LABELING THEORY CAPSTONE PAPER

Ex-offender employment programs and recidivism:

A meta-analysis

CHRISTY A. VISHER*, LAURA WINTERFIELD and

MARK B. COGGESHALL Urban Institute, 2100 M St. NW, Washington, DC 20037, USA

*corresponding author: E-mail: cvisher@ui.urban.org

Abstract. One consequence of the tremendous growth in the number of persons under supervision of

the criminal justice system, whether incarcerated, on parole, or on probation, is the effect of this

criminal history on finding and keeping a job. Ex-offenders, especially those recently released from

prison, face substantial barriers to many types of legal employment; nonetheless, stable employment is

one of the best predictors of post-release success. Thus, policy-makers concerned about high recidivism

rates face an obvious need to improve the employment prospects of ex-offenders. Over the last 25 years,

many programs that were designed to increase employment (and, by so doing, reduce recidivism) among

ex-offenders have been implemented and evaluated. [Wilson, D. B., Gallagher, C. A., Coggeshall, M. B.

& MacKenzie, D. L. (1999). Corrections Management Quarterly 3(4), 8Y18; Wilson, D. B., Gallagher, C. A. & MacKenzie, D. L. (2000). Journal of Research in Crime and Delinquency 37(4), 347Y368] conducted a quantitative synthesis and meta-analysis of 33 evaluations of educational, vocational, and

work programs for persons in correctional facilities. To date, however, the evaluation literature on

employment programs for those with a criminal record who are not in custody has not been

systematically reviewed. This paper presents the results of a quantitative meta-analysis of eight random

assignment studies of such programs, using the Campbell Collaboration methodology. The results

indicate that this group of community employment programs for ex-offenders did not reduce recidivism;

however, the experimental design research on this question is small and does not include some of the

promising community employment programs that have emerged in the last decade.

Key words: employment programs for offenders, experimental studies, meta-analysis, offenders,

prisoners, randomized controlled trials, recidivism, systematic review

Introduction

As is well known, the rapid growth of prison populations that occurred in the late

1980s and 1990s has translated into a large flow of men and women being released

from prison. A key policy concern that has emerged is identifying strategies that

would help former prisoners successfully reintegrate into their communities and

reduce the likelihood that they would commit new crimes.

Research has indicated that having a legitimate job lessens the chances of re-

offending following release from prison and that recidivism is less likely among

those with higher wages and higher quality jobs (Sampson and Laub 1997; Harer

1994). A good job not only provides the means for basic survival, but also is a key

element in rebuilding self-esteem, attachment to a conventional lifestyle, and a

Journal of Experimental Criminology (2005) 1: 295–315 # Springer 2005

sense of belonging in the community. Work organizes daily behavior and patterns

of interaction, and becomes an important source of informal social control for ex-

offenders (Sampson and Laub 1977; Uggen 1999; Uggen and Staff 2001; Wilson

1997).

According to data from a national study, three-quarters of state inmates reported

that they held a job just prior to their incarceration (Lynch and Sabol 2001).

Nonetheless, having a criminal record represents a substantial barrier to many

types of legal employment, and these barriers are compounded after a term of

prolonged incarceration. Long periods of incarceration may weaken social contacts

that lead to legal employment opportunities upon release (Western et al. 2001;

Hagan and Dinovitzer 1999). Research also suggests that having a criminal record,

whether an arrest, conviction, or prison term, adversely affects subsequent

employment wages and job stability, even after controlling for duration or severity

of prior criminal involvement (Bushway 1998; Western et al. 2001; Sampson and

Laub 1997). Other barriers that ex-offenders face in finding and keeping a job

include the lack of recent job experiences, a lessening of job-related skills, and

transportation difficulties.

These barriers to gainful employment coupled with the likely public safety

consequences of high levels of unemployment among ex-offenders create an

immediate need to identify effective interventions that might increase employment

for this population. Employment interventions can be either in-prison programs or

post-release employment services, or rarely, both. Although the period of incar-

ceration could be viewed as an opportunity to build skills and prepare for placement

at a future job, the evaluation literature has provided mixed to negative support for

the effectiveness of in-prison job training programs, including a meta-analysis of 33

programs (Bushway and Reuter 1997; Gaes et al. 1999; Wilson et al. 1999, 2000).

A flurry of community-based employment interventions, generally involving

some combination of job readiness, job training, and job placement services, were

implemented in the 1970s and 1980s, mostly with government support. There is a

long history in the United States of federal funding of community employment

programs for former prisoners, and for disadvantaged youth and adults who may

have arrest or conviction records. The U.S. Department of Labor funded programs

targeted to former prisoners under the authority of the Manpower Development

and Training Act of 1962. The result of that early effort was the well-known

studies of Living Insurance for Ex-Prisoners (LIFE) and the Transitional Aid

Research Project (TARP), which were the first major experimental evaluations of

community employment programs for ex-prisoners. However, the results did not

clearly support the value of such programs in reducing recidivism (Mallar and

Thornton 1978; Rossi et al. 1980). A series of federal job training programs

followed, including the 1973 Comprehensive Employment and Training Act

(CETA), the 1983 Job Training Partnership Act (JTPA), and the 1998 Workforce

Investment Act (WIN). After the end of CETA in 1982, government funding of

employment programs for adult ex-prisoners largely disappeared, although JTPA

and WIN continued to target disadvantaged older youth (including those with

arrest records). In 2002, with the recent resurgence of attention to prisoner reentry

CHRISTY A. VISHER ET AL.296

and the obstacles former prisoners face in finding and keeping jobs, the Depart-

ment of Labor developed Ready4Work, a business, faith and community pilot

initiative for increasing employment of ex-offenders in 18 cities.

