Restorative Justice Conferencing (RJC) Using Face-to-Face Meetings of Offenders and Victims: Effects on Offender Recidivism and Victim Satisfaction. A Systematic Review

1.1 DEFINITION OF RJC

Our definition of an RJC is this: a planned and scheduled face-to-face conference in which a trained facilitator “brings together offenders, their victims, and their respective kin and communities, in order to decide what the offender should do to repair the harm that a crime has caused” (Sherman and Strang, 2012: 216). This definition covers a homogenous group of programs inspired by the work of the Australian theorist John Braithwaite (1989) and the Australian trainer John McDonald, whose dialogue spread both the idea of RJCs and the opportunity for rigorous evaluations of them from Canberra to the US and UK from 1995 through 2005. Other training organizations have taught a similar method in English-speaking countries, emphasizing the following procedures to be followed by facilitators—most often police—trained to organize and convene an RJC that could last from 60 to 180 minutes or more: •

Facilitative discussion one-on-one with offenders and victims about what an RJC is, how it works, and whether they would consent to participate in one

This procedure has been used both in and out of criminal justice contexts, but all of the strong evidence of its effectiveness has been generated by comparisons to conventional criminal justice. These comparisons have been made with both juvenile and adult offenders who have accepted responsibility for their crimes in a wide range of offense categories, including burglary, serious assaults, vehicle theft, robbery and arson, at several points in the criminal process (Sherman and Strang, 2007, 2012): a)

As post-arrest diversion from, and a substitute for, prosecution in court

1.2 THEORETICAL BASIS

RJ Conferencing has strong theoretical connections to Braithwaite's theory of reintegrative shaming (1989), Tyler's theory of procedural justice (1990; Tyler and Huo, 2002), Sherman's theory of defiance (1993), Braithwaite's theory of responsive regulation (2002), and Collins' (2004) theory of interaction ritual chains. There is no causal theory that fully describes the manner in which conferencing might affect repeat offending and victims' satisfaction (see, e.g., Ahmed, et al, 2001).

Perhaps the closest theory to the predicted win-win effects of RJCs on offenders and victims is found in Collins (2004), whose theory is itself based partly on evaluations of RJCs. Using Durkheim's (1912) concept of “collective effervescence,” Collins develops a causal model around the intense emotions of events like a RJC. Durkheim's concept denotes that the energy produced by a gathering of people changes their behavior in the aftermath of the gathering, as in a religious service that reaffirms a commitment to obey certain moral imperatives. Rossner (2011) provides some evidence that supports Collins' theory, but no tests have yet compared competing or complementary theories of why RJCs can affect offending behavior and victim outcomes.

Collins' theory also provides the basis for limiting the present review to crimes in which an identifiable person has been harmed as a victim. RJCs have been tested on both the “victimless” crime of driving with blood alcohol levels over prescribed limits, and on the crime of shoplifting against corporate victims (Sherman and Strang, 2012). In neither test did the offender confront anyone with whose suffering they could empathize, suffering which the offender had personally caused. While we have reported the results of these tests elsewhere (Sherman and Strang 2012), we exclude them from the present review on the theoretical grounds that they do not share the fundamental bio-psychological conditions of an RJC with cases in which a harmed person faces an offender (Sherman and Strang, 2011). This decision has no effect on the conclusions reached below (since the two excluded studies reach opposite conclusions with each other about RJC effects), but it does set a theoretically sound basis for the future addition of new studies to updates of this review. The best interpretation of the available evidence to date on RJCs is that the evidence offers an assessment of a policy rather than a theory. This conclusion is especially warranted by the wide range of delivered treatments in the wake of random assignment. In medical terms, the available evidence includes virtually no efficacy trials, under controlled conditions, guaranteeing high levels of delivery of the program elements described above. Rather, the available evidence reports what are best described as effectiveness trials under real-world conditions. Future research that creates greater consistency of delivery of RJC elements may yield different, and possibly stronger, effect sizes than those reported in this review.

3.1 CRIT ERIA F OR CONSID ERIN G STUDIES FOR THIS REVIEW

This review of the effects of RJCs was limited to studies that had all eight of the following characteristics: 1)

Study was reported in the English language.

