PROTOCOL: Opioid-specific medication-assisted therapy and its impact on criminal justice and overdose outcomes

Problem, condition, or issue

Opioids have become increasingly available worldwide and pose some of the most serious health consequences, as compared to other types of drugs (United Nations Office on Drugs & Crime, 2015). In 2018, 58 million people used opioids worldwide. Over two-thirds of deaths due to drug use are from opioids, and in 2017, over 115,000 died from an opioid overdose (World Health Organization [WHO], 2020).

The overlap between criminal justice system involvement and drug use is well documented across a variety of countries and samples (e.g., Boutwell et al., 2007; Dolan et al., 2007; European Monitoring Centre on Drugs and Drug Addiction [EMCDDA], 2012; Winkelman et al., 2018). Once released from secure correctional facilities, people with opioid addiction are at high risk for relapse and criminal recidivism. Specifically, a meaningful minority of deaths of former inmates is attributable to opioid overdose (Binswanger et al., 2013; Singleton et al., 2016; World Health Organization [WHO], 2010), and a significant percentage of former inmates will recidivate within 5 years (Fazel & Wolf, 2015).

Criminal justice agencies have been particularly overwhelmed by the recent opioid epidemic. Treating opioid (and other substance) addiction as a means to reduce the risk for future criminality and improve public safety is inherently a responsibility for the criminal justice system, as the influence of substance use on criminal activity is well documented in the literature (Bonta & Andrews, 2017). Of course, one could also argue that opioid addiction, its withdrawal symptoms, and its recovery constitute a serious medical condition for which criminal justice agencies have a responsibility to treat and manage in accordance with the United Nations requirements for the Basic Principles for the Treatment of Prisoners (United Nations, 1990). In fulfilling their responsibility to provide adequate healthcare for individuals in their custody, and through their efforts to rehabilitate offenders to reduce their risk for recidivism more generally, correctional providers must treat substance use disorder. When they do, they may impact criminal recidivism as well as health outcomes like future overdose. As such, it is necessary to deploy the most effective treatment available to achieve maximum impact on these outcomes.

Policy recommendations (WHO, 2009) place emphasis on the use of medication-assisted treatments (MAT) as a front-line defense among correctional populations, because its efficacy and effectiveness have been well established in other contexts (Belenko et al., 2013; Koehler et al., 2014). Despite these policy recommendations, criminal justice agencies have been reluctant or slow to do so (Friedmann et al., 2012; Matusow et al., 2013; Parrino et al., 2015). Many factors may contribute to the poor uptake of this particular approach for managing and treating opioid addiction. It is possible that practitioners may question the utility for MAT to impact public safety outcomes—the chief policy concern of the criminal justice system. Indeed, the uptake of psychological research evidence—particularly that which establishes a strong link between addiction and criminality—into correctional policy and practice has been slow, at best (Gannon & Ward, 2014). Moreover, there may be confusion or even hesitation among practitioners in correctional settings about their responsibility to encourage or administer an intervention that traditionally falls under the purview of healthcare providers.

The intervention

There are a variety of MAT drugs that are currently used for the management and treatment of opioid addiction. This review focuses on those most modern and commonly used drugs to treat opioid addiction over the long term, in the form of supervised maintenance programs, drug substitution, or antagonist protocols. Thus, this review will not examine the effects of Naloxone, which is a drug used to revive someone in a singular emergent opioid overdose event.

The drugs examined in the current review include opioid agonists (heroin and methadone), partial agonists (buprenorphine), and antagonists (naltrexone). Opioid agonists are drugs that work on the opioid receptors in the brain and produce a full opioid effect. Heroin and methadone maintenance MAT services must be administered under the supervision of medical professionals in a highly controlled environment and on a regimented schedule. This approach is designed to help reduce the illicit or off-label use of opioids, cravings, and, gradually, the amount of opioid intake over time. Partial agonists such as buprenorphine also operate on the opioid receptors but produce weaker euphoric effects than felt with full agonists. This class of MAT is also designed to help lower dependency symptoms, misuse, cravings, and symptoms of withdrawal. Buprenorphine is a longer acting agent, so it can be administered less frequently and has the approval to be administered in a variety of clinical settings. Opioid antagonists like naltrexone block the opioid receptors entirely so that if a patient used an opioid, he or she will not be able to achieve any euphoric effects. It is designed to relieve withdrawal and cravings and must be administered by a doctor, nurse, or nurse practitioner.

How the intervention might work

The impact of opioid-specific MAT on overdose outcomes is well established. MAT reduces cravings, illicit drug use, and the amount of opioid use over time (Belenko et al., 2013; Koehler et al., 2014). All of these, in turn, aid to the reduction of overdose outcomes. The mechanisms by which opioid-specific MAT impact criminal justice outcomes are less understood. However, prior research on substance use treatment in general and correctional rehabilitation theory suggests MAT could reduce criminal risk. As substance use is a robust predictor of criminal involvement, reducing substance use reduces future criminal involvement (see Bonta & Andrews, 2017). By extension, any intervention targeting addiction, including MAT, should operate to reduce recidivism risk. More specifically, because MAT facilitates reductions in risky drug use, opioid users will engage less frequently or not at all in drug-related behaviors that warrant a criminal justice response (i.e., drug use, possession, trafficking, paraphernalia possession). Similarly, by reducing cravings and use, people will no longer be motivated to engage in criminal activity that supports, or fuels, their addiction (e.g., burglary).