Several large-scale, experimental evaluations of the older DOL programs have

been conducted, but results for ex-offender subgroups have been reported only

rarely. Unfortunately, the conclusions from these evaluations have generally been

disappointing (Bushway and Reuter 2002; Uggen et al. 2002). In addition, a small

group of other evaluations of community employment programs for ex-offenders

exists that has not been integrated with the older studies. Thus, a systematic review

of community employment programs for ex-offenders and their effects on re-

cidivism will provide new information on the effectiveness of these interventions.

The primary research question for this meta-analysis is: What is the effect of

non-custodial employment services interventions on the subsequent criminal

behavior of ex-offenders? This review will survey the existing empirical evidence

that examines the effectiveness of community employment programs on recidivism

among persons who have been previously arrested, convicted, or incarcerated. It is

limited to those studies using random assignment because of the specific interest in

isolating effects from experimental designs. The remainder of this paper presents

the studies reviewed and the findings from our meta-analysis; implications for

policy and practice are then discussed.

Subjects and methods

Our review has focused on studies using random assignment experimental designs.

Eligible studies had to have included one or more treatment groups and one or more

comparison groups. Some measure of criminal behavior subsequent to the beginning

of the intervention must have been reported for the ex-offenders in both the

treatment and comparison groups. The outcome measure of criminal behavior may

have been either official (i.e., arrest, conviction, technical violation) or self-reported

and may have been reported either dichotomously or on a continuous scale.

Both the treatment and comparison groups must have been composed, at least

in part, of ex-offenders: persons who had been arrested, convicted, or incarcerated

in connection with a criminal charge before becoming a study subject. If either the

treatment or comparison group included subjects who were not ex-offenders, the

results must have been reported so that effect sizes could be coded for the ex-

offenders alone. Only studies of adults (as defined by the jurisdiction within

which a given study is conducted) or studies that combine older youth (age

16Y17) and adults are eligible for this review.1 Studies were excluded if the comparison group included persons who did not meet the eligibility criteria for the

treatment. The comparison group could have received either Ftreatment as usual_ or no treatment. Comparison subjects may have been drawn from waiting lists or

Ftreatment as usual_ pools; if the treatment group was drawn from subjects who volunteered to receive the intervention, the comparison group also had to be com-

posed of volunteers.

EX-OFFENDER EMPLOYMENT PROGRAMS AND RECIDIVISM: A META-ANALYSIS 297

In order to be included, some of the treatment must have been delivered in a

non-custodial setting (i.e., not in a prison or jail); studies of treatment delivered in

a halfway house, group home, or similar facility were eligible. The program may

have been either residential or non-residential so long as equivalent residential and

custodial requirements were placed on both the treatment and comparison subjects.

The treatment program must have included a job-placement component or a job-

training component, although other components, such as life-skills training,

remedial education, or social-service assistance, may have been included. In the

case of multiple-service delivery, all components (i.e., employment and non-

employment components) were coded.

This review only includes study reports written in English. It is not known how

many studies in other languages may be eligible. Further, we limited our search to

those studies where at least some of the study subjects received treatment after

1964, and the study was completed during or since 1970 in order to ameliorate the

potential effects that changes in the economic environment might have on

programmatic effectiveness. This was necessary because most of the programs

available for analysis occurred during the 1970s and 1980s.

Study identification and selection

So that we did not rely on only published studies in highly visible academic

journals, where the tendency is to report on studies that demonstrate effectiveness,

we used the following search modes:

� Contacts with leading researchers; � Searches of the bibliographies of published reviews of related literature in the

U.S. and Western Europe (Uggen et al. 2002; Bushway and Reuter 2002; Buck

2000; McGuire 1995; Webster et al. 2001); � Scrutiny of annotated bibliographies of related literature (e.g., Clem 1999); and � Searches of computerized databases.

The specific databases that were searched were:

� Catalog of U.S. Government Publications (CGP), U.S. Government Printing Office;

� Criminal Justice Abstracts; � Digital Dissertations; � Economic Literature Index; � National Criminal Justice Reference Service (NCJRS) Abstracts; � ProQuest Social Sciences Index; � Sociological Abstracts; � Social Science Citations Index; � Wilson Humanities Index; and � The Campbell Collaboration Social, Psychological, Educational and Crimino-

logical Trials Register.

CHRISTY A. VISHER ET AL.298

The specific search terms that we used were Boolean combinations of: (1)

employment, job train, job counsel, job placement, job-seekers allowance, jobless

benefit, employable, after-care, case manage, job service; and (2) offender, ex-

offender, criminal, arrest, convict, incarcerat, parole, probation, diversion, inmate.

Each word was following by a question mark to denote any number of unspecified

characters (e.g., incarcerat? could be incarcerate or incarceration).

The literature on employment and crime, broadly defined, is voluminous and

our search methods generated hundreds of titles, most of which had abstracts. If the

abstract did not mention an evaluation report, no further review was initiated. For

the 30Y35 reports thought to be evaluations using random assignment designs, full studies were requested and reviewed by one of the senior authors (Visher or

Winterfield). Studies were divided into four categories: experimental studies with

random assignment, quasi-experimental studies, non-experimental studies, and

other (process evaluations, review articles, etc.).

The total number of independent studies using random assignment designs that

satisfied our eligibility criteria was eight, including two studies in which two sep-

arate samples were coded. Upon review, two studies thought to be eligible ended

up being excluded. First, a British evaluation of a program that provided

employment assistance to ex-offenders was excluded because the amount of

assistance provided was not standardized for the treatment group (Soothill 1999).