These criteria are justified below. As Braithwaite (1998, 2002) suggests, the restorative justice label embraces a wide range of similar programs that have very different dynamics. These differences could create heterogeneity in the program content that would limit the face validity of our systematic review. A leading example is Victim-Offender Mediation (VOM) programs. VOM is more structured than conferencing, and mediators play a much more prominent (and more negotiator-like) role in controlling the discussion in VOM than conference facilitators play in RJCs. While supporters are sometimes involved, VOM may consist only of the victim, the offender, and the mediator. In VOM, the mediator negotiates between the two parties; the victim and the offender may never meet face to face. The primary focus of VOM is often material restitution rather than emotional restoration or reconciliation (Umbreit et al, 1994). For similar reasons, the eligibility criteria for this review excludes Victim-Offender Reconciliation Programs (VORP) (Peachey, 1989) and ‘circle sentencing,‘ in which a judge talks to stakeholders about the appropriate penalty for a crime before formally imposing a sentence (Stuart 1996).

Random assignment generally provides the best means for eliminating selection bias, as well as other rival hypotheses, in assessing the effects of a policy (Cook and Campbell, 1979). Non-random comparison groups are abundant in restorative justice evaluations (McCold, 1998; Miers, et al, 2001), but are arguably plagued by biased selection of cases that were deemed more “appropriate” for RJCs than cases to which they were compared—either historical or matched controls, including some studies in which those who refused RJC were compared to those who agreed.

The requirement for identifiable victims is justified by the very different dynamics observed in RJCs with and without a victim present. Qualitative evidence indicates far lower levels of emotional intensity and offender remorse in cases without personal victims than in cases where personal victims are engaged (see also quantitative observational data in Strang, et al, 1999). In terms of interaction ritual chain theory (Collins, 2004), the level of collective effervescence in the conference appears far lower in RJCs without a personal victim: conference length appears much shorter, tears appear less often. Victimless conferences may also be less traumatizing for the offender than the description provided by Peter Woolf (2007), a high-frequency burglar who suffered nightmares and racing thoughts for years after a long RJC where two of his victims vehemently expressed their anger.

The issue of consent prior to random assignment shapes a decision made to exclude two experiments conducted in Bethlehem, Pennsylvania (McCold and Wachtel, 1998), in which over half of the cases randomly assigned to RJC failed to comply with the treatment as assigned. The high refusal rate followed the use of a procedure in which consent was sought after random assignment rather than before. This decision not only adversely affected the internal validity of the test. It also affected the external validity of the test to cases in which participants agree to attend an RJC. Because random assignment preceded the agreement, the population randomly assigned did not match the target population to which the study could be generalized. This review is limited to studies that define the target population as an eligibility criterion prior to random assignment.

The decision to use frequency of subsequent recidivism as the outcome for offenders is driven by both policy and pragmatism. The policy issue is whether a measure of prevalence of future offending is a reliable indicator of public benefit without taking frequency into account. Since total harm to the public corresponds more closely to the number of crimes committed than to the number of active criminals committing those crimes, the review chooses the former. It thus provides a clearer guide to policy by preferring frequency counts over the “one or more crimes” measure of proportion of offenders re-offending.

As a matter of pragmatism, frequency of convictions is also a more statistically powerful and less confusing way to measure impact in small samples. It thereby reduces bias due to low power, and the potential confusion that underpowered tests may cause to policymakers. Shapland et al's (2008: 27) meta-analysis of the seven UK experiments in RJC, for example, shows consistent benefits of restorative justice using both prevalence and frequency measures, both of which have similar effect sizes. Yet because of its lower power levels, the prevalence analysis fails to achieve statistical significance in meta-analysis. Shapland et al's (2008: 27, Figure 2.6) frequency analysis, in contrast, shows significance levels well within conventional thresholds (p= .013), again with the same effect sizes as in the prevalence analysis. Yet the authors have repeatedly encountered confusion among UK policymakers about the meaning of prevalence vs. frequency, and a reluctance to make policy based on “mixed” results. This review chooses to clarify the findings by use of the single measure (Piantadosi, 1997: 128) that the authors recommended from the outset of the first trials of RJC: frequency of offending (see Sherman et al, 2000).

The preference for convictions where available is also pragmatic, since 7 of the 10 experiments eligible for this review reported on no other measure of repeat offending. Only one of ten experiments (McGarrell and Hipple, 2007) reported no data on convictions, using arrests as the only repeat offending measure. Given the juvenile status of the offenders in that one exception, this may be a distinction without a difference as data on juvenile arrests in Indiana appear to be recorded on a similar basis as juvenile convictions are reported in the UK data. A similar pragmatic criterion limited the outcomes to post-treatment differences only, which is all that was reported for 8 of the 10 eligible experiments.

The two-year window of outcome assessment for offending effects is selected in accord with the recommendations of the Coalition for Evidence-Based Policy, the National Research Council, and the Office of Management and Budget, all in the United States.

