.009
.032
.025

22.55∗
22.53∗
1.53
2.34
.070∗∗∗

.011
.011
.029
.017

.010
.010
.028
.017

1.13
1.03
1.03
1.01

2.041
2.037
.018
.004
.032
.035
2.012
2.028

.011
.012
.022
.019
.016
.021
.012
.013

23.74∗∗∗
23.08∗∗
.79
.21
1.94
1.70
21.01
22.17∗

.098∗∗∗
.094∗∗∗
.077∗∗∗
.078∗∗∗
.074∗∗∗
.077∗∗∗
.083∗∗∗
.089∗∗∗

Custodial Sanctions and Reoffending

000

TABLE 2 (Continued )
Moderator Variable
Age at first offense (54)
Prior record (392)
Substance abuse (77)
Mental health (36)
Risk level (65)
Sentence length (98)

Coefficient

SE

z-Value

Intercept

.017
.001
.044
2.026
2.045
2.066

.022
.012
.021
.062
.022
.018

.78
.11
2.12∗
2.43
22.02∗
23.70∗∗∗

.077∗∗∗
.078∗∗∗
.075∗∗∗
.079∗∗∗
.084∗∗∗
.083∗∗∗

NOTE.—Estimates are based on the full sample (N p 981). The frequencies of effect
size estimates are in parentheses. Models were estimated separately for each moderator.
IPTW p inverse probability of treatment weighting; PSM p propensity score matching;
RCT p randomized control trial; SE p standard error.
∗

p ! .05.

∗∗

p ! .01.
p ! .001 (two-tailed test).

∗∗∗

the effects of custody remain null or criminogenic. In table 2, findings related to the possible moderating effects of variations in methodological
characteristics are presented. These results illustrate that effect sizes drawn
from studies using multivariate regression models and natural experiments
were significantly less than those drawn from studies that used no controls
or matching variables. For example, the mean correlation between custody
and reoffending in the uncontrolled studies was .102, indicating a small but
statistically significant criminogenic effect of imprisonment. This effect
was reduced to .048 and 2.005 in multivariate regression and natural experiment studies, respectively. Effect sizes from studies that used basic
matching or propensity score techniques did not differ significantly from
those of uncontrolled studies.
Table 2 also indicates that variations in sample size had little influence
on effect sizes until samples reached 50,000 offenders. Specifically, studies with samples of between 50,000 and 99,999 and greater than 100,000
had significantly smaller effect sizes than those with 100 to 499 participants.
The type of publication in which results were presented made little difference
in effect size estimates. The only category that differed significantly from
peer-reviewed journal articles was results appearing in book chapters.
However, this category contained only 10 effect size estimates drawn from
two studies, so this result should be interpreted with caution. In terms of
the type of reoffending assessed, effect size estimates were smaller for both
convictions and reincarcerations when compared to models examining

000

D. M. Petrich et al.

arrests or charges. The length of postsanction follow-up, which varied
quite widely across the entire sample, did not emerge as a moderating
factor. Finally, we also examined whether controlling for or matching
participants on a host of theoretically relevant confounds impacted effect
size estimates. As table 2 indicates, models that included controls for or
matched on age, gender, conviction offense type, risk level, and sentence
length reported smaller effects of custody on reoffending than models
that did not. By contrast, models that controlled for or matched on participants’ history of substance abuse produced larger effect size estimates.
Table 3 displays the findings of moderator analyses examining the impact of variations in sanction characteristics on effect size estimates. As
noted in Section III, the sample included effect sizes from studies that examined a range of different forms of custodial and noncustodial sanctions.
The most common form of custodial sanction examined in primary studies
was prison, accounting for 63.9 percent of the sample of effect size estimates (N p 627). Among studies that examined the effects of prison, the
intercept column in table 3 shows that the mean correlation between custody and reoffending was .053. This finding indicates that serving a term in
prison has a small, but statistically significant, criminogenic effect on postrelease reoffending. Table 3 also shows that relative to studies examining
prison, being sentenced to jail or juvenile detention was associated with a
larger criminogenic effect of imprisonment. In terms of the various types
of noncustodial sanctions, probation was the most common form represented in the sample of effect sizes (53.5 percent; N p 525). For studies
that used probationers as a comparison group, the mean correlation between custody and reoffending was .113, which again demonstrates that serving time in custodial settings has a criminogenic effect. The results reported
in table 3 reveal that, relative to studies examining probation, the effects of
custody were smaller in magnitude—albeit still criminogenic—when comparison offenders were sentenced to receive intensive probation, community service or fines, a suspension or dismissal, or some other noncustodial
disposition. Table 3 also shows that variations in the amount of time spent
in custody generally had no moderating influence on effect size estimates.
The sole exception was that, when compared with studies that did not report the length of custody, the mean criminogenic effect of custodial
sanctions was smaller in studies examining individuals sentenced to between one and less than six months in prison.
Table 4 presents the results of moderation analyses examining sociodemographic characteristics that might affect the generality of custody’s