Second, an evaluation of a work release program was excluded because the

requirement that both treatment and control groups be in a similar residential status

was not met and the experimental design was compromised by the addition of a

matched comparison group to increase the sample size (Turner and Petersilia

1996).

Data management

A Microsoft Access database was constructed for the meta-analysis, and infor-

mation from the eligible studies was entered into the database. The database

included details on study eligibility, program description, sample description,

treatment-group circumstances, methodological rigor, outcome information, and

effect-size information.

When an eligible study report did not provide the necessary information to

calculate effect size (for example, outcomes could have been reported for

subgroups of treatment and control groups, differentiated by age, but the subgroup

Ns may not have been available), we contacted the original authors by email; there

were two instances for which this was necessary. Of these, one author could not

retrieve the necessary information, and one author was able to do so. The first

study was, however, included in this review after we learned from one of the

authors that a reasonable approximation of the size of the treatment and

comparison groups could be estimated based on the sampling criteria (ratio of

treatment to comparison sample was 2 : 1).

EX-OFFENDER EMPLOYMENT PROGRAMS AND RECIDIVISM: A META-ANALYSIS 299

Description of studies

The eight studies identified for this review were conducted over more than 20

years, with the first study being implemented in 1971 (Mallar and Thornton 1978)

and the most recent study being implemented in 1994 (Rossman et al. 1999).

(Publication dates are not a good indicator of when the study was conducted

because several studies we include are based on reanalyses of previous studies.)

Four studies were published in academic journal or book publications. Three

studies were nonpublished reports to government agencies, including one that has

not been widely cited in the recent literature on employment and recidivism

(Rossman et al. 1999). Four studies included women (Rossman et al. 1999; Rossi

et al. 1980; Cave et al. 1993; Schochet et al. 2001). Combining across studies,

more than 6,000 older youth (aged 16Y17) and adults with prior contact with the criminal justice system participated in the eight studies in this review.

2

Six of the experiments were simple two-group designs (the exceptions being

Rossi et al. 1980 and Mallar and Thornton 1978), and all reports explicitly stated

that study participants were randomly assigned to either the treatment or control

group. However, the specific procedures for conducting random assignment were

either only vaguely described or not described at all. Recidivism measures

primarily included arrests, based on either official record sources or self-reported

information. The follow-up periods ranged from 6 to 36 months. Taken together,

these eight experimental studies with random assignment designs that examined

the impact of job training and employment programs, albeit broadly defined,

among ex-offenders report modest or no effects of such services on criminal

activity. We summarize each study below in chronological order by date of

program initiation.

The Baltimore Living Insurance for Ex-prisoners (LIFE)

The Baltimore Living Insurance for Ex-Prisoners (LIFE) experiment was the

initiation of several studies sponsored by the U.S. Department of Labor in the 1970s

(Mallar and Thornton 1978; see also Rossi et al. 1980: Ch. 2). The Department of

Labor was acting on a mandate from the Manpower Development and Training Act

of 1962, which provided for programs that would aid released prisoners in

obtaining employment. A series of demonstration projects tested the hypothesis

that income support to released prisoners would facilitate post-release adjustment

and reduce the likelihood of property crimes. Beginning in 1971, 432 prisoners

released from Maryland state prisons and returning to Baltimore were randomly

assigned to one of four groups: those who received 13 weeks of payments of $60

per week and intensive job counseling and placement services, those who received

payments only, those who received counseling and placement only, and a control

group who received neither payments nor counseling. However, eligibility for the

program (before random assignment) was limited to prisoners who were

considered at high risk for returning to prison because of their previous criminal

CHRISTY A. VISHER ET AL.300

history (see Mallar and Thornton 1978: 210Y211). Recidivism was measured as any new arrest at 1 year.

The LIFE experiment found that those receiving weekly cash payments of $60

(about $225/week in 2002 dollars, based on CPI) had fewer arrests in the first year

than those in the control group. Surprisingly, when examining just arrests for theft,

the largest effects were for those study participants who did not receive job

placement services along with the financial assistance. Uggen et al (2002) point out

that this early experiment found an age interaction in that those who were at least

26 years old were much less likely to be arrested than younger participants.

Transitional Aid Research Project (TARP)

Following the results of the LIFE experiment, the Department of Labor decided to

repeat the study with slightly different benefits and no limits on eligibility in two

additional experiments, commonly referred to as the Transitional Aid Research

Project (TARP). Initiated in Texas and Georgia in 1976, approximately 4,000 ex-

prisoners participated in two studies (one in each state) with random assignment

into four experimental and two control groups in each study (Rossi et al. 1980;

Berk et al. 1980). 3

The experimental treatments included either unemployment

insurance benefits or job placement. For those who received the unemployment

insurance benefits, either 13 or 26 weeks of eligibility for unemployment insurance

benefits could be received; for those who received the 13 weeks of benefits, either

100% or 25% tax rate on earnings could be received. Computerized arrest records

in each state were examined 1 year after participants had been released from

prison.

TARP, which was intended to be a replication and extension of LIFE, added a

program detail that was not communicated effectively to participants (termination

of or reduction in payments when employment was secured), which may have led

to a work disincentive effect (Rossi et al. 1980: 7). 4

The evaluators claim that the

resulting unemployment of program participants had the effect of increasing arrests

for the treatment group; no significant differences were found in arrest rates

between the four TARP experimental groups and two control groups in either

Georgia or Texas. 5

Thus, the financial assistance experiments of the 1970s (LIFE

and TARP) were not consistent in their findings of an impact of such programs on

criminal activity.