Finally, the use of an intention-to-treat (ITT) criterion is, in the authors' view, essential for this review. It is only by using ITT that we can meet our objective of testing a policy of attempting RJCs, not just the effects of completing RJCs. Given the costs inherent in each attempt, it is far more policy-relevant to the public interest to understand the overall benefit of attempting to deliver RJCs in relation to the total cost of the attempts—including both successes and failures.

3.2 SEARCH STRATEGY FOR IDENTIFICATION OF STUDIES

The authors searched reference lists, contacted other authors, conducted electronic searches, and examined all reports related to restorative justice in the program of the American Society of Criminology from 1997 to 2012. Published and unpublished studies were considered. While some databases were restricted to particular periods of time, electronic searches were not otherwise limited by date. Indexes were searched in which non-English publications were expected to appear, but only reports written in English were considered for the review.

In 2012, one author electronically searched 15 databases related to criminal justice, law, and related areas of social science. The most common search was applied to databases indexed by Cambridge Scientific Abstracts; these databases were searched using the following terms: ((restorative AND (justice OR sentenc*)) OR (mediate OR mediation OR restitution OR conferencing) AND ((criminal OR offender OR perpetrator) AND victim))) AND (reoffend* OR recidiv* OR victim) AND (ab=random* OR ab=controll*). All databases searched and the particular terms used to search each database are listed in Table 1.

3.3 SELECTION OF STUDIES

One author checked titles and abstracts to identify studies that could be excluded based on information provided in the title or abstract. When a study could not be excluded based on that information, more information was obtained by retrieving the article or by contacting the authors.

The search identified articles in languages other than English. The authors are not aware of any completed or ongoing RCTs that have not been reported in English, but the authors are unable to conclude that none would be identified by combing these articles or by conducting a broader search.

Two authors extracted information from the full text of articles when published reports were available. Other information was obtained directly from investigators, including the authors and their colleagues in the primary studies.

Given the decision to limit eligible studies to RCTs, which were small in number, the studies were not compiled in a coded format.

3.4 DATA MANAGEMENT AND EXTRACTION

Data on repeat offending and on victim impact were extracted from each of the completed studies. Where this information was missing from the published reports, the reviewers requested it directly from the original investigators.

3.5 OUTCOME MEASURES

The authors would have preferred the use of before treatment-after treatment frequency analysis as the most logically sound test of intervention effects on recidivism. Pragmatically, however, only two studies offered before-and-after frequency analysis, while ten of them offered only post-treatment frequency measures. To examine outcomes from the maximum number of experiments, the authors decided to employ the “highest common denominator” allowing comparative analyses of effect sizes: two-year post-treatment differences in the frequency of criminal convictions per offender for nine of the studies, and of arrest in Indianapolis.

3.6 EFFECT SIZE ESTIMATES AND MODERATOR ANALYSES

The reviewers used Comprehensive Meta-Analysis v.2 (Borenstein et al, 2005) to analyze frequency of conviction with the standardized mean difference (Cohen's d). Outcomes were meta-analyzed using traditional inverse-variance weighted meta-analysis. In all cases, a random effects model was assumed a priori. The Q-test was used to measure for heterogeneity across effect sizes.

Samples of criminal cases may vary on many dimensions, each of which poses a challenge in a systematic review that integrates the findings of diverse tests. Examining the effects of RJCs across a wide range of offenses and offender types is not unlike examining the effects of aspirin across a wide range of diseases, including cancer, heart disease, influenza, sunburn, and syphilis. Further, the character of RJ conferences may change in relation to the populations and problems studied. There is no a priori reason to expect any intervention to be equally or consistently effective across all conditions, particularly when the intervention is an interaction among people rather than a drug. The reviewers attempt to avoid generalizations about included studies that would mislead readers about the effects of conferencing under tightly defined specific conditions.

Studies of conferencing vary in several ways, including offender age, offense type, location in the criminal justice process, type of comparison interventions, measures of dependent variables, period of follow-up, and percentage of cases in which the intervention is delivered as assigned. Some of these differences may also be related. With a small universe of eligible studies, the best we can do is to present moderator analyses in a variety of ways.

4.1 DESCRIPTION OF STUDIES

In all, 15 RCTs and one study that appeared to be an RCT were considered for the review. Six were excluded and ten remained (See Appendix A for rationale for exclusions). The eligible studies we included covered five jurisdictions on three continents, across a range of decision points in the criminal justice system, with a total of 734 interviewed victims and 1,879 offenders accepting responsibility for their crimes. The main characteristics of each experiment are described in Table 2.

4.2 ASSESSMENT OF METHODOLOGICAL QUALITY OF INCLUDED STUDIES

4.3 META-ANALYSIS OF REPEAT OFFENDING

The primary criterion of the effect of RJC on crime is the frequency of repeat offending over the two years after random assignment. In the meta-analyses presented below, the post-treatment measure of repeat offending is criminal convictions in all tests except Indianapolis, for which the measure is repeat arrests. We first calculated the odds ratios (OR) for the outcomes and then converted these OR into standardized differences of means (d) using the logit method.