Custodial Sanctions and Reoffending

000

TABLE 3
Bivariate Moderator Analyses for the Impact of Sanction Characteristics
on Effect Size Estimates
Moderator Variable
Custodial sanction type:
Prison (627)
Jail (85)
Juvenile detention (104)
Boot camp/shock (36)
Residential treatment (11)
Other (118)
Noncustodial sanction type:
Probation (525)
Intensive probation (148)
EM/house arrest (34)
Community service/fine (79)
Tx-focused NCS (16)
Suspended/dismissal (57)
Other (122)
Time in custody:
Not reported (724)
!1 month (14)
1 to !6 months (71)
6 months to !1 year (126)
1 to !2 years (20)
≥2 years (26)

Coefficient

SE

z-Value

Intercept
.053∗∗∗

.072
.096
2.032
.030
.046

.015
.018
.037
.062
.026

4.75∗∗∗
5.41∗∗∗
2.84
.49
1.74
.113∗∗∗

2.096
2.038
2.048
2.017
2.053
2.061

.012
.029
.023
.040
.019
.020

28.04∗∗∗
21.30
22.09∗
2.43
22.74∗∗
23.05∗∗
.087∗∗∗

2.027
2.093
.001
2.040
2.053

.027
.045
.024
.038
.069

21.00
22.09∗
.02
21.04
2.77

NOTE.—Estimates are based on the full sample (N p 981). The frequencies of effect size
estimates are in parentheses. Models were estimated separately for each moderator. EM p
electronic monitoring; NCS p noncustodial sanction; SE p standard error; Tx p treatment.
∗

p ! .05.
p ! .01.

∗∗

∗∗∗

p ! .001 (two-tailed test).

effects on reoffending. Several findings are noteworthy. First, results for
age composition indicate that the average correlation between custody and
reoffending was .065 in adult-only samples but increased to .112 in juvenileonly samples. Thus, imprisonment appeared to have larger criminogenic
effects for juveniles than adults when no other moderators were included
in the regression model. Second, studies using mixed-gender samples (80 percent or less male) tended to report larger criminogenic effects of custody
than studies examining male-only samples. There was, however, no significant difference in mean effect sizes between exclusively male and exclusively
female samples, although the number of effect sizes from female-only

000

D. M. Petrich et al.

TABLE 4
Bivariate Moderator Analyses for the Impact of Sociodemographic
Characteristics on Effect Size Estimates
Moderator Variable
Age composition:
Exclusively adults (644)
Exclusively juveniles (158)
180% adults (230)
180% juveniles (5)
Missing (144)
Gender composition:
Exclusively males (159)
Exclusively females (30)
180% males (331)
Mixed (133)
Missing (328)
Publication decade:
2010s (655)
2000s (130)
1990s (136)
1980s (36)
1970s (5)
1960s (19)
Study location:
United States (762)
Canada (12)
United Kingdom (51)
Australia (33)
Nordic countries (47)
The Netherlands (40)
Other (36)

Coefficient

SE

z-Value

Intercept
.065∗∗∗

.047
.015
.030
.040

.014
.038
.077
.038

3.37∗∗
.39
.38
1.05
.067∗∗∗

.024
.013
.078
2.015

.026
.020
.012
.021

.95
.65
6.30∗∗∗
2.75
.080∗∗∗

2.011
2.022
.034
.168
.018

.024
.023
.038
.071
.065

2.48
2.97
.90
2.37∗
.28
.070∗∗∗

.019
.030
.049
2.022
.040
.041

.054
.040
.040
.049
.042
.342

.36
.75
1.22
2.56
.96
1.21

NOTE.—Estimates are based on the full sample (N p 981). The frequencies of effect size
estimates are in parentheses. Models were estimated separately for each moderator. SE p
standard error.
∗
p ! .05.
∗∗

p ! .01.