National Supported Work Demonstration

The National Supported Work Demonstration, also funded by the U.S. Department

of Labor, enrolled in nine U.S. cities men who had been recently incarcerated,

were currently unemployed, and had been employed for no more than three of the

preceding 6 months between 1975 and 1977 (Piliavin and Gartner 1981; Uggen

2000). Study participants were randomly assigned to either minimum-wage jobs in

crews with 6Y8 other workers or a control group. In a reanalysis of the original

EX-OFFENDER EMPLOYMENT PROGRAMS AND RECIDIVISM: A META-ANALYSIS 301

data, Uggen (2000) examined first self-reported arrest for two theoretically im-

portant subgroups: those under age 26 and those aged 26 and older. The combined

sample size was 3,105 and the follow-up period ranged from 18 to 36 months,

depending on the date of enrollment into the program.

Uggen’s (2000) reanalysis of the National Supported Work Demonstration

showed that the effect of an employment program varied by the age of the study

participants. Specifically, a program that originally was deemed a failure was

found to significantly reduce recidivism among ex-offenders over the age of 26.

For younger ex-offenders, at the end of 1 year, 31% of those in both the treatment

and control groups reported that they had been arrested. Among older offenders,

however, those in the treatment group had arrest rates about 8 percentage points

lower than those in the control group. These differences increased to 11 percentage

points after 3 years (Uggen 2000). [Exact percentages of those arrested by age

group are not provided.] Uggen’s work (1999, 2000; Uggen et al. 2002), docu-

menting the significance of age of participant in the success of the employment

program, is an important step forward in the disappointing 20-year history of

job training and employment programs for ex-offenders.

Job training program for probationers

In a study conducted in a Midwestern city during the years 1979, 1980, and 1981,

216 probationers were randomly assigned to either a job training program or to

standard community probation (Anderson and Schumacker 1986). Program partic-

ipants were CETA-qualified and were aged 18 to 25 years. The program provided a

variety of job-training skills including preparing resumes and employment

applications, role-playing job interviews, and providing some skills training.

Participants were compared on an overall measure of recidivism, including arrests,

probation revocation, and new sentence, at 6 and 12 months. Anderson and

Schumacker (1986) found no differences in 6- and 12-month outcomes in their

evaluation of the job training program for probationers. At 6 months, 15% of the

control group and 13.5% of the treatment group had Fdifficult_ outcomes, defined as probation revocation, or new conviction resulting in a jail or prison sentence. At

12 months, the adjusted means showed fewer difficult outcomes for the treatment

group compared to the controls (15.5% vs. 23%), but the difference was not

statistically significant. Because of the need to control for some differences

between the groups, we chose to code adjusted means for the meta-analysis.

Job Training Partnership Act (JTPA)

The Job Training Partnership Act (JTPA) supported employment and training

programs for economically disadvantaged Americans, including school dropouts

with previous arrest records. Services provided varied across sites and were

individually tailored to study participants. For the ex-offender youths, services

CHRISTY A. VISHER ET AL.302

typically included basic education and Bmiscellaneous services^ such as job- readiness training, vocational exploration, job shadowing, and tryout employment

(Bloom et al. 1994: 27, 51). JTPA is described as a less intensive approach than

either JOBSTART or the youth component of the National Supported Work

Demonstration. The evaluation, commissioned by the U.S. Department of Labor,

required an experimental design with random assignment to treatment and control

groups at 16 study sites during the period 1987 to 1989. The study reports arrest

outcomes for 390 male ex-offenders at an average follow-up period of 21 months

and 198 participants at 36 months (Bloom et al. 1994).

The evaluation of the Job Training Partnership Act (JTPA) program found no

discernable effects on male youth (aged 17Y21) with previous arrest records. During the first follow-up period (at 21 months, on average), 43% of both the

treatment and control group had been arrested. At the second follow-up (at 36

months, on average), 59% of the youth in JTPA were arrested, compared to 56% of

the control group (Bloom et al. 1994: Exhibit 11).

JOBSTART

The JOBSTART demonstration was created in 1985 as an alternative approach to

both Job Corps (see below) and the Job Training Partnership Act (JTPA).

JOBSTART provided a combination of basic skills education, occupational

training, support services and job placement assistance to young, low-skilled

school dropouts in 13 sites between 1985 and 1989. One subgroup in the

evaluation comprised 291 male and female ex-offenders (with a prior arrest) aged

17Y21 who were either randomly assigned to the experimental group or a control group (Cave et al. 1993). Arrest records were examined for participants and

controls at 1 and 4 years after enrollment in the program.

JOBSTART, which provided longer-term services than JTPA to an essentially

similar population of disadvantaged young adults with arrest records, also found no

differences between the treatment and control groups at the end of 4 years. At the

end of 1 year, 35% of both those in the program and the control group had been

arrested, but at 4 years, 69% of the experimentals and 75% of the controls had been

arrested. However, this difference was not statistically significant because of the

small sample sizes in this subgroup (Cave et al. 1993: 194). Thus, following the

mixed results of the financial assistance experiments of the 1970s, the federally-

sponsored employment demonstrations targeting disadvantaged young adults with

a criminal history, were found to be very disappointing.

Job Corps

Job Corps is a long-term residential program that emphasizes academic and

vocational preparation with some job placement assistance for a seriously

EX-OFFENDER EMPLOYMENT PROGRAMS AND RECIDIVISM: A META-ANALYSIS 303

disadvantaged population, primarily school dropouts. Funded by the U.S.

Department of Labor since 1964, Job Corps received $1.3 billion and enrolled

60,000 youth aged 16 to 24 in 1999. An evaluation conducted in 2000 used random

assignment on all applicants who applied to Job Corps between November 1994

and February 1996. The control group was not allowed to sign up for the program

for 3 years, but many did receive some type of training elsewhere, often vocational

training (Schochet et al. 2000). The evaluation examined self-reported arrests over

a 48-month period for a subgroup of 998 ex-offenders (defined as ever been

arrested) who were enrolled in the program as compared to ex-offenders in the

control group.