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Effects of RJC on Frequency of Repeat Offending, 2-year Follow-Up Period

Figure 1 below shows that the average effect of RJC is to reduce crime. More precisely, across 1,879 offenders in all 10 eligible experiments, the average effect size is .155 standard deviations less repeat offending among the offenders in cases randomly assigned to RJC than among the offenders in cases assigned not to have an RJC. The 95% confidence interval for this effect lies between only .06 standard deviations less crime and .25 standard deviations less crime. This means that the average effect across all these experiments is highly unlikely to be a chance finding (d = .155, p =.001).

Put another way, only one out of the ten experiments shows a statistically significant effect,–but 9 out of 10 of the experiments show less crime with RJCs than without them. Either of those calculations alone could be misleading. But when the average effect size across all ten studies is calculated—including one in which there was more crime with RJCs (but not significantly more)—the pattern of findings can be described as statistically “significant” and favoring the benefits of RJCs. That means, in this case, that there is only a one in a thousand chance that the pattern in Figure 1 could have occurred by chance.

What is difficult to convey about these findings is how many crimes were prevented, or how big the effect of RJCs is likely to be in practical terms. The percentage differences associated with the ten experiments range from 7% to 45% fewer repeat convictions or arrests. This may help practitioners to grasp how much crime that would mean with the kind of offenders they might consider using RJCs with. But an even better way to judge the practical value of these differences is to use the cost-of-crime prevented data presented in section 5 below.

4.4 MODERATOR ANALYSES

The overall meta-analysis of the ten experiments can be unpacked to learn whether RJCs work better with some kinds of samples, or in some kinds of experiments, than others. These different ways of sorting the experiments are called “moderator analyses,” because they can reveal whether some third factor is “moderating” or changing the findings. By “third factors” in this review we mean the age of the offenders, or the kinds of offenses they were arrested for. That could suggest, for example, that if RJCs were used with only the kinds of cases associated with a third factor, it would get much better or worse results than the average effects across all ten experiments. Because the ten experiments vary widely in the third factors they represent, it is important to probe whether the overall average is being driven up or down by one or more of those factors. That is the purpose of presenting Figures 2-3 below.

Half of the experiments in the sample, for example, tested RJCs with violent crimes. Figure 2 shows what the average effect of RJCs is on just violent crimes. (Two others had a mix of violent and property crimes: Indianapolis and Northumbria Final Warning). The average effect of RJC for experiments limited to violent crimes was .2 standard deviations. That is an effect size that is 28% larger than the effect of RJC for all ten experiments. This means that, on average, RJCs appear to work better for violent crimes than for all crime types in these ten experiments combined, but because that difference is not statistically significant (Q = 1.021, P= .9) it must be treated with caution. Three of the other five experiments used samples of property crimes only. Figure 2 shows that RJCs have far less effect, on average, in these property crime experiments than in the violent crime experiments. The average effect appears to be very close to zero. This result could have been different with a different set of property crimes or offenders, and it is hard to generalize on the basis of just three experiments. Nonetheless, there seems to be something very different about the impact of RJCs for property crime than for violent crime.

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Crime Type as Moderator of Study Outcomes

Many public officials say that RJCs are more appropriate for juvenile offenders than for adults. Yet the findings from this Review suggest otherwise, at least for offenses with personal victims. In Figure 2 we see that the average effect of RJCs in six experiments with all adults is .150 standard deviations. Yet as shown in the Figure, we see that the average effect of RJCs on experiments with juveniles is only .119. The difference in effect size between adult and juvenile offenders is not large. But it is nonetheless in the opposite direction from the conventional wisdom.

One of the major policy debates in restorative justice is whether it should merely supplement conventional justice (CJ), or replace it altogether. In Figure 3 we see that the average effect of RJCs is larger in the 8 experiments when it is used as a supplement to conventional justice than for the average effect for all ten experiments (.19 vs. .15), but this difference is not statistically significant (Q = 0.447, P =0.50). Thus while the average effect for using it as a substitute may appear to be lower, the broad range of effect sizes in the two tests of RJC as a substitute leaves us too uncertain about its average effect. Put another way, both the worst and second-best results in the entire sample are found in the substitutional category. How much lower the effect of using RJCs as a diversion from conventional justice can, somewhat, be shown from the two studies. The moderator analysis in Figure 3 shows that on average, the two experiments in Canberra with personal victims had almost no effect (.001 standard deviations difference) on the frequency of repeat offending. It also shows that the individual studies went in opposite directions, canceling each other out. Moreover, the effect of the diversion of violent crimes to RJCs was .279 standard deviations, one of the largest benefits in the entire meta-analysis. Based on these two studies alone, there may still be potential for using RJC as a diversion rather than as a supplement. More research will be needed for a reliable comparison of substitutional and supplemental uses of RJCs.