∗∗∗

p ! .001 (two-tailed test).

samples was quite small (N p 30). Third, neither the country from which
data were drawn nor the decade during which studies were published generally had any significant association with the size of custody’s effects on
reoffending.
To summarize the results thus far, the bivariate moderator analyses suggest that some aspects of the primary studies’ research designs, the sanctions

Custodial Sanctions and Reoffending

000

evaluated, and the sociodemographic characteristics of samples do account
for variation in effect size estimates. Effect sizes tended to be smaller, albeit
still null or criminogenic, in studies that used stronger research designs,
accounted for more confounding factors related to reoffending (e.g., age,
gender, risk level), and had larger sample sizes. Incarceration also appeared
to be more criminogenic for juvenile offenders than for adults, and there
were many differences in effect size when looking at variations in the specific forms of custodial and noncustodial sanctions (e.g., probation versus
intensive probation, jail versus prison). However, factors such as the length
of follow-up, amount of time spent in custody, the gender composition of
samples, the decade of publication, and the country from which data were
collected had no significant moderating influence on effect sizes. In other
words, the effects of custody were general across those characteristics.
2. Meta-Regression Moderator Analysis. Although some characteristics
emerged as significant moderators in the bivariate analyses, it is important
to note that moderators may be correlated with each other (Lipsey 2003).
Without accounting for the correlations between moderators, the relationships between them and effect sizes may be spurious and the magnitudes of
their associations inflated or deflated. For example, we explained above that
stronger research designs tend to produce smaller effect sizes than weaker
designs. However, it is possible that there is nothing inherent in the design
itself that affects effect sizes, but rather that stronger designs tend to account for a broader range of confounders (e.g., age, gender, prior record).
In order to evaluate whether those sorts of moderator confounding issues
existed in our bivariate analyses, the next step was to examine the statistically significant moderators from the initial bivariate analyses together in
meta-regression models. This regression approach provides a stronger test
of moderation given its ability to isolate the effect of a given moderator
after controlling for the influence of other moderating variables. As detailed below, the meta-regression approach was used to assess moderation
in both the full sample of effect size estimates (N p 981) and a subsample of
effect sizes from multivariate studies that accounted for at least some
confounding variables through random assignment, matching, or statistical
controls (N p 497).
To conduct the meta-regression analyses, it was necessary to initially
check that multicollinearity among the variables was not a concern. Multicollinearity exists when there are very strong correlations between the
independent variables included in a regression model. Strong correlations
can indicate that the variables are measuring the same construct, making

000

D. M. Petrich et al.

it difficult to isolate the effect of any single variable (Weisburd and Britt
2014). To check for this problem, we examined the data for correlations
of greater than .750 between moderating variables and variance inflation
factors above 4.00 (Tabachnick and Fidell 2007; Weisburd and Britt 2014).
In the full sample of effect size estimates (N p 981), diagnostic tests indicated multicollinearity between the statistical control or matching indicators.
For example, there were very strong correlations between the indicators of
whether studies had included age and race (r p .740), prior record (r p
.756), and current offense-type (r p .744) in their statistical models. Given
the presence of multicollinearity between the statistical control or matching
indicators, those variables were excluded from the meta-regression with the
full sample.
Findings from the meta-regression analysis with the full sample are
presented in table 5 (Model 1). The results were quite similar to the bivariate moderator analyses reported above in tables 2–4. Specifically, after accounting for the influence of other moderator variables, effect sizes from
multivariate regression models and natural experiments tended to be
smaller than effect sizes from studies that did not use statistical controls /
matching variables. There were no significant differences between uncontrolled or unmatched studies and those using basic matching or propensity
score techniques. Likewise, there were significant differences in effect sizes
depending on the specific types of custodial and noncustodial sanctions examined. For example, studies examining jail, juvenile detention, and residential treatment tended to report larger criminogenic effects of custody
than studies examining prison. Studies examining intensive probation, community service or fines, and suspended sentences or dismissals also reported
smaller criminogenic effects of custody than studies examining regular probation. Another similarity to the bivariate moderator analyses was that the
full-sample meta-regression indicated studies examining convictions and
reincarceration tended to report smaller effect sizes than studies examining
rearrests. There were, however, two important differences in the full-sample
meta-regression model. First, in the bivariate analyses, the criminogenic effects of custodial sanctions were larger in studies with juvenile-only samples
than in adult-only samples. In the meta-regression context, this effect was no
longer significant. This finding suggests that once other aspects of studies are
accounted for (e.g., research design, covariates adjusted for, sample size), the
outcome of incarceration is generally the same for both adults and juveniles.
Second, large sample sizes (i.e., greater than 50,000) were no longer a significant predictor of effect size estimates in the meta-regression context.

