Abstract
1. BACKGROUND 1
In 1984, the Minneapolis domestic violence arrest experiment (Sherman and Berk, 1984), reported that arrest in misdemeanor domestic assault cases reduced reoffending substantially in comparison to two informal alternatives (mediation or separation). The evidence from this experiment strongly supported the hypothesis of specific deterrence theory, and these findings thus culminated in a rich academic discussion (Mills, 1998; Schmidt & Sherman, 1996; Tolman & Weisz, 1995) as well as elaborate public attention (National Institute of Justice, 2001). In many ways, this experiment paved the way to mandatory arrest policy in domestic violence cases in numerous countries around the western world.
Subsequent trials funded by the National Institute of Justice (commonly known as the Spousal Assault Replication Program (SARP)), however, failed to replicate the Minneapolis findings, reporting inconsistencies in the direction and impact of arrest in domestic violence cases (Berk et al., 1992a; Dunford et al., 1990a: 1990b; Hirschel et al., 1992; Pate and Hamilton, 1992; Sherman, 1992a).
Some systematic reviews of the NIJ studies were conducted (e.g., Garner et al., 1995; Maxwell et al., 2002; Sugerman & Boney, 2000). Across the completed replication studies, Maxwell (1998) and Maxwell et al. (2002) have reported the results of case-level analysis of the five replication studies using available offender and victim case-level data. They produced an overall effect (odd-ratios) for the arrest versus no arrest treatment comparison for the prevalence, frequency, and the time-to failure rates for all male offenders (n=4,032) and for the male offenders whose victims were interviewed after the incident and could report failure data (n=3,147). To account for differences in study designs and sample demographics, Maxwell et al. (2002) also weighted their pooled, cross-site effects by simultaneously controlling for the study sites and within study follow-up lengths, and several offender characteristics. Maxwell, et al. (2002) reports a modest yet consistent significant cross-site preventive effect of arrest on the rate of intimate partner violence re-victimization, using pooled analyses of the five replication studies.
Using data produced by Garner et al. (1995), Sugerman and Boney (2000, p. 67) reported that the average effect size for the arrest versus the non-arrest comparison on official recidivism rates was not significant, nor was it variable across the six sites. However, they do report a significant deterrent effect for arrest on the offenders' rate of subsequent re-victimization as reported by the victims (p. 68). In the context of these victim-reported data, they also reported that the “variation among these six effect sizes may be accounted for by chance” (p. 68). Thus, this more traditional meta-analysis of published results produced conclusions that are substantively consistent to those articulated in Maxwell, et al.'s (2002) pooled analysis of case-level data from nearly the same studies. More precisely, both refereed studies found non-significant results for arrest across several re-arrest rates, but significant reductions in the re-victimization rate. They both also found that the results (e.g., effect sizes) replicated each other across the applicable studies. The only marginal difference produced by these two symmetric reviews was the degree to which assigning arrest influenced the rate of re-victimization. Maxwell, et al. (2002) reported an average reduction of about 25% in the prevalence of re-victimization attributed to assigning arrest while Sugerman and Boney (2002) reported finding just a 5% reduction due to arrest. This difference could be attributed to either the differences in the samples (Maxwell, et al. selected cases from just the five replication studies while Sugerman and Boney used effect sizes from all six completed studies), or because of the difference in their approaches to producing their synthesis (pooled data with covariates vs. meta-analyses of bivariate published summary results).
However, the available evidence from these trials and similar studies was not assessed under a full meta-analytic procedure within a Campbell review, measuring mean effect sizes and correlations between study features and effect sizes. Specifically, the reviews have not demonstrated across trials the relative magnitude of the difference between arrests and no-arrests, which can arguably provide a more informative assessment of arrest versus alternative-to-arrest police policies (although we take under consideration the possibility that the results might be equivocal). Neither Sugerman and Boney (2002) or Maxwell, et al. (2002) reported sub-treatment effects since both reviews chose to collapse the many nonarrest treatment groups into just one control group. Therefore, this review could add information about whether the arrest effects produced by these earlier syntheses varied across alternative control groups.