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Effects of RJC as Supplement or Substitute to Conventional Justice on Frequency of Repeat Offending, 2-year Follow-Up Period

4.5 SENSITIVITY ANALYSES

In this section, we report a series of tests for whether the results presented above are “sensitive” to the inclusion or exclusion of certain kinds of tests, which may reflect certain kinds of biases that could in turn limit the generalizability of the results. The points we examine are the the effects of the authors as evaluators, the effects of using arrests (in Indianapolis) in a meta-analysis that uses convictions in all nine other experiments, and the effect of excluding from the sample offenders who had no time at risk to re-offend because they were in prison for the entire follow-up period of two years after random assignment (or treatment).

4.5.2 Arrests vs. Convictions.

Figure 4 addresses the question of whether the results of this review are sensitive to the use of arrests in one experiment, while the others report convictions. It displays the effect of 9 experiments, omitting the Indianapolis study—which accounted for over one-third of all the offenders in the review. The effect or removing Indianapolis is to reduce the effect size of RJC somewhat, but not to change the direction or the statistical significance of the result. Compared to the effect for all ten experiments (.15), the effect size of .12 without Indianapolis is close enough to conclude that the result is not sensitive to any aspect of including or excluding this study from the meta-analysis.

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Effects of RJC on the Frequency of Criminal Convictions, 2-year Post-treatment Follow-up Period

4.5.3 Time at Risk.

As noted above at 4.2.3, two of the ten studies - the London burglary and robbery pre-sentence experiments - used a procedure that included all offenders who were out of prison for any period of time during the two years after date of random assignment, from one day to two years minus one day, without controlling for variation in time at risk (Shapland, et al, 2008). They did, however, have reported effect sizes based on the evaluators' decision to delete any cases in which the offender was incarcerated for the entire two-year followup period. We elected to include these studies because the result of doing so was apparently to reduce the overall mean effect size of the ten available tests. Because we could not make any secondary attempts to standardize repeat conviction (or arrest) rates by days at risk (out of prison) within the two-year followup, the only choice was between inclusion or exclusion of these two London experiments evaluated by Shapland et al (2008). Figure 5 shows that the mean effect size of RJC on repeat offending when these two London studies are removed, so that all studies consistently have no deletions for any reduced level of time at risk. The standardized mean difference across only the eight studies was D = .165, or slightly higher than the mean effect for all ten studies (see Figure 1). This difference was due to a lower effect size of adding RJ to criminal sentencing in the two London experiments than in the two Thames Valley experiments, which were confined to assault cases but also had very serious injuries. Figure 6 shows that the mean effect size for the two studies that deleted randomly assigned cases in which offenders spent the entire two-year followup period in custodial punishment was only .08, or far lower than the overall mean. This does not indicate that the results of RJC for robbery and burglary cases are necessarily less effective. It could simply mean that more time is needed to examine the impact of RJC in such serious cases. More years of followup could provide more time for offenders to re-offend (or not), potentially even showing bigger effects on the cost of crime than found in experiments with less serious instant offenses. The point is that we simply cannot tell what the long-term effects would be without further followup.

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Effects of RJC on the Frequency of Repeat Offending (Without Deletions for Time at Risk), 2-year Post-treatment Follow-up Period

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Effects of RJC on the Frequency of Repeat Offending (With Deletions for No Time at Risk), 2-year Post-treatment Follow-up Period

Lest it appear that the smaller effect sizes may be due to less time in prison in the RJC group than in the conventional justice group, we can cite a separate study conducted by Strang, Barnes, Sherman, Bennett and Inkpen (2005), which found no significant differences between the RJC and conventional justice groups in the London experiments in either the prevalence of sentences to time in prison or the mean number of days sentenced. The study was conducted because of an initially higher rate of prison sentences for the RJC group than for the cases randomly assigned to the conventional justice (no-RJC) group. This difference flattened out by the end of the enrolment of all the cases the program randomly assigned. While not all of those cases were included in the Shapland, et al (2008) evaluation, the vast majority were. If there is any difference, it would be more prison time with RJC than without it. Prison cannot therefore explain why the effect of RJC would be lower in these experiments, as opposed to being higher due to a “boost” from more incapacitation from imprisonment.