Custodial Sanctions and Reoffending

000

The full sample meta-regression (table 5, Model 1) analysis revealed
that fewer characteristics of studies moderate effect size estimates once
other variables are controlled for. To probe this issue further and provide
an even stronger test of moderation, we thus estimated a second metaregression model with a subsample of effect sizes from multivariate models that accounted for confounding variables through random assignment, matching, or statistical controls (N p 497). In this reduced sample,
correlations between the statistical control or matching variable indicators
were no longer problematic (e.g., correlation between age and prior record
was 2.040), and none of the variance inflator factors exceeded 4.00; thus,
these indicators were included in analyses of the multivariate effect size
estimates. As the results in table 5 (Model 2) illustrate, there are several important findings when examining moderators of effect size within the
multivariate-only sample. First, there are still differences in effect size based
on the overarching research design used in the primary studies. Effect sizes
from models using basic matching and propensity score techniques were
significantly larger than those from multivariate regression models, while
those from natural experiments were smaller. Similar to the earlier moderator analyses, the reductions in effect size for natural experiments were sizable. However, even with these reductions, the mean effect of custody is
null or slightly criminogenic.
Second, the types of statistical controls or matching variables used in
models were less predictive of effect size estimates after accounting for
other moderators in the multivariate sample. Specifically, only age, socioeconomic status, and risk level remained statistically significant in the
meta-regression model. Studies that included any of those three variables
tended to report smaller effect sizes than studies that did not include them.
However, whether studies included other factors such as sentence length,
conviction offense, and gender was no longer predictive of effect size in the
multivariate-only sample. Third, when looking at the type of reoffending
measure used by researchers, effect sizes from studies examining convictions remained smaller than those using arrest after accounting for other
moderators. Finally, the specific types of sanctions examined—both custodial and noncustodial—made less of an impact on effect size estimates in
multivariate models. For example, in contrast to the analyses of the full
sample that included bivariate effect size estimates (table 5, Model 1), multivariate models that examined jail and juvenile detention did not have significantly different effect sizes from those examining prison as a custodial
sanction. In other words, better-controlled models tend to find that custody

TABLE 5
Multivariate Meta-Regression of Effect Size Estimates on
Methodological, Sanction, and Sociodemographic Variations
Model 1
Full Sample
Moderator Variables
Fixed Effects
Model Intercept
Study design:
No controls/matching
Multivariate regression
Basic matching
PSM/IPTW
Natural experiment
RCT
Sample size:
100 to 499
!100
500 to 999
1,000 to 4,999
5,000 to 9,999
10,000 to 49,999
50,000 to 99,999
1100,000
Recidivism measure:
Arrest/charge
Conviction
Reincarceration
Technical violation
Other
Statistical controls/matching variables:
Age
Gender
Marital status
Employment status
Education
Socioeconomic status
Race/ethnicity
Conviction offense
Age at first offense
Prior record
Substance abuse
Mental health
Risk level
Sentence length
Custodial sanction type:
Prison

Coefficient

SE

Model 2
Multivariate Sample
Coefficient

SE

.125∗∗∗

.024

.086∗∗

.029

2.067∗∗∗
2.035
.001
2.129∗∗∗
2.050

.015
.030
.015
.023
.057

(Ref )
.066∗
.036∗
2.069∗∗∗
.002

.027
.018
.011
.052

.033
.015
.001
.009
.005
2.027
2.017

.037
.014
.017
.022
.018
.030
.026

.009
.043∗∗
2.006
.014
2.011
.017
.012

.042
.013
.015
.017
.016
.031
.022

2.026∗∗
2.026∗∗
.060∗
.023

.008
.009
.029
.086

2.034∗∗
2.005
.019
.007

.013
.014
.036
.016

2.053∗
.020
2.010
.026
2.010
.065∗
2.015
.029
.028
.031
.000
.015
2.076∗∗
2.019

.026
.026
.026
.032
.026
.028
.022
.021
.018
.018
.028
.056
.026
.015

000

TABLE 5 (Continued )
Model 1
Full Sample
Moderator Variables
Jail
Juvenile detention
Boot camp/shock
Residential treatment
Other
Noncustodial sanction type:
Probation
Intensive probation
EM/house arrest
Community service/fine
Tx-focused NCS
Suspended/dismissal
Other
Age composition:
Exclusively adults
Exclusively juveniles
180% adults
180% juveniles
Missing
Gender composition:
Exclusively males
Exclusively females
180% males
Mixed
Missing
Number of effect sizes (Level 2)
Random effects:
Level 1 (Effect size estimates):
Variance between models
Variance explained
Level 2 (Study):
Variance between studies
Variance explained