Lastly, previous studies and available reviews have not examined interaction effects with social bonds. Under the stake-in-conformity hypothesis (e.g., Toby, 1957; Sherman et al., 1992), it may be the case that there is an interaction effect of arrest with certain demographic characteristics of the suspect. Sherman and others (Sherman and Smith, 1992; Pate and Hamilton, 1992, and Berk et al., 1992b) have all reported a differential and interactive effect of arrest with the employment status of the suspect (as measured by victim interviews). Sherman (1992a) also reports similar but weaker interaction with marriage. Based on these earlier, less rigorous analyses, we propose to conduct moderator analysis of the available evidence in order to test this hypothesis. We hypothesize that that arrest deters employed suspects from committing additional offenses, but increases subsequent domestic assault by unemployed suspects. We will also test the effect of marriage, education and age as moderators of arrest effects on repeat domestic violence; however the scope of the additional subgroup analyses largely depends on the data available in the original reports.
2. OBJECTIVES
The objective of this review is to systematically review and synthesize credible evidence on the effectiveness of arrest policy for misdemeanor domestic violence on repeat offending. Of interest are the effects on future reoffending in terms of same-victim violence and different-victim violence by the offender, and the moderating effect of stakes in conformity. We further plan to produce separate point estimates by specific control groups, which we believe will an improvement over the existing meta- and pooled-analyses. It is anticipated that this review will help inform policy-makers' decisions regarding mandatory arrest policy. Many jurisdictions have already adopted and continue to enforce such policy and a critical examination of the existing evidence is warranted.
3. METHODOLOGY
3.1 CRITERIA FOR CONSIDERING STUDIES FOR THE REVIEW
3.1.1 TYPES OF INTERVENTION
The intervention of interest is mandatory arrest for misdemeanor domestic abuse. Mandatory arrest is defined as the legal duty of police to make an arrest if the officer has reason to believe a domestic violence act has been committed. Although different jurisdictions have different requirements to determine qualifying factors for mandatory arrest, they include at least the immediate physical removal from the scene of the incident and the physical incapacitation of the offender for a relatively short period of time (between a few hours to a couple of days). Arrest may also be used in conjunction with other immediate treatments, such as restraining orders, commitment to avoid additional offences, etc. Such studies will be included as well, however we will assess mixed treatments separately, in order to learn how arrest interacts with other treatments as well.
In order to compare the effect of arrest, we will look for studies that either did not apply any intervention in the comparison group, or — in the more likely event --any alternative to an arrest, such as mediation, separation, restorative justice, consultation, citation, counseling as “ticket” citation, or any other processing carried out by the police in misdemeanor domestic violence cases that does not result in the suspect being taken into police custody at a different location. Collectively, we call this comparison category any “alternative to an arrest”, though we are keen to assess different ‘control groups’ separately as well.
3.1.2 TYPES OF STUDIES
We will include the following study designs (we will follow Campbell guidelines of reporting results separately for these two designs): Field randomized controlled trials/true experiments that randomly allocate participants to arrest condition and an alternative condition. Studies must include at least one alternative-to-an-arrest employed as the control intervention. Whenever more than one type of comparison intervention is tested, separate point estimates will be used for each type. Quasi-experimental designs that include a control group and baseline assessment of comparability. While we recognize that the strength of evidence from these studies is generally, but not always, weaker than from true experiments, we are still interested in capturing the relationship between arrest and recidivism found in quasi-experimental designs so that we can fully summarize the existing evidence in this area. We therefore will look to identify: An identifiable comparison group that does not receive arrest. This may be designed based on historical comparison group design. Excluded comparison groups will include those who were ineligible for arrest (e.g., mental defects). Studies that include baseline assessment of the comparability of arrest and comparison conditions. This means that we will assess the comparability of the study conditions and observed differences on several variables that may be associated with future criminal behavior and risk behaviors, such as critical demographic variables (i.e., age, employment, and marital status) as well as outcome measures at baseline.
3.1.3 TYPES OF PARTICIPANTS
Eligible studies will be based on samples of individuals (offenders) involved in a domestic abuse case. These may be both male and female participants, juvenile and adult participants, where participants of one of the treatment groups were arrested for misdemeanor domestic abuse in the presence of the police, shortly after a domestic abuse incident was reported to the police. In other words, only studies in which the offender was present at the scene upon arrival of police will be included in the review (cf. Dunford et al., 1990a). The nature of misdemeanor domestic abuse suspects may vary in different jurisdictions
2
. Collectively, these are cases in which one family member commits or threatens violence against another family member or household member - although we are specifically interested in violence between couples. These couples include any form of intimate partnerships, including spouses, roommates, housemates, dating partners, and same-sex partners.