4.6 VICTIM IMP ACT MEASURES: NARRATIVE FINDINGS FROM THE TEN INCLUDED STUDIES

Although RJC is often described as a victim-centered approach to justice, evaluations of effects and effectiveness often are not reported as clearly or extensively for victims as for offenders. This deficit exists both for methodological reporting – numbers of victims in the study, number of interviews, response rates – and for reporting of outcome measures. These problems arise because all the studies reported in this review - the two Canberra (Reintegrative Shaming) experiments, the seven United Kingdom (UK) experiments conducted by the Justice Research Consortium (UK), and the Indianapolis study of young offenders - use cases or offenders as their unit of random assignment and analysis: victims are ‘attached’ to the cases randomly assigned and the random assignment sequence does not create comparability across victims in the same way that it does for offenders.

In all these studies, primary attention was focused on offender effects, especially on re-offending, rather than victim effects. Also, while criminal justice records must identify each offender arrested in a case, there is no imperative to record each victim affected: indeed, there will never be any official record of victims who do not come to the attention of the police or where the identification of complainants/victims in a case is highly arbitrary, e.g. a spouse or children in a burglary. In addition, in some cases where the eligibility criteria are met in respect of the offense and the offender, there may be no identifiable victim, e.g. possession of a concealed weapon. Thus, an objective of including in the sampling frame for any study all victims associated with the randomly assigned cases (or offenders) is not practically possible and the research designs of the included studies can only be quasi-experimental with respect to victim effects.

4.6.5 Emotional restoration

The emotional harm victims suffer from crime can take many forms. One of them concerns self-blame for the crime's occurrence. Victims in the two Canberra experiments and the UK burglary and robbery experiments were asked whether they blamed themselves for what had happened. Figure 7 shows that there were no consistent differences in self-blame between the treatment groups or across locations (reprinted from Sherman, et al, 2005).

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Victim Self-Blame

An important measure of emotional restoration for victims is a sense of safety or, conversely, a fear of victimisation. In Canberra, 18 percent of court-assigned victims anticipated that their offender would repeat the offense on them, compared with five percent of RJC-assigned victims (p<0.005, d=.78). Among property victims, three times as many court as RJC victims believed the offender would do so (21 percent vs. 7 percent, p<0.05, d=.70); among violence victims, more than five times as many court as RJC victims believed the offender would do so (11 percent vs. 2 percent, p=0.01, d=.99).

When Canberra victims were asked whether they anticipated their offender would repeat the offense on another victim, a significantly higher percentage of court than RJC victims believed they would do so (55 percent vs. 35 percent, p<0.005, d=.47). Among property victims, a significantly higher percentage of court than RJC victims believed this would be the case (54 percent vs. 31 percent, p<0.05, d=.53). Similarly, among violence victims, significantly more court victims than RJC victims believed this would be the case (58 percent vs. 40 percent, p<0.01, d=.402).

Perhaps the most significant factor in emotional restoration relates to whether victims receive an apology from their offender, and how they rate the sincerity of the apology offered. Almost 90 percent of all Canberra victims said that they wanted an apology but there were great differences between the court-assigned victims and the RJC-assigned victims when they were asked whether they had received one. Of the victims whose cases were assigned to RJC, 72 percent said they had received an apology (and 86 percent of those who had actually attended an RJC), compared with 19 percent of the court victims (p< 0.000, d=1.33). (In none of the court cases was the apology part of the court outcome but rather negotiated separately, whereas it was almost always part of the RJC outcome).

When victims in the UK burglary and robbery experiments were asked about apologies, again there were great differences between the RJC-assigned and the court only-assigned. In burglary, 96 percent of the RJC victims received an apology compared with 7 percent of the court victims (d=3.18). In robbery, all of the RJC victims received an apology compared with 14 percent of the court-only victims. Figure 8 displays these data in a meta-analysis reprinted from Sherman et al 2005.

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Victim Received a Sincere Apology

There was also a significant difference between the groups when they were asked to rate the sincerity of the apology: in Canberra, 58 percent of the RJC violence victims believed it was ‘sincere’ or ‘somewhat sincere’, compared with 11 percent of the court victims (d=1.33); 55 percent of the RJC property victims said that it was ‘sincere’ or ‘somewhat sincere’ compared with 10 percent of the court victims (d=1.32). In the UK experiments, 79 percent of the RJC robbery victims rated it as sincere compared with 11 percent of the court-only victims (d=1.88); 57 percent of the RJC burglary victims said it was sincere compared with 7 percent of the court-only victims (d=1.58).

These findings confirm that courts often neglect the non-material dimensions of victimisation, while RJC is moderately successful in delivering the emotional restoration victims seek, and especially in providing a forum for the transaction of apologies.