Coefficient

SE

Model 2
Multivariate Sample
Coefficient

SE

.084∗∗∗
.072∗
2.042
.101∗∗∗
.017

.014
.032
.037
.027
.062

2.007
2.029
2.088∗∗
.025
.008

.015
.037
.033
.055
.026

2.101∗∗∗
2.029
2.046∗
2.030
2.056∗∗
2.073∗∗∗

.011
.028
.023
.041
.056
.021

2.001
2.006
2.027
.021
2.063∗∗∗
2.012

.012
.023
.024
.033
.012
.021

.012
.023
2.051
2.007

.023
.038
.078
.042

2.008
.005
.010
...

.017
.050
.067
...

.011
.012
2.068∗
2.036
2.000

.021
.020
.031
.026
.001

.001
.013
2.029
2.037
2.000

.013
.015
.022
.027
.001

.00499
24.11%

.00028

.00131
36.30%

.00014

.00680
4.36%

.00131

.00402
35.14%

.00094

NOTE.—Full sample N p 981; Multivariate sample N p 497. Abbreviation: SE p standard error.
∗

p ! .05.
p ! .01.

∗∗

∗∗∗

p ! .001 (two-tailed test).

000

000

D. M. Petrich et al.

is ineffective or criminogenic regardless of which specific form of custody
is examined. Coefficients for the noncustodial sanction type indicators similarly show that custody has null or criminogenic effect regardless of the
type of noncustodial sanction served by comparison groups.
Taken together, our meta-regression analyses reveal that very few factors moderate effect sizes capturing the influence of custodial sanctions
on reoffending. In other words, the analyses show that the null or slight
criminogenic effect of custody is general rather than specific to particular
research designs, varieties of custodial or noncustodial sanctions, or sociodemographic characteristics of samples. The minimal effects of custody on
reoffending are the same for both males and females and both adults and
juveniles. The effects of custody also do not vary much based on whether
researchers study prison, jail, or other forms of custodial sanctions, or whether
they compare custody to probation, intensive probation, electronic monitoring, or other noncustodial sanctions. The overarching study design (e.g., uncontrolled, propensity score analysis, natural experiment) and type of reoffending measured did have significant moderating influences on effect size
estimates in both meta-regression models. However, none of these moderation effects were large enough to change the overall finding of a null or
criminogenic effect of custody on reoffending.
3. Best-Case Studies. As a final step in the analyses, we sought to identify the mean effect size estimate in studies that met the methodological
“best-case” criteria. As discussed previously, Nagin, Cullen, and Jonson
(2009; see also Villettaz, Gillieron, and Killias 2015) note that although
RCTs are the gold standard for evaluating treatment effectiveness, they
are often neither viable nor ethical when sanctioning offenders. At a minimum, then, they urge researchers to implement quasi-experimental designs
that can account for the influences of offenders’ age, race or ethnicity, gender, current offense, and prior record on both sanction assignment and
reoffending. We therefore conducted a supplementary analysis that compared mean effect size estimates drawn from studies that implemented a natural experiment or RCT, or used propensity score techniques to account for
at least the five factors noted above, with studies that did meet these criteria.
As expected, the mean correlation between custody and reoffending among
the 226 effect sizes that met these criteria (r p .050) was approximately 40%
smaller than the mean among the 755 effect sizes that did not (r p .083).
However, these results illustrate that even in studies that meet fairly rigorous methodological criteria, a weak but statistically significant criminogenic
effect of custodial sanctions is observed.

Custodial Sanctions and Reoffending

000

We thus reach the same conclusion as all of the other analyses presented
in this essay: imprisonment has either no effect or makes reoffending
outcomes worse when compared with noncustodial sanctions such as probation, electronic monitoring, or otherwise. This finding echoes those of
prior reviews of the literature by Smith, Goggin, and Gendreau (2002),
Nagin, Cullen, and Jonson (2009), Jonson (2010), and Villettaz, Gillieron,
and Killias (2015). However, we have extended those reviews to show that
the null or criminogenic effect of custody exists regardless of the specific
varieties of custodial and noncustodial sanctions that are compared; the
age and gender distributions of participants; where the data were collected;
the type of reoffending measured and for how long; and variations in the
research designs of primary studies. Although effect sizes did vary significantly by research design and the type of reoffending measured across all
analyses, the substantive conclusion of a null or criminogenic effect did
not change. There does not appear to be a particular group of offenders
that is more deterrable by incarceration than others, nor a particular type
of research design that points to a deterrent effect when others do not
(for a similar conclusion, see Loeffler and Nagin 2021).