3.1.4 TYPES OF OUTCOME MEASURES
The primary outcome of interest in this systematic review is criminal behavior following the arrest for domestic violence, against the same victim. Outcome data may comprise of official records such as arrests, charges or re-convictions for a new offense; or victim self-reported victimization made by the same-victim of the said arrest. These various outcome measures will be analyzed separately, as discussed below. The secondly outcome of interest in this systematic review is the same as the primary, except it includes recidivism data against any victim. If outcome measures are not reported separately or are not clearly defined as such, we will assume they are meant to pertain to any-victim crimes — although a cursory review of the literature indicates that such specificity is usually reported.
3.1.5 SETTINGS AND TIMEFRAME
We will not exclude studies on the basis of language or geography. We will work with our international contacts to learn which countries are likely to have used and evaluated the effect of arrest in misdemeanor domestic violence so that we can target foreign language and location searches appropriately. Studies using data collected from 1970 onwards will be included. The rationale for this timeframe is twofold: first, it is unlikely that any older studies with eligible research designs exist; and second, the social context is markedly different. For example, the police culture changed extensively between the 1980s and 1990s in its views on domestic affairs. Furthermore, the structure of the criminal justice system has changed considerably since the 1960s, which would potentially make the coding of domestic violence-related offense types difficult.
Studies that do not meet one or more of the above criteria will be excluded from the review altogether, or just from the relevant portion of the review. Both reviewers will independently screen the full text of studies and recommend whether to include them in the review. Disagreements will be resolved upon discussion and if no resolution is achieved, the study will not be included in the review. Each excluded study will be listed along with a reason for its exclusion.
3.2 SEARCH METHODS FOR IDENTIFICATION OF STUDIES
The search strategy will include the following sources: Searches for NIJ-funded experiments on the impact of arrest in domestic abuse incidents; Extensive search of online databases (see section 2.4 below); Searches of narrative and empirical reviews of literature that examined the effectiveness of arrest in preventing subsequent domestic abuse. Search for literature reviews on the relationship between arrest and domestic abuse; Searches of bibliographies on the effectiveness of arrest in preventing domestic abuse; Registers of randomized controlled trials: the Registry of Randomized Experiments in Criminal Sanctions, 1950 — 1983 (Weisburd, Sherman and Petrosino 1990) and the Social Psychological, Educational and Criminological Trials Register (SPECTR) developed by the Cochrane Centre; As studies will be located, their references will be examined for details on other relevant studies. These will then be examined with accompanying notes being made to explain where the document was originally cited; Contact with key researchers in this field. Each title and abstract will then be screened to establish if it meets the criteria established in Section 3.1 above. These studies will be assessed using the checklist attached hereto as Appendix I. The checklist form will be completed for each of the studies. No limitations are made on the nature of publication (i.e., published or unpublished material and ‘gray literature’). See Section 3.6.2 below in relation to publication bias analysis.
3.3 SEARCH TERMS
Three categories of keywords were developed for this search. The intention of separating the terms in this manner is to include all the potentially relevant results, while simultaneously excluding the large bodies of literature on domestic violence from non-criminological disciplines. These sets of keywords will be combined with a Boolean “AND”.
3.3.1 Policy of Interest
[“ARREST*” or “CRIME*” “OFFEND*” or “BATTER*” or “SUSPECT”] and [”DOMESTIC VIOLENCE” or “DOMESTIC ABUSE*” or “DOMESTIC ASSAULT*” or “MARITAL VIOLENCE” or “BATTERED WOMEN” or “BATTERED PARTNERS” or “SPOUSAL ABUSE” or “WIFE BEATING*” or “INTIMATE PARTNER VIOLENCE” or “FAMILY VIOLENCE” (however violence solely against non-partner members, such as teen on parents or juveniles, will be excluded);
3.3.2 Outcomes
CRIM* or DELINQUEN* or ARREST* or DETAIN* or DETENTION or “CALL* FOR SERVICE*” or OFFEND* or VIOLEN* or ASSAULT or FIGHT* or RE-ARREST or RECIDI* or “DETER” or “CONFLICT TACTICS SCALE” or “CTS” or “CTS2” or “CTSPC” or “RECONVICTION”
3.3.3 Research Design
”EXPERIMENT” or “QUASI-EXPERIMENT” or “RANDOMIZED CONTROLLED TRIAL” or “RCT” or “RANDOM ASSIGNMENT” or “FIELD EXPERIMENT” or “EVALUATION AND COMPARISON” or “EVALUATION AND CONTROL”
Key terms will also be used in conjunction with “DISSERTATION” or “THESIS” to locate such works as well.