Furthermore, given the significant heterogeneity, we conducted a moderator analysis for this outcome based on gender. As shown below in Figure 8, the magnitude of the difference for female victims was much larger than for male victims (d=-2.082 compared to d=-1.642, respectively).

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Victim Received a Sincere Apology: Gender analysis

4.6.8 Desire for revenge

An underestimated aspect of victimisation is the personal anger victims sometimes feel towards their offenders which, especially in the case of violent crime, may be translated into a desire to physically harm them. This aspect was explored in the two Canberra experiments and in two of the UK experiments, London robbery and London burglary (Figure 10).

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Desire for Revenge

In the Canberra experiments victims were asked whether they would harm their offenders themselves if they had the chance. Only a small percentage of property victims said they would do so (9 percent of the court-assigned and 6 percent of the RJC-assigned, d=-.24), whereas with violence victims, 45 percent of the court – assigned said they would do so, compared with only 9 percent of the RJC-assigned (d=-1.17).

In the UK experiments, the prevalence of desire for revenge was also lower among the RJC-assigned victims than the control-assigned victims in the London burglary and robbery experiments (Angel 2005, Sherman et al 2005). None of the burglary victims assigned to RJC said they wanted to harm their offenders compared with 5 percent of the control group victims; only 3 percent of the robbery victims assigned to RJC wanted to harm their offenders compared with 14 percent of the control group (d=-.92). These findings strongly suggest that RJC can succeed in assuaging the feelings of vengeance felt by many victims of violent crime towards their assailants. Figure 10 displays these effects in a reprint from Sherman et al (2005).

4.7 COST EFFECTIVENESS

The measurement of harm caused by crime to the community is generally underdeveloped. This review has relied primarily on the inadequate measure of frequency of crimes, in which all crimes are counted equally. In this framework, a murder is equal to an auto theft; a rape is equal to a burglary. Treating crimes of such disparate weight with equal seriousness is, on reflection, offensive to fundamental human values. We do not sentence people to prison for equal terms for these unequal crimes. Neither can we be content with evaluating the impact of crime as if all crimes caused equal harm.

In seven of the experiments included in this review, the evaluators (Shapland, et al 2008) took the highly original and important step of giving widely varying weight to each crime for which offenders were convicted in the two-year follow-up period. They did this in two ways, both of which had been developed by the UK government. The first method was to use a scale of crime severity. The problem with that method is that as adopted by the Home Office at the time, the scale was truncated at 10 to 1. That is, the maximum difference between murder and any other crime was limited to 10 times greater seriousness for murder than, for example, a pickpocket taking a wallet with £5 in it. Such a “flat” scale communicates the differences in crime seriousness no better than saying that a $1,000,000,000 annual salary is only ten times greater than a salary of $30,000.

The second and far more accurate method that Shapland and her colleagues (2008) used was the Home Office calculations of the cost of crimes, based on empirical research for average crime costs over samples of many of the most common kinds of crime. This method, developed by DuBourg and his colleagues (2005), employs a range of tens of thousands of pounds or dollars between the lowest and highest cost crimes. As Shapland et al. (2008) applied it to the data in the RJC experiments they evaluated, it created a far more sensitive metric for the evaluation of RJC effects on offenders. Evaluating impact in this way produced much larger effect sizes, greater statistical power, and differences in effect sizes from the measure based on frequency of crimes counted equally.

The most striking evidence of how the impact assessment can be changed substantially by using costs rather than counts is found in their results for London. While the experiments with robbery and burglary offenders in London yielded small and non-significant effect sizes of RJCs on the frequency of reconvictions, the cost-effectiveness ratios in London were the highest of any UK experiment in RJCs. As compared to the 61% lower frequency of violent offenders given RJCs in the Northumbria Magistrates' court (Sherman and Strang, 2012: 231), the London robbery experiment had only 8% fewer reconvictions and the London burglary experiment had only 16% fewer reconvictions for RJC cases than controls. But when the cost of crime prevented in London was compared to the running costs of delivering RJCs (excluding startup costs of a new project), the ratio was £14 in the cost of crime prevented for every £1 spent on delivering RJCs. In Northumbria, across all 3 experiments (as reported by Shapland et al 2008), the cost-benefit ratio was only £1.2 in cost of crime saved for every £1 invested in police delivering RJCs. Yet all of the cost calculations in the UK sites were statistically significant, even where they were not for comparing counts of crimes. In Thames Valley, the benefit across the two experiments aggregated was reported at £2 in costs of crime prevented for every £1 spent on RJCs.