V. Conclusion
In 1976, Gordon Hawkins incorporated into his short but illuminating
book, The Prison: Policy and Practice, a chapter on “The Effects of Imprisonment.” He reviewed commentary on why prisons might or might not be
“schools of crime.” For those on either side of the debate, some consolation
could be drawn from knowing that the “belief that all who enter prison are
ineluctably doomed to deterioration” has no more basis than the “antithetical idea” that prisons might “transform all offenders into model citizens”
(p. 80). In moving forward, he argued that “critical evaluation of penal
measures is an essential precondition to rational and effective policy formulation and planning” (1976, pp. 175–76). Alas, a “lack of knowledge”
existed, which prompted Hawkins (1976, pp. 175–76) to caution, “There
is depressingly little methodologically rigorous evaluative research available to guide our efforts.”
Five years later, Hawkins joined with Michael Sherman in another
slim volume taking stock of “imprisonment in America.” Sherman and
Hawkins (1981, p. 1) documented troubling trends, noting that the nation’s
prisons and jails may house “more than a half million adults,” a “fraction of
the citizenry larger than that of any other Western nation.” They noted that

000

D. M. Petrich et al.

conversations in the US Senate ranged from Strom Thurmond declaring
that “overcrowded conditions in our prisons have become a national crisis”
to Joe Biden introducing federal legislation to fund the construction of more
prison cells at the state and local level (1981, p. 3). They decried this “crisis
mentality,” however, arguing that the opportunity still existed to “choose
the future” of American corrections. They argued for a balanced approach
that incorporated conservative and liberal values and that would stabilize
prison populations. Sherman and Hawkins (1981, p. 132) trumpeted this
approach as a “principled stance” and concluded that “it seems literally a
shame not to try.”
Four decades later, the consequences of “not trying” are palpable. The
era of mass imprisonment that unfolded was costly, negatively affected
the lives of individuals and communities, had racially disparate effects,
and left the nation with an incarcerated population of approximately two
million—a figure that makes the half million inmates of 1981 seem almost
quaint (Clear 2007; Alexander 2010; Simon 2014; Aviram 2015; Pratt
2019). Still, Hawkins’s writings are useful not only as a reminder of the correctional past that existed when his books were written but also for the
lessons they teach that remain pertinent today. Two seem most important.
First, moments exist when the opportunity to choose a new correctional future is most propitious. Historians can settle whether 1981 was
one of these occasions. It is clearer, however, that we are now at a possible
correctional turning point where the past does not have to be a prelude to
the future (Petersilia and Cullen 2015). The seemingly ineluctable growth
in prisons halted around 2009 and has since trended gradually downward
(Maruschak and Minton 2020). Public punitiveness is in prolonged decline
(Enns 2016; Pickett 2019), and public support for correctional reform, including alternatives to incarceration, is widespread (Sundt et al. 2015;
Thielo et al. 2016; Butler et al. 2020).
Second, Hawkins is correct that “rational” policy and practice should be
informed by research. The lack of knowledge was near complete when The
Prison was written, but this is not the case today, when “evidence-based
corrections” has evolved. Substantial scientific evidence, much of it based
on evaluation research, provides direction on what does and does not work
to change the behavior of justice-involved individuals (Lipsey and Cullen
2007; Bonta and Andrews 2017; more generally, see Cullen and Jonson
2017). This literature is clear in showing the limits of punishment-oriented
interventions. Among this category of punitive sanctions, the data reveal
that custodial placements, including in prison settings, are not effective

Custodial Sanctions and Reoffending

000

in reducing future reoffending. We explore below the implications of this
conclusion for criminology and public policy.