In the recent evaluation of Job Corps, Schochet et al (2001) found no

differences in self-reported arrests between Job Corps participants with prior

arrest records and controls. The difference in proportions rearrested was 1.3% for a

group with prior arrests for nonserious crimes and 4.7% for a group with serious

prior arrests (Schochet et al. 2001: Table F. 12). Additional data presented on

follow-up convictions also do not indicate any impact of the Job Corps program for

those with prior arrests (Schochet et al. 2001: Table F. 12). However, alcohol

consumption and hard drug use declined among Job Corps participants with a prior

nonserious arrest (Schochet et al. 2001: Table H. 4).

Opportunity to Succeed (OPTS)

The most recent study, the Opportunity to Succeed (OPTS) program, initiated in

1994, was a 3-year demonstration program designed to reduce substance abuse

relapse and criminal recidivism by providing comprehensive post-release services,

including job readiness classes, job training, and job placement to ex-prisoners

with alcohol and drug offense histories (Rossman et al. 1999). The program

operated in five communities but the evaluation was carried out in three: Kansas

City, MO, St. Louis, MO, and Tampa, FL. The evaluators randomly assigned 398

participants to treatment and control groups; services were available for up to 2

years for OPTS clients. Outcomes included both self-reports and official records.

Official criminal justice records of arrest and technical violations were obtained for

84% of the sample at the end of the first year of supervision or OPTS program

participation.

An evaluation of OPTS found that there was little substantive or statistical

difference between the participants in the program and the control group on self-

reported arrests (Rossman et al. 1999). Program clients reported committing fewer

robberies and engaging in less disorderly conduct than the controls, but these

differences are significant only at the 0.10 level (Rossman et al. 1999: Figure 6-2).

Analysis of official records found no differences in the two groups on number of

arrests, but the program participants did have a greater rate of technical violations

than the controls. The authors suggest that OPTS clients had greater contact with

case managers which may have resulted in increased detection of violations.

CHRISTY A. VISHER ET AL.304

Meta-analysis

Effect sizes for the eight studies were computed using inverse-variance

methods and followed the meta-analytic approach recommended by Lipsey

and Wilson (2001). Continuous outcome measures were preferred to dichoto-

mized outcomes wherever both were available. All effect sizes were coded so

that a positive effect size indicates the treatment group subjects experienced less

recidivism than the comparison group. We applied the formula recommended

by Hedges (1981) to adjust for upward bias in standardized mean difference

(SMD) effect sizes due to small sample sizes. This bias adjustment was trivial

for all studies as all of the effect sizes were based on samples of 200 or more

subjects. An arcsine transformation was applied to the effect sizes computed

from dichotomized outcome measures to make them comparable to the SMD

effect sizes.

All of the studies reported arrests during the follow-up period as an outcome

measure. Dichotomized arrest measures (i.e., the proportion of subjects who were

arrested) were reported for six of the eight studies. We applied an arcsine trans-

formation to these proportions and computed effect sizes as differences of pro-

portions. The remaining two studies (Rossman et al. 1999; Rossi et al. 1980)

reported a continuous recidivism measure (i.e., the mean number of arrests during

follow-up), and so SMD effect sizes were computed. The follow-up periods for

which we were able to code outcomes from the eight studies ranged from 6 to 48

months with a mode of 12 months.

Two of the studies (Mallar and Thornton 1978; Rossi et al. 1980) used crossed

designs involving multiple treatment groups, each of which received a different

intervention, being compared with a single comparison group. Separate effect sizes

computed for each treatment group would not have been statistically independent

because of the common comparison group. To keep the effect sizes independent,

we computed a weighted mean of the outcome measures for the multiple treatment

groups in each Fsub-study_ using the degrees of freedom in each treatment group (i.e., n j 1) as a weight. A single effect size was computed for each study using the

weighted mean outcome for the treatment group effect and the sum of the degrees

of freedom for the k treatment groups (i.e., n1 + n2 + . . . + nk j k) as the treatment

group sample size. In short, we used aggregation to avoid statistically dependent

effect sizes at the cost of the ability to examine the effects of the different

treatment modalities separately.

The TARP experiment (Rossi et al. 1980) was actually two simultaneous

studies, one in Texas and another in Georgia, using the same design. Four treat-

ment groups and one comparison group were created in each state, so we were able

to compute a single effect size for the Texas study and an independent effect size

for the Georgia study.

Besides the TARP experiment, the only study to contribute two effect sizes was

Uggen’s (2000) reanalysis of the National Supported Work Demonstration Project.

He split the sample into subjects 26 years of age and younger and those 27 and

older. This produced two independent treatment groups and two independent

EX-OFFENDER EMPLOYMENT PROGRAMS AND RECIDIVISM: A META-ANALYSIS 305

comparison groups. Consequently, we were able to compute two effect sizes,

bringing the total to 10 effect sizes for the eight studies.

To summarize, we formulated and applied three rules to reduce the set of coded

effect sizes to a group of 10 statistically independent effect sizes: (1) where studies

had reported the same outcome for the same subjects at multiple time points, we

used the average outcome measure across the time points to compute a single

effect size; (2) where studies reported both adjusted (for detected areas of initial

non-equivalence between the study groups) and unadjusted effect size information,

we used the adjusted estimates; and (3) where studies reported the same outcome

for differing groups of subjects at multiple time points (e.g., as a consequence of

subject attrition during the follow-up period), we used the effect size information

from the follow-up period nearest to 12 months, which was the modal follow-up

period for entire sample of effect sizes. The second and third of these rules were

applicable only to the handling of Anderson and Schumacker (1986), where effect

size data were reported after 6 months of follow-up and again after 12 months of

follow-up. 6

We computed the effect size for the Anderson and Schumacker (1996)

study using the 12-month effects and the 12-month sample sizes.

