Systematic Review of Non-Custodial Employment Programs: Impact on Recidivism Rates of Ex-Offenders

Eligibility Criteria

Search Strategy for Study Identification

So that we did not rely on only published studies in highly visible academic journals, where the tendency is to report effectiveness, we used the following search modes: ■

Contacts with leading researchers;

The specific databases that were searched were: ■

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

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, aftercare, 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).

Selection of Studies

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 a focus on an evaluation report, no further review was initiated. For the 30-35 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.).

Upon examination of the studies, it became clear that there would not be sufficient random assignment studies involving former prisoners to conduct a formal meta-analysis. Thus, we expanded the selection criteria to include subjects with a previous arrest or conviction.

The total number of independent studies using random assignment designs that satisfied our revised eligibility criteria was eight, including two studies in which two separate 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 and Extraction

A Microsoft Access database was constructed for our meta-analysis, and information 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 (Bloom et al., 1994) 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).

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, Berk and Lenihan 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 short-term income support to released prisoners, coupled with job counseling and placement assistance, would speed an ex-prisoner's return to the labor force and, consequently, reduce the likelihood of criminal activity (especially, property crimes used to gain income).

Beginning in 1971, 432 prisoners released from Maryland state prisons and returning to Baltimore were randomly assigned to receive 13 weeks of payments of $60 per week and/or intensive job counseling and placement services or placed in a control group that received no payments or 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 history (see Mallar and Thornton 1978:210-211). Recidivism was measured as any new arrest at one year.

The LIFE experiment found that the job placement and counseling intervention had no impact on arrests in the first year, but 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, the fewest arrests (for theft) occurred for those study participants who only received financial assistance with no job placement services. Uggen and his colleagues (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 (see also Lenihan 1976).

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 4000 ex-prisoners participated in two studies (one in each state) with random assignment into four experimental and two control groups in each study (Rossi, Berk, and Lenihan 1980; Berk, Lenihan, and Rossi 1980).6 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, and for those who received the 13 weeks of benefits, either 100 or 25 percent tax rate on earnings could be received. Computerized arrest records in each state were examined one 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).7 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.8 The financial payments actually reduced the number of weeks worked, although ex-offenders who received payments did get better jobs, and those who were employed had fewer arrests. However, the employment services component in both the LIFE and TARP experiments had no effect 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 arrested, convicted, or incarcerated, were currently unemployed and had been employed for no more than three of the preceding six months between 1975 and 1977 (Piliavin and Gartner 1981; Uggen 2000). Study participants were randomly assigned to either minimum-wage jobs in crews with 6-8 other workers or a control group. In a reanalysis of the original data, Uggen (2000) examined first self-reported arrest for two theoretically important subgroups: those under age 26 and those aged 26 and older. The combined sample size was 3105 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 one year, 31 percent 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), documenting the significance of age of participant in the success of employment services interventions, 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, 108 probationers enrolled in a job training program during the years 1979, 1980, and 1981 were compared to a random sample of 108 community probationers (Anderson and Schumacker 1986). Program participants 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 six and twelve months.

Anderson and Schumacker (1986) found no differences in six and twelve month outcomes in their evaluation of the job training program for probationers. At six months, 15 percent of the control group and 13.5 percent of the treatment group had “difficult” outcomes, defined as probation revocation, or new conviction resulting in a jail or prison sentence. At twelve 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 typically included basic education and “miscellaneous 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 17-21) with previous arrest records. During the first follow-up period (at 21 months, on average), 43 percent of both the treatment and control group had been arrested. At the second follow-up (at 36 months, on average), 59 percent of the youth in JTPA were arrested, compared to 56 percent 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 17-21 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 one and four 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 four years. At the end of one year, 35 percent of both those in the program and the control group had been arrested, but at four years, 69 percent of the experimentals and 75 percent 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, 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 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 three 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 and his colleagues (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 percent for a group with prior arrests for nonserious crimes and 4.7 percent 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 three-year demonstration program designed to reduce substance use 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 two 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 percent 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 .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.

Summary

These eight studies find little or only modest effects of employment services programs for reducing the recidivism of ex-offenders. In several of the studies, the experimental subjects did have better outcomes than the control subjects but the differences were not statistically significant. Unfortunately, these random assignment studies of employment services programs for ex-offenders are dissimilar in many respects. First, these eight studies span almost

25 years. Second, the employment services interventions tested in these studies vary widely, from job readiness programs (including basic education) and intensive vocational training to job placement assistance to work crew assignments. Third, the participants in these studies range in age from older youth (16-17 years) to those in their 40s. Fourth, the prior criminal histories of the participants vary from an arrest for a nonserious crime to a recent incarceration for a serious offense. Special analyses of two of the studies by Uggen did find that older participants (at least 26 years) were much less likely to be arrested than younger participants. However, the interventions in these two studies were quite different – financial incentives and work crew assignment.