A. A Criminological Fact
Over the past two decades, research has steadily accumulated assessing
the effects of custodial sanctions, including imprisonment, on reoffending.
Although developing slowly at first and with variable quality, this line of inquiry has produced a growing number of quasi-experimental and regressionbased studies. This literature has been assessed through careful systematic
reviews (Nagin, Cullen, and Jonson 2009; Loeffler and Nagin 2021) and
by meta-analyses (Smith, Goggin, and Gendreau 2002; Villettaz, Killias,
and Zoder 2006; Jonson 2010; Villettaz, Gillieron, and Killias 2015). Every review has reached nearly the same conclusion: compared with noncustodial sanctions, custodial sanctions, including imprisonment, have no appreciable effect on reducing reoffending. The studies tend to show that placing offenders
in custody has a slight criminogenic effect, although this association is not
sufficiently robust to argue for its certainty. In most analyses, including
ours, some moderator factors may influence effect sizes, but they do not
qualify the central conclusion regarding custodial sanctions.
Based on past research and the findings of this meta-analysis, the limited
effects of custodial sanctions on reoffending should be viewed as a criminological fact. The null effects finding has been replicated repeatedly and independently. The highest quality studies reduce the criminogenic effect
of custodial sanctions but do not eliminate it. This meta-analysis of a large
sample of heterogeneous studies reaches the same conclusion. Narrative
reviews do also. Consensus that custodial sanctions, overall, do not reduce
reoffending is universal.
Calling the null effects finding a criminological fact is not an attribution
of sacred status. Facts in science are based on the available literature. When
the literature is slim, caution is advised. As shown vividly by Ritchie (2020)
in Science Fictions, many claims about empirical reality do not replicate and
are eventually renounced. Long ago, Merton (1942, p. 126) highlighted
the importance of the scientific norm of “organized skepticism”—of the
community of scholars scrutinizing assertions and suspending “judgment
until ‘the facts are at hand.’” In the current case, however, scrutiny has occurred and the facts are at hand. The literature is large and its conclusions
are consistent. Unless prisons and other custodial settings change their nature, there is no reason to expect that a new generation of studies will

000

D. M. Petrich et al.

reveal their crime-reducing effects. Although we acknowledge that empirical claims are always open to revision, if not falsification, we believe the
point has been reached at which custodial sanctions as a behavioral intervention can be adjudged—using the rating scheme employed by the National Institute of Justice’s Crime Solutions—as having “no effects” (see
https://crimesolutions.ojp.gov/rated-programs).
B. Policy Implications
Imprisonment can be justified on the grounds of just deserts and incapacitation, but the criminological fact of a null effect for custodial
sanctions undermines any justification based on specific deterrence. In
a time of evidence-based corrections, those favoring prisons on this basis
are embracing a policy, with substantial economic and social costs, that
has no demonstrable effects on reoffending. The research on custodial
effects is thus salient in providing critics of incarceration with data showing that a key rationale for locking people up is empirically invalid. Advocates of custodial sanctions are in the uncomfortable position of
defending something that the existing evidence concludes is ineffective
(Cullen, Jonson, and Nagin 2011).
A pernicious aspect of prison policy in past decades is that the immiseration of inmates was trumpeted as a means both to exact retribution
(making prisoners suffer) and to increase the pains that deliver the lesson
that crime does not pay. Prisons as a deterrent requires no positive action.
If prisons are crowded, unsafe, and unhealthy, the accumulation of misery
makes their burdens more intense. This thinking rationalized deliberate
efforts to push the policy of “austere” or “no frills” prisons (Applegate 2001).
Although limited, research shows that harsh or painful prison conditions
are not associated with reductions in reoffending and, if anything, are
criminogenic (Chen and Shapiro 2007; Drago, Galbiati, and Vertova 2011;
Listwan et al. 2013; Mastrobuoni and Terlizzese 2018). Punitive custodial
conditions cannot be justified on crime-savings grounds (Cullen, Jonson,
and Nagin 2011). As Durlauf and Nagin (2011) show, the core engine
underlying effective deterrence is the certainty and not the severity of punishment—a stubborn reality that argues against the continued overuse and
extensive financial investment in imprisonment (see also Chalfin and
McCrary 2017).
A common response to the null effects finding is to call for research on
the mechanisms that might cause some inmates to become more prosocial
and others less so (Nagin, Cullen, and Jonson 2009; Mears, Cochran, and