Results

The first stage of the analysis is summarized in Table 1. The mean of the 10 effect

sizes is 0.03, which is not statistically significant (z = 1.34; P = 0.1790). This

finding indicates that, on average, the employment interventions examined did not

reduce arrest among the treatment group subjects by more than the amount

Table 1. Mean effect size and heterogeneity test statistic, Q.

Study ES se

95% CI

LL UL

Bloom j 0.01 0.11 j 0.22 0.20

Cave 0.13 0.13 j 0.12 0.39

Schochet 0.03 0.04 j 0.05 0.11

Uggen (927) 0.20 0.06 0.08 0.33

Uggen (G27) j 0.03 0.04 j 0.12 0.06

Anderson 0.19 0.14 j 0.09 0.46

Mallar a

0.07 0.11 j 0.14 0.29

Rossi (TX) a

0.02 0.08 j 0.14 0.17

Rossi (GA) a

j 0.07 0.08 j 0.22 0.09

Rossman j 0.05 0.11 j 0.26 0.17

MEAN 0.03 0.02 0.01 0.07

Q 12.5, df = 9, P(9 Q) = 0.1871

a Effect sizes computed from the weighted mean outcome in multiple treatment groups contrasted with a

single comparison group.

CHRISTY A. VISHER ET AL.306

expected by chance. We also computed a Q statistic to test the null hypothesis that

the variance of the sample of 10 effect sizes could be accounted for by sampling

error alone. The value of Q is distributed as chi-square. Our test yielded a value of

13.45 (P = 0.1462; df = 9), which indicates that sampling error alone could explain

the effect size variance in our sample.

With only 10 effect sizes in the sample, this null finding was easy to explain.

Only one of the individual effect sizes, Uggen’s (2001) sample of older subjects,

was statistically significant (Figure 1). This effect was positive, indicating that

treatment subjects had a lower incidence of arrest than comparison subjects. Four

of the remaining nine effect sizes were negative and not significant, however.

To gauge the extent to which single effect sizes were driving our statistical

inferences, we re-estimated the mean effect size and Q statistic excluding each

study one at a time. Only when Uggen’s (2001) younger sample was excluded did

the remaining nine effect sizes yield a statistically significant (P 9 0.05) mean effect size (Table 2). The value of Q never reached statistical significance.

However, even this lone significant finding was tenuous. We found that it was

contingent on our handling of the effect size from the Anderson and Schumacker

(1986) study. In that study, the 6-month effect size was substantially smaller than

the 12-month effect size. If we had elected to use the 6-month effect size or to

average the two, there would have been no combination of nine effect sizes that

yielded a statistically significant mean.

We were also concerned that our initial inferences based on the model in

Table 1 might be sensitive to our choice of analytic approaches, so we tested an

alternative. We had outcome estimates in the form of proportions for all of the

studies. Using these dichotomized measures of recidivism, we computed 10 new

logged odds ratio (OR) effect sizes, a new inverse-variance weighted mean effect

size, and a new estimate of Q. This approach offered a greater degree of analytic

consistency than the earlier sample comprised of a mix of seven arcsine

transformed proportion differences and three SMD effect sizes. Two of the LOR

effect sizes, Rossi (TX) and Rossman, differed in sign from their SMD

Figure 1. SMD effect sizes, 95% confidence intervals, and inverse-variance weighted mean effect size.

EX-OFFENDER EMPLOYMENT PROGRAMS AND RECIDIVISM: A META-ANALYSIS 307

counterparts because these studies reported both the mean number arrests during

follow-up as well as the proportion of subjects arrested. In these cases, the LOR

and SMD effect sizes were based on different estimates.

The new mean effect size (0.06) was somewhat larger than the first (0.03), but

the standard error of the mean of the logged OR effect sizes was also larger (0.05

vs. 0.02) (Table 3, Figure 2). The basic inference, however, remained the same: On

average, these employment services interventions had no significant effect on the

Table 2. Sensitivity of mean effect size and Q to the exclusion of single effect sizes.

Excluded ES Mean ES se P(9 Mean ES)a

95% CI

Q P(9 Q)LL UL

Bloom 0.03 0.02 0.0805 j 0.01 0.08 13.20 0.1052

Cave 0.03 0.02 0.1168 j 0.02 0.07 12.76 0.1204

Schochet 0.03 0.03 0.1232 j 0.02 0.08 13.38 0.0994

Ugeen (9 27) 0.01 0.02 0.3942 j 0.04 0.05 5.07 0.7501 Uggen (G 27) 0.05 0.03 0.0244 0.00 0.10 10.83 0.2115

Anderson 0.03 0.02 0.1256 j 0.02 0.07 12.07 0.1481

Mallar b

0.03 0.02 0.1082 j 0.02 0.07 13.21 0.1048

Rossi (TX) b

0.03 0.02 0.0918 j 0.01 0.08 13.36 0.1000

Rossi (GA) b

0.04 0.02 0.0503 j 0.01 0.08 11.79 0.1608

Rossman 0.03 0.02 0.0723 j 0.01 0.08 12.89 0.1157

a P values are one-tailed.

b Effect sizes computed from the weighted mean outcome in multiple treatment groups contrasted with a

single comparison group.

Table 3. Mean effect size and heterogeneity test statistic, Q, computed from logged-odds ratios.