Such a heterogenous group of studies is not ideal for a meta-analysis, although with a larger number of studies, characteristics of the studies themselves (i.e., type of program, age of participant) could be taken into account in a multivariate analysis. However, an N of eight studies precludes such an analysis. Nonetheless, we proceeded with the meta-analysis because over 6,000 subjects with a history of criminal justice involvement had participated in these employment services interventions, the studies had not been previously subjected to a quantitative meta-analysis, and we wanted to establish a baseline for future systematic reviews of this literature when additional studies become available.

Results

The first stage of the analysis is summarized in Table 1. We 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 = .1462; df = 9), which indicates that subject-level sampling error alone could explain the effect size variance in our sample. We proceeded with the analysis based on fixed-effects assumptions, most notably that all 10 effect sizes were drawn from the same population. We based this decision on the fact that our eligibility criteria imposed a high degree of methodological and subject-area uniformity on the studies. In addition, the P-value of the Q statistic was greater than .10 and was based on 10 effect sizes based on relatively large samples ranging in size from 203 to 2,125 subjects.

The mean of the 10 effect sizes is 0.03, which is not statistically significant (z = 1.34; P = .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 expected by chance.

To provide context for the mean effect size, we computed mean proportion of comparison subjects who were not arrested during the follow-up period for the seven comparison groups where that proportion was available (i.e., those to which we applied arcsine transformation in computing the effect size). We found that, on average, 54.3% of the comparison subjects were not arrested during the follow-up period, and the standard deviation of this proportion was 49.1%. If we expect 54.3% of the comparison subjects to not be arrested and the mean effect size of the employment interventions on arrest is 0.03, then we would expect an average of [54.3% + (0.03 * 49.1%)] 55.8% of treatment subjects to not be arrested.

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.

OPEN IN VIEWER

1

SMD Effect Sizes, 95% Confidence Intervals, and Inverse-Variance Weighted Mean Effect Size

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 > .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 (1996) 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 counterparts because these studies reported both the mean number of 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 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. Once again, we proceeded under fixed-effects assumptions.

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 (.05 vs. .02) (Table 3, Figure 2). The basic inference, however, remained the same: On average, these employment services interventions had no significant effect on the likelihood of arrest among ex-offenders.

OPEN IN VIEWER

2

LOR Effect Sizes, 95% Confidence Intervals, and Inverse-Variance Weighted Mean Effect Size

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 (2001) 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 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 (2001) study. On the other hand, the largest mean effect size obtained for any nine of the 10 effect sizes was .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.

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 and the timing of the intervention (upon release from prison or shortly after sanction). 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.

Implications for Research

This systematic review reveals that our ability to make definitive conclusions about the effectiveness of non-custodial employment services for ex-offenders is hampered by inadequate research. Only eight studies that use random assignment could be identified in English-language publications, and these date back to the early 1970s. 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 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.

We found that, on average, 54.3 percent of the comparison subjects were not arrested during the one-year follow-up period. Given a mean effect size of the employment interventions on arrest of 0.03 and taking into account the variation in the individual studies, we would expect an average of 55.8 percent of treatment subjects to not be arrested.

The original intent of this systematic review was to examine employment services interventions for formerly incarcerated individuals who had been recently released to the community. Unfortunately, only one study was completed in the last ten years with that specific target population (Rossman et al. 1999). Thus, contemporary studies of employment services interventions 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.

As part of our search for appropriate studies for this meta-analysis, we did discover a number of studies that used quasi-experimental designs (i.e., see Buck 2000; Finn 1998a; Finn 1998b; Finn 1999; Menon, et al 1992; Martin, et al. 1999; Soothill 1974; Soothill, Francis, and Ackerly 1997; Turner and Petersilia 1996; Virginia Department of Corrections 1985, as discussed in Buck 2000). Some of the employment services interventions tested in these studies appear promising, although most of the treatment groups in these studies suffer from the problem of offender self-selection into the intervention, which likely renders the comparison group at higher risk for failure.