3.4 ELECTRONIC SOURCES
The databases listed in Appendix III will be searched for eligible studies (list of databases appears in alphabetical order), followed by a search in Google Scholar. We will also collect subject-level data from the Interuniversity Consortium for Political and Social Research (ICPSR), which stores the collected data from at least six known replication studies funded by the National Institute of Justice with the aim of replicating the Minnesota Domestic Violence Experiment (Sherman & Berk, 1984). This will enable us to download the six replication studies from ICPSR, each containing multiple data files that will need merging, to produce the stakes in conformity models using criminal history and victim interview data and ultimately conduct the analyses listed in 3.9.2 below: The bibliographies of relevant articles from specialized journals (e.g., Journal of Interpersonal Violence and Journal of Family Violence will be reviewed as well.
3.5 CODING OF STUDIES
The two independent reviewers will extract information from full-text versions of eligible studies using the coding protocol (see Appendix II). If both reviewers agree on the rating results of each article and the coding of the data from each article, then the data will be entered into SPSS and Comprehensive Meta-Analysis 2.0.
The following issues will be dealt with in the coding process: Effect-sizes for all available time periods will be coded (i.e., 6-, 12-, 18 and 24-months follow-up period). The outcome measure will be reported separately for two main categories: frequency data gathered from official records (police arrest or offense reports) and prevalence data from victim surveys (initial domestic violence victims). Because of our aim to assess whether the effect of arrest was conditional upon “stakes in conformity” (Toby, 1957), any social “stakes measures” for the offender will be codes as well, including other potential moderators such as age, gender and education levels.
It is likely that information on these indicators will appear in the unofficial reports, such as interviews conducted with either the offenders or their victims. At the same time, this source of information is problematic due to likely poor response rate. Therefore, any study in which the response rate is less than 60% will be excluded from that portion of the review.
3.6 DATA COLLECTION AND ANALYSIS
3.6.1 ASSESSMENT OF RISK OF BIAS IN INCLUDED STUDIES
The extent to which we can draw conclusions about the effect of arrest in domestic violence cases depends on the validity of the outcomes of the primary studies. We are particularly concerned about internal and external validities, given the arguably non-comparability of studies. The reliability of the results may also be at risk, given the methodologies used in primary studies, should low-level studies be included as well.
We plan on using critical assessment for various risk domains in a checklist format, proposed by Juni (2001). This list appears in a tabular format in Appendix IV and it contains five types of biases: Selection bias (i.e., systematic differences between baseline variables that define the groups before the arrest); Attrition bias (i.e., systematic differences between the groups in withdrawals or exclusions of participants from the results of a trial; in this context, we specifically mean systematic differences between participants who were arrested as assigned and those that were not arrested though assigned such treatment); Performance bias (i.e., systematic exposure to factors other than arrest, specifically in the comparison groups); Detection bias (i.e., systemic measurement differences); and Reporting bias (e.g., selective outcome reporting).
Some items are objective and quite apparent (e.g., the participants were selected and allocated in non-random procedures, precise exclusion criteria were not always used in the selection of the participants, and studies have not incorporated power calculations), and some are subjective (e.g., can the design address the studied question in a comprehensive way?). We will take a robust approach by stating whether within each study there is a “low” “medium” or “high” level of bias on every risk domain, which we will score independently. We will then review these scores to obtain a measurement of each bias across the studies, in order to assess whether their plausible impact on the outcomes. We will also record the source of each bias as well.
3.6.2 ASSESSMENT OF PUBLICATION BIAS
Publication bias can lead to systematic bias in our review. We will estimate the reporting bias in published versus unpublished works using funnel plots (Rothstein, Sutton and Borenstein, 2005). Funnel plots can be used to assess whether a systematic review is likely to be vulnerable to publication bias, by plotting arrest treatment effect (i.e. mean difference between intervention group and control) against the inverse of the variance or the sample size.
However, we will only explore this option should enough studies meet our eligibility criteria.