It is worth noting that in their analysis of costs and benefits, Shapland (et al) 2008 made two key distinctions. One was between running costs and startup costs; the other was between total costs and costs only to the criminal justice system. The difference between ongoing, year-in-year out “running” and the one-time, initial “startup” costs is an important issue for external validity. Startup costs may vary much more widely than running costs, especially in terms of working out the inter-agency arrangements needed to establish a process of recruitment of cases and delivery of treatment. Startup can take a year or more, with the costs depending on how many people are assigned to the job of implementing a very different way of processing criminal cases. It is arguably more appropriate to focus on the running costs, which indicate what can be the costs after a startup period—no matter how costly or low-cost the startup may be. The labor costs for delivery are much lower than for the construction of the process, and of greater interest to those who would like to run restorative justice as a long-term strategy.

The second distinction the Shapland et al (2008) cost-benefit analysis draws is between total costs versus criminal justice system costs. We highlight here the total costs, since health and welfare costs are often born by taxpayers and personal costs to victims are of concern to the public interest. Some officials, however, prefer a closed system of cost analysis, in which the focus is on how much money a criminal justice reform can save for the criminal justice budget. For those who prefer that approach, they may find the data in Shapland et al (2008), which clearly show less benefit (to criminal justice alone) in return for RJC costs than for the total estimated costs of crime.

5.1 IMPLICATIONS FOR PRACTICE

The effects of RJCs on the frequency of repeat offending are especially clear as a supplement to conventional justice, with less certainty about its effects when used as a substitute. Yet RJCs may be seen as most appealing when they can both reduce crime and save money—starting with diversion from expensive court processes. The use of restorative processes in this way has grown rapidly in some countries without rigorous testing, sometimes by citing the evidence from using RJCs as a supplement. Cost-saving goals have apparently strengthened the appeal of RJ in theory, but without the kind of evidence reviewed here.

Readers should be well-advised that nothing in the present review provides any evidence in support of immediate “community resolutions” or “restorative resolutions' using restorative principles. That does not mean that the review shows such a quick-fix approach cannot work. It simply means that the time-consuming preparations for a two to three hour conference led by a specialist cannot be compared to a brief interaction at the scene of an incident or shortly thereafter, often with minimal victim involvement. The present review shows only the effects of formal RJ conferences arranged well in advance so that all persons affected by a crime may have a chance to attend.

When RJ conferences are conducted as they were in the experiments included in this review, there can be a high confidence of good results with violent crime, and somewhat less confidence with property crime. The evidence suggests that with serious offenders with long criminal records, the delivery of RJCs also offers substantial cost-effectiveness. The evidence in the London experiments in particular suggests that banishing RJC to low-seriousness crimes is a wasted opportunity. If governments wish to fund Restorative Justice at all, this evidence suggests that the best return on investment will be with violent crimes, and also with offenders convicted after long prior histories of convictions.

5.2 IMPLICATIONS FOR RESEARCH

The take-up rate by offenders and victims for testing RJCs in these experiments was neither low nor high. Had they been higher—upwards of 66% or more—the potential of this method for reducing crime might become more testable. Had they been lower, or under 25%, the potential value of the method might be seen to be reduced. Yet many attempts to introduce RJCs run into major difficulties of recruitment and retention of cases. The evidence in this review suggests that perhaps even greater benefits from RJCs could be obtained by finding ways to increase the takeup rate. New research could also test ways to increase the delivery rate for RJCs when both parties consent. Future research should perhaps focus on the practical issues of delivering high-integrity implementation of RJCs. Experiments designed to compare different delivery mechanisms could also include offender and victim outcome measures to add to the evidence on what works in restorative justice.

One way to interpret the results reported here is to say that the effects of RJC on serious or frequent offenders was to make them hurt people less. That is just what the empathy-based theory of shared values emerging from effective interaction rituals (Collins, 2004, Rossner, 2013) would predict. Yet it is not possible to observe it by merely counting the numbers of crimes or arrests. It is also important for future research to include qualitative measures of the amount of harm that offenders cause before and after they engage in an RJC. The Shapland et al (2008) studies in particular show how this can be accomplished. As new places, especially in Latin America, attempt to conduct experimental evaluations of RJCs, the chance to measure the benefits in this way should not be missed.

The value of cost of crime data too is apparent from the success of the Shapland et al (2008) innovation in showing how much difference, and how much more precision, outcome measures based on costs have to offer, compared with counts of crime. The far greater sensitivity of cost of crime data also means that the smaller sample sizes of experiments testing difficult to implement programs are not doomed to failure. The low power of counts can be sidestepped by exploiting the greater sensitivity of costs. In the process, the cost and difficulty of conducting randomized experiments may potentially be reduced, or their return on investment may be increased.