Custodial Sanctions and Reoffending

000

Cullen 2015; Loeffler and Nagin 2021). Moderator analysis does this on a
broad level, seeing, for example, if sanction effects vary by factors such as
age (juveniles vs. adults) or risk (low vs. high) categories. These analyses
have not yielded consistent findings. Furthermore, to unlock the black
box of prison effects on individual offenders, it would be necessary to conduct, in essence, a life-course study of inmates from the time they enter
prison to the time they complete a period of community supervision. Such
a study would need to measure factors associated with offender change in
the literature, including cognitive, motivational, or identity transformations
(Maruna 2001; Paternoster and Bushway 2009; Petrich 2020), acquiring social bonds (Sampson and Laub 1993), and relinquishing antisocial attitudes
and associates (Bonta and Andrews 2017). From a policy perspective, this
knowledge might provide guidance on what prison programs and practices
to employ while offenders are in custody.
On a broader level, a more transformative policy approach appears warranted. If the past is the best predictor of the future, there is no reason to
believe that custodial settings will produce different effects unless they are
fundamentally changed. More of the same will produce more of the same,
which has been demonstrated by consistent findings reported in literature
reviews and meta-analyses over the past two decades. Informed by the
findings of the Stanford Prison Experiment (Zimbardo 2007), one position
is that total institutions are inherently inhumane and coercive. They are
not capable of inspiring the better angels of anyone—the kept or their
keepers. Null effects, or worse, are inevitable. The alternative view is that,
as with all organizations, management matters. Prisons can be “governed”
well or poorly, and they can achieve goals if designed to do so (DiIulio
1987).
As Rothman (1971) detailed in his classic Discovery of the Asylum, the
inventors of the American prison believed that if the internal workings of
the prison could be designed perfectly—either as a solitary or congregatesilent system—inmates would be transformed into law-abiding citizens.
Alas, the “penitentiary” was based on the flawed correctional theory that
offender resistance to worldly temptations could be strengthened by forced
isolation from corrupting influences in a context of hard work and religious
influence. But the underlying vision of these early reformers had merit: the
key to changing offenders is creating an institution intended and organized
to achieve this outcome.
In this regard, two flaws inhibit the capacity of the modern correctional institution to reduce reoffending: intended goals and organizational

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D. M. Petrich et al.

design. First, despite research showing that correctional workers—from
wardens to correctional staff and new recruits—support rehabilitation
(Cullen, Lutze, et al. 1989; Cullen, Latessa, et al. 1993; Sundt and Cullen
2002; Burton et al. 2021), these sentiments are not translated into a shared
organizational goal. In particular, achieving a reduction in recidivism is
not monitored or incentivized (Cullen, Jonson, and Eck 2014). In recent
decades, police departments seeking to decrease crime events implemented
crime mapping and statistical systems to measure fluctuations in offending
and to hold managers accountable for improved performance (see, e.g.,
Weisburd et al. 2003). In corrections, however, no similar movement has
materialized. Performance reviews of wardens and staff do not take account
of institutional reoffending rates. Custodial facilities, especially prisons, are
generally not evaluated for their effectiveness in changing inmate behavior.
Rhetoric aside, reducing reoffending is not the intended goal of correctional
institutions. It should be—if this outcome is to be attained.
Second, within community corrections, some agencies embracing the
“RNR Model” (Bonta and Andrews 2017) have tried to create an organization capable of rehabilitating supervisees. A key tool is the Correctional Program Assessment Inventory (CPAI), which is a multifaceted assessment tool comprising a series of surveys or checklists that evaluators
use to identify an agency’s adherence to the principles of effective intervention (Bonta and Andrews 2017). Research shows that reductions in
recidivism are positively associated with scores on the CPAI (Lowenkamp,
Latessa, and Smith 2006; Lowenkamp et al. 2010; Bonta and Andrews
2017). The implications for prisons and custodial settings are clear. Drawing on the evidence-based treatment theory informing the CPAI, correctional organizations should be redesigned to become people-changing institutions. This would include repeated assessment of offender risk levels,
use of effective treatment modalities, building quality relations between
staff and inmates, training staff in techniques to reinforce prosocial attitudes and behavior, providing released prisoners with systematic aftercare, continual monitoring and evaluation of staff and the organization,
and creating an organizational culture marked by concern for ethical values
and for the use of core correctional practices (Bonta and Andrews 2017).
An immediate objection is that these reforms are too costly. Three responses are merited. First, many practices are not expensive but simply
require greater professionalism. Effective counseling sessions lasting an hour
are no more expensive than ineffective counseling sessions lasting an hour.
Similarly, interacting with prisoners using cognitive behavior techniques

Custodial Sanctions and Reoffending

000

costs no more than interacting with prisoners coercively and ineffectively.
Second, with internet access, much inmate assessment and staff training
can be conducted virtually and at low expense. Such services can be delivered from centralized locations, either from within departments of corrections or from universities, across multiple institutions. Third and most
important, doing more of the same with dismal results is indefensible. The
opportunity costs of failing to reduce reoffending are enormous: prisoners
return to crime and often to prison, and citizens are victimized in minor and
serious ways. These harms are potentially preventable. Prisoner lives
should matter—for their benefit and ours.

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