The quasi-experimental set of studies is representative of a new generation of employment services programs for ex-offenders. In an effort to move beyond the generic ‘employment program’ and consider aspects of such programs that may be specifically efficacious for former prisoners (as opposed to disadvantaged young adults), it is useful to examine these ‘new’ programs and consider the differences in organizational and programmatic structure.

Most of the quasi-experimental studies focus on programs that have been specifically designed for recently released prisoners. Elements of these programs include traditional work release, transitional employment in the community, pre-employment services (basic education, life skills, substance use and mental health counseling), job readiness training (resume preparation, interviewing, job search skills), job placement assistance, and post-employment support. In addition, some programs begin providing services before release from prison and continue services after release. Programs also differ on their role as a community intermediary (see Solomon et al., 2004) between the former prisoner and the business community.

The more comprehensive programs appear to have incorporated knowledge about the multiple challenges former prisoners face as they are released (see Petersilia, 2003; Travis et al., 2001) and have been designed to be programs that are not purely “employment services.” It is hard to argue with a conceptual philosophy that focuses initially on basic needs and skills (i.e., housing, sobriety, education) before offering employment services. On the other hand, transitional employment programs that immediately assign former prisoners to day labor and work crews were one of the interventions found effective in the 1970s, at least for older offenders. The cornerstone of the Center for Employment Opportunities in New York, which has been in operation for over twenty years, is immediate transitional employment, although the program also provides some pre-employment services and job readiness training.

Thus, the new generation of employment services programs for ex-offenders relies on several different models and types of service delivery. Moreover, many programs bundle several of these different types of interventions – for example, combining pre-employment services with job placement assistance. Future evaluations are likely to find it difficult to isolate the independent effect of these intervention components. Among the highest priority for rigorous research and evaluation are examinations of the effectiveness of transitional employment, continuity of services from in prison to after release, continued support/services after job placement, and traditional work release programs.

This systematic review also points to the need for an examination of age of the subject as an important correlate of the effectiveness of employment services for ex-offenders. Two studies implemented in the 1970s show stronger effects for older ex-offenders, those at least 26 years old. However, these findings have not been replicated for more contemporary programs. Moreover, age may simply be a proxy for motivation. By virtue of their frequent experiences with the criminal justice system, older offenders may be more motivated to take full advantage of employment services programs in an effort to desist altogether from criminal activity.

Thus, our knowledge about the effectiveness of contemporary employment services programs for former prisoners, or even ex-offenders in general, is extremely limited. A number of random assignment evaluations of various programs supported by the Department of Labor in the U.S. are underway, but results are not expected for several years. In the meantime, a useful next step would be to canvass research in other countries to determine whether rigorous evaluations of employment services programs for ex-offenders have been conducted.

Implications for Practice

Stable employment is a critical predictor of post-release success for individuals released from prison. However, employment programs may only be effective for motivated individuals and standard employment programs are unlikely to change motivation. Steady, satisfying employment can provide a way to new social networks and a conventional lifestyle and thus be a critical component in the desistance process (Bushway, 2003; Laub and Sampson 2003; Sampson and Laub 1993).

Nonetheless, former prisoners and other ex-offenders typically have poor work histories and a limited range of skills. These deficits, coupled with a recent felony conviction and possible 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. Moreover, ex-offenders may have other needs that preclude immediate employment, including serious educational deficits, substance abuse, mental illness, and a lack of affordable or stable housing. In most cases, these issues will need to be addressed before an individual is deemed job-ready.

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 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 pre-employment and job readiness services before entering the labor market. Employment programs may be more effective with this population if the needs of individuals can be identified and linked to specific types of services. Ideally, a new generation of evaluations would provide some direction to policymakers as to the most effective combination of services for specific types of former prisoners.

The challenges for practitioners are many. Buck (2000) interviewed service providers and policymakers for her review of employment programs for ex-offenders and identified critical components of their work that need strengthening, including improving the continuity of services between program activities inside and outside of prison, moving ex-offenders beyond entry-level jobs by offering occupational skills training and GED classes, and better communication among service providers to provide opportunities to learn from one another. In addition, limited public resources for these programs hampers the number of ex-offenders who can benefit. Waiting lists are common for programs in prison and in the community. Finally, practitioners agree that the dearth of knowledge about what makes an employment services program effective inhibits their ability to substantially improve the long-term employment rate of ex-offenders.

It is hoped that the results of the random assignment evaluations currently underway will provide better information to policymakers and practitioners who are working with ex-offenders.