3.7 DESCRIPTION OF METHODS USED IN PRIMARY RESEARCH
Very few studies randomly assign domestic violence offenders to either arrest or an alternative-to-arrest groups; a cursory review of the literature suggests that the NIJ replication (e.g., Dunford 1990; Maxwell 1998; Schmidt and Sherman 1993) and the Sherman and Berk (1984) Domestic Violence Minneapolis experiment are the leading if not the only experiments in this field. Some studies have had after-only measures of repeat victimization, of those victims whose partners were arrested compared to those whose partners were not arrests; such studies controlled for baseline equality statistically (e.g., Cho and Wilke 2010). Most studies looked at official records as the main outcome variable (e.g., Hirschel et al 1992), where others looked at victim interviews following random assignment to arrest and control conditions (e.g. Jolin et al. 1999).
3.8 CRITERIA FOR DETERMINATION OF INDEPENDENT FINDINGS
3.8.1 Combing Multiple Outcomes
There are likely several independent outcomes (e.g., arrest and reconviction) or time-points within each study (e.g., arrest within 6 months or 12 months), and we will report and synthesize each separately (for example, a separate meta-analysis for arrest data and a separate for reconviction data). We hope that sufficient data will be available to cluster the available information within such homogeneous outcomes. In the case of studies the measure more than one alternative to an arrest, these will be first be collapsed into a single categorical condition of “alternative-to-an-arrest”, but will also be analyzed independently, based on the number of studies available under each category, as described below.
3.8.2 Multiple Subgroups
We also plan to analyze the following subgroups within studies, where possible. First, if sufficient data are reported in the primary studies, we will explore the impact of potential covariates on the outcomes, using random effects meta-regression or analogue-to-the-ANOVA moderators' analysis with SPSS METAF macro (Professor Wilson, 2003)
3
. We thus want to be able to look into the various treatment components as well as extraneous elements that may influence the results, such as treatment components (long versus short arrest; with or without additional treatments) and methodological quality of the study (e.g., experimental, non-experimental). More importantly, as we emphasized earlier, we place particular importance on the conditional effect of arrest on stakes in conformity - primarily marriage and employment, however other features of the participants are of interest as well (age, gender, education, and ethnicity).
3.9 MEASURES OF TREATMENT EFFECT
The primary outcome measure will be the frequency of official police records of repeat arrests or reports of domestic violence with the same offender against the same victim. The secondary outcome measure will be the same as the primary, except that it will include any additional non-domestic violence offending. The tertiary measure will be the victim-reported measures of reoffending. We elaborate on these processes below.
3.10 EFFECT SIZE CALCULATIONS AND DATA SYNTHESIS
The Outcomes will be meta-analyzed using traditional inverse-variance weighted meta-analysis if possible. In all cases, a random effects model will be assumed a priori. Cochrane-Q and I2 statistic4 will be used to measure for homogeneity and In order to
3.11 TREATMENT OF QUALITATIVE RESEARCH
Qualitative research will not be included in this review or in the meta-analysis.
4. TIMEFRAME
We envisage completion of the review within 10 days of approval of this protocol.
5. PLANS FOR UPDATING THE REVIEW
The review will be updated on a three-year basis. As part of this update we will need to code any new studies identified and rerun the analyses.
6. ACKNOWLEDGEMENTS
We wish to thank the anonymous reviewers of this protocol for their valuable comments. We would particularly like to thank Professor David Wilson for his insightful suggestions.
7. STATEMENT CONCERNING CONFLICT OF INTERESTS
None.
Footnotes
1
We wish to thank Campbell Collaboration's anonymous reviewers and the Editor for their insightful commentary which we have incorporated in the text below.
2
The term “misdemeanor violence” mean a criminal offence that is punished less severely than felonies (e.g., punishable with incarceration for one year or less) but more severely than administrative infractions. Under American Federal or State law, for example, misdemeanor domestic violence “has a element, the use of, or attempted use of physical force, or the threatened use of a deadly weapon. It is an offense which was committed by a current or former spouse, parent, or guardian of the victim, by a person with whom the victim shares a child in common, by a person who is cohabiting with or has cohabited with the victim as a spouse, parent, or guardian, or by a person similarly situated to a spouse, parent, or guardian of the victim” (Title 18, United States Code, Section 922(g)(9); see also § 925(a)(1). In the review, we will separate between both same-victim and any-victim crimes, as more fully dealt with in 2.1.4.1 below
4
I 2 is expressed as a percentage of the total variance in all the data, with 25%, 50% and 75% considered as low, moderate or high level of heterogeneity.
5
Because they are present prior to randomization, the proposed moderator variables should be uncorrelated with treatment assignment and we do not envisage requiring any specialised handling given the ITT approach.