Study ES se

95% CI

LL UL

Bloom j 0.01 0.22 j 0.44 0.41

Cave 0.30 0.29 j 0.28 0.87

Schochet 0.06 0.08 j 0.11 0.22

Uggen (9 27) 0.42 0.13 0.16 0.68

Uggen (G 27) j 0.06 0.09 j 0.23 0.11

Anderson 0.54 0.36 j 0.17 1.26

Mallar a

0.13 0.22 j 0.31 0.58

Rossi (TX) a

j 0.07 0.16 j 0.39 0.25

Rossi (GA) a

j 0.04 0.16 j 0.35 0.27

Rossman 0.06 0.23 j 0.39 0.50

MEAN 0.06 0.05 j 0.03 0.15

Q 13.0, df = 9, P(9 Q) = 0.1631

a Effect sizes computed from the weighted mean outcome in multiple treatment groups contrasted with a

single comparison group.

CHRISTY A. VISHER ET AL.308

likelihood of arrest among ex-offenders. Furthermore, the Q statistic was not

significant in this sample of logged odds ratios indicating that it is plausible to

claim that all of the effect sizes were drawn from the same population. The

variance in this sample of effect sizes can be plausibly attributed to sampling error

alone.

We repeated our sensitivity analysis with the logged-odds ratios and found a

similar pattern. The only combination of nine logged-odds ratios to yield a

significant mean effect size excluded Uggen’s (2000) younger sample (Table 4).

The Q statistic was not significant for any combination of nine effect sizes.

We concluded that, on average, these eight employment services interventions

had no significant effect on the likelihood that the treatment subjects would be

Figure 2. LOR effect sizes, 95% confidence intervals, and inverse-variance weighted mean effect size.

Table 4. Sensitivity of logged OR mean effect size and Q to the exclusion of single effect sizes.

Excluded ES Mean ES se P(9 Mean ES)a

95% CI

Q P(9 Q)LL UL

Bloom 0.07 0.05 0.0737 j 0.02 0.16 12.86 0.1168

Cave 0.06 0.05 0.1032 j 0.03 0.15 12.34 0.1367

Schochet 0.07 0.05 0.1078 j 0.04 0.17 12.98 0.1125

Ugeen (9 27) 0.02 0.05 0.3675 j 0.08 0.11 4.71 0.7881

Uggen (G 27) 0.11 0.05 0.0201 0.00 0.21 10.28 0.2459

Anderson 0.06 0.05 0.1096 j 0.03 0.14 11.23 0.1890

Mallar b

0.06 0.05 0.0945 j 0.03 0.15 12.90 0.1153

Rossi (TX) b

0.07 0.05 0.0570 j 0.02 0.17 12.28 0.1391

Rossi (GA) b

0.07 0.05 0.0616 j 0.02 0.16 12.52 0.1295

Rossman 0.06 0.05 0.0838 j 0.03 0.15 12.99 0.1122

a P values are one-tailed.

b Effect sizes computed from the weighted mean outcome in multiple treatment groups contrasted with a

single comparison group.

EX-OFFENDER EMPLOYMENT PROGRAMS AND RECIDIVISM: A META-ANALYSIS 309

rearrested. With only 10 independent effect sizes, however, our statistical power

was, no doubt, modest. The possibility of Type II error cannot be discounted,

especially since our sensitivity analysis showed that we might have concluded that

these programs had a modest salutary effect but for the inclusion of the younger

sample from Uggen’s (2000) study. On the other hand, the largest mean effect size

obtained for any nine of the 10 effect sizes was 0.11, a rather small effect. The

evidence seemed to support a rather confident conclusion that the effect of the

employment services interventions on recidivism was either null or salutary and

quite small. 7

With this null finding and a non-significant heterogeneity test, we might have

concluded the analysis. However, we wanted to investigate explicitly the

possibility that the effect of the intervention was related to the significance of

the subjects’ prior criminal records. Five of the 10 effect sizes (Uggen, Schochet,

Bloom, and Cave) were contributed by studies that relied on samples of persons

who did not necessarily have a prior criminal conviction. The remaining five effect

sizes (Mallar, Rossi, Rossman, and Anderson) were contributed by studies of

persons with one or more convictions. The Mallar, Rossi, and Rossman studies

included only former prisoners; the Anderson study examined probationers. We

divided the effect sizes accordingly into two sub-samples, convicts and non-

convicts, and computed a new mean for each (Table 5). The results suggested that

the studies involving samples of less serious offenders (no recent convictions or

incarcerations) showed evidence of larger, but still not significant, effects.

Discussion

This systematic review reveals that knowledge about the effectiveness of non-

custodial employment services for ex-offenders is hampered by inadequate

contemporary research. Only eight studies using random assignment, dating back

to the early 1970s, could be identified in English-language publications. Moreover,

these studies are quite disparate in terms of primary intervention and target

population. Nonetheless, we concluded that, overall, the eight interventions had no

significant effect on the likelihood that participants would be rearrested. When the

Table 5. Sub-sample analysis by conviction status of the subjects.

Sub-sample Mean ES se P(9 Mean ES)a

95% CI

Q P(9 Q)LL UL

Convicts b

0.01 0.04 0.4272 j 0.08 0.09 3.14 0.5347

Non-convicts 0.04 0.03 0.0729 j 0.01 0.09 9.90 0.0421

a P values are one-tailed.

b Effect sizes computed from the weighted mean outcome in multiple treatment groups contrasted with a

single comparison group.

CHRISTY A. VISHER ET AL.310

studies were divided into two groups, based upon whether the target population

had a prior conviction or had only a prior arrest, the results did not change.

The original intent of this systematic review was to examine employment

services interventions for non-custodial offenders. Unfortunately, only one random

assignment study was located that was completed in the last 10 years with this

target population (Rossman et al. 1999). The lack of federal funding for ex-

offender employment programs in the 1980s appears to have created a gap in the

development and implementation of these programs, particularly for persons

leaving prison. Thus, rigorous evaluations of contemporary employment inter-

ventions for former prisoners are sorely needed. Although many such programs

operate in communities, evaluations of their effectiveness are rare and random

assignment designs have not been used (Finn 1998). In the course of this review,

several quasi-experimental studies of more recent community employment

programs were located (e.g., Finn and Willoughby 1996; Lattessa and Travis

1991; Menon et al. 1992; Turner and Petersilia 1996), but none report that the

programs significantly reduced recidivism. Thus, inclusion of these studies in a

broader meta-analysis appears unlikely to alter our conclusions.

In the 1990s, a new generation of community employment programs for ex-

offenders emerged. Programs such as the Safer Foundation in Chicago, Center for

Employment Opportunities in New York, and Project Rio in Texas are run by non-

profit organizations but work closely with the criminal justice system. These

employment programs are more intensive and are prepared to help clients with

basic life skills, job readiness, social support, job-placement assistance, and

continued support after a job is secured (Buck 2000; Finn 1998; Solomon et al.

2004). They also appear more focused on matching the needs of clients with

appropriate services than the government-funded community employment pro-

grams of the past. For many of these programs, rigorous, random assignment

evaluations are underway.

Stable, satisfying employment is a critical predictor of post-release success for

individuals released from prison. However, former prisoners typically have poor

work histories and a limited range of skills. These deficits, coupled with a recent

felony conviction and period of incarceration, often lead to difficulty finding and

keeping a job that will allow these individuals to provide financial support for

themselves, and for many of them, their families. Employment interventions can

include a range of services such as job-readiness classes, vocational education,

GED certification, job training, job placement, and job monitoring by a case

manager for some time period. Not all returning prisoners need all these services.

Many held legitimate jobs before incarceration and only need assistance in locating

an employer who would hire them, given their recent conviction and incarceration.

Others may never have held a full-time job with regular hours and need a full set of

services before entering the labor market. Community-employment programs may

be more effective with this population if the needs of individuals can be identified

and linked to specific services. Ideally, a new generation of evaluations would

provide some direction to policy-makers as to the most effective combination of

services for specific types of former prisoners.

EX-OFFENDER EMPLOYMENT PROGRAMS AND RECIDIVISM: A META-ANALYSIS 311

Acknowledgements

The authors would like to thank Vera Kachnowski, Erika Olsen, William Turner,

Jamie Watson, and Alyssa Whitby for their assistance with this project. Mark

Lipsey provided invaluable advice on calculating and interpreting effect sizes. In

addition, the authors are grateful for the advice and contributions of Shawn

Bushway and Christopher Uggen, whose work on employment and crime set the

context for this systematic review. The project was funded by the Smith-

Richardson Foundation and the Campbell Collaboration, Crime and Justice Group.

Notes

1 We permitted one exception to this criterion. The Job Corps study (Schochet et al. 2001)

used a study sample that included some 16-year-olds. 2 This discussion benefited greatly from the overview of many of these studies provided in

Uggen et al. (2002).

3 Only one of the two control groups in each study was interviewed in the same manner as

the treatment group. The second treatment group was followed through review of official

records only. We ignored the non-interviewed comparison groups when coding the TARP

studies because of this dissimilarity in data sources.

4 Participants in the LIFE program were told that they were entitled to partial benefits if

they worked. In fact, almost all participants received the full $780 in the first 13 weeks;

hence, in practice, participants did not encounter the Femployment tax_ that the TARP

participants faced (Mallar and Thornton 1978: fn. 3).

5 In Georgia, the arrest rates of the four experimental groups ranged from 48.4% to 49.9%,

compared to 48.4% or 48.7% in the two control groups (Rossi et al. 1980: Table 5.1). In

Texas, the arrest rates ranged from 34% to 42.5% for the experimentals, and 35.5% to

36.5% for the controls (Rossi et al. 1980: Table 5.2).

6 One of the 101 treatment group subjects dropped out of the sample between the 6- and 12-

month observations and none of the 103 comparison subjects were lost.

7 We also examined our results using a 0.10 alpha level and none of the inferences from our

analysis changed.

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About the authors

Christy A. Visher is Principal Research Associate with the Justice Policy Center at the

Urban Institute in Washington, D.C. Dr. Visher has 20 years of experience in policy research

on crime and justice issues. Her research interests focus on prisoner reentry, criminal

careers, communities and crime, and the evaluation of strategies for crime control and

prevention. Dr. Visher received her M.A. and Ph.D. in Sociology from Indiana University,

Bloomington.

Laura A. Winterfield is a Senior Research Associate with the Justice Policy Center at the

Urban Institute in Washington D.C. Dr. Winterfield has been actively involved in all aspects

of criminal justice research since the early 1970s, including courts, field services, alternatives

to incarceration, and offender treatment approaches. Her areas of expertise include etiology

of crime and delinquency, community corrections, the development of prediction models

for criminal justice decision-making, estimating the impacts of diversion programs on incar-

ceration, and evaluation research. She received her Ph.D. from the University of Colorado.

CHRISTY A. VISHER ET AL.314

Mark B. Coggeshall, M.A. (University of Maryland) is a research associate with the Justice Policy Center of the Urban Institute in Washington, D.C. His research interests include

school violence, gun control and gun violence, and program evaluation. His publications

have appeared in School Psychology International, Psychology in the Schools, Education

and Urban Society, and Corrections Management Quarterly.

EX-OFFENDER EMPLOYMENT PROGRAMS AND RECIDIVISM: A META-ANALYSIS 315

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