Why it is important to do this review

The current evidence base for MAT on reoverdose outcomes is strong, but little is known about its impact on the subsample of people with an opioid addiction who also come into contact with the criminal justice system. Because these individuals face challenges posed by addiction and criminal justice involvement, they likely have different experiences and thus needs and risks than people not facing this combination of challenges. Thus, it is necessary to identify whether the same positive clinical outcomes seen among nonoffender groups can be observed among people with criminal justice involvement. Further, although addressing substance use should—and does—reduce criminal risk (Bonta & Andrews, 2017), it is unclear if it is enough to reduce recidivism for people with a serious opioid addiction. A rigorous and systematic synthesis of the evidence base on the effectiveness of MAT for improving public safety will allow criminal justice agencies to make informed decisions about policy, practice, and the allocation of resources. In light of the range of MAT options currently available and the pressing need for methodologically robust results and changes to the underling legal and public health landscape, an updated and complete review is particularly policy-relevant today.

This systematic review will be an update and modification of a 2009 Campbell Systematic Review entitled “Effects of Drug Substitution Programs on Offending among Drug-Addicts” (Egli et al., 2009). Although the authors of this review reported the intent to publish an update every 5 years, no update has yet been published. To the current authors' knowledge, an update is also not currently in progress or planned. As 10 years of research has amassed on this topic, particularly during the height of the “opioid epidemic,” it is necessary to update this review. Further, this review will be far more comprehensive in focus than any reviews on the topic performed to date, because it will include multiple outcomes observed among criminal justice samples and incorporate studies on a variety of pharmacological interventions for opioid use—some of which are quite new.

Criteria for considering studies for this review

Search methods for identification of studies

Description of methods used in primary research

The studies to be included in the current review will employ an experimental or strong quasi-experimental design examining the impact of specified MATs on individual-level criminal and overdose outcomes. All studies will include a measure of the impact of an opioid-specific MAT on offending or overdose outcomes within criminal justice-involved populations.

In the quasi-experimental and experimental studies, the treatment group will receive an opioid-specific MAT (e.g., Buprenorphine, naltrexone, methadone maintenance, heroin maintenance), and the control group may receive a different type of opioid-specific MAT (e.g., methadone compared to Buprenorphine), a placebo, some sort of alternative medication not specific to opioid addiction, talk therapy(e.g., individual or group counseling), or no treatment at all. Additionally, the treatment condition may also be a MAT + talk therapy treatment. All talk therapy interventions will be further coded into cognitive-behavioral (CBT) versus other, since cognitive-behavioral therapies traditionally produce greater effects and have a larger evidence base than other approaches in the treatment of substance use disorder (McHugh et al., 2010).

Criteria for determination of independent findings

As discussed in Egli et al. (2009), there are three potential avenues for the nonindependence of findings: (a) multiple indicators of offending reported from a single study (e.g. arrest, conviction); (b) the same outcome measured at multiple points in time; and (c) the same data being reported across multiple studies (e.g., in multiple past systematic reviews). The criteria for the determination of independent findings will be the same for the current review as was outlined in the Campbell Review Protocols (e.g., Lipsey & Landenberger, 2006).

In the event that there are multiple indicators of offending reported from a single study, the authors will select a commonly used outcome measure from other studies, the “all offenses” category, typically using a measure of rearrest. In the event that the “all offenses” category is not available, an offense category will be selected at random (see Egli et al., 2009; Lipsey & Landenberger, 2006). This will be done in an effort to maintain as much comparability across studies as possible.

In the event that the same outcome is measured at multiple points in time, the authors will include the measure which has the closest timing to those most commonly used across the other studies (i.e., outcome at 12 months). This is again to encourage as much comparability as possible given the unique methods employed across some studies (Lipsey & Landenberger, 2006).

Lastly, in the event that the same data are reported across multiple studies, the coding protocol will include measures that allowed the current review authors to identify the shared reporting of data. This will include identifiers of each study's authors' names, location, and time frame of the study, as well as sample descriptions. In the event that multiple publications report results using the same set of data, the study with the most complete and detailed manuscript will be used as the primary coding source. From there, the coding protocol will also track which manuscript will be the primary coding source, and whether there are other manuscripts reporting the same data. These additional manuscripts will only be consulted given the need for clarification surrounding the data in the primary designated manuscript.

Selection of studies

The research team will review all potentially relevant studies for the proper inclusion criteria using the same coding system as the original study, made available to the current authors by Egli et al.'s (2009) team. All studies will be coded in two phases. In the first phase, the titles and abstracts will be reviewed to determine basic inclusion criteria is met—that is, (a) the evaluation of effectiveness of MAT services (b) on criminal or overdose outcomes (c) for people with opioid use disorder (d) who are or have been involved in the criminal justice system. Studies meeting these criteria or any study for which this information cannot be readily determined from the title or abstract will be retained for coding in Phase 2. In Phase 2, the full text of each study will be reviewed. All studies with irrelevant independent or dependent variables, ineligible sample characteristics, and studies that lack the methodological rigor will be removed from consideration for inclusion. The number of studies removed during this process will be recorded and reported.

To ensure reliability regarding exclusion, the lead and corresponding authors will each independently screen half of the pool of potential studies for inclusion. If at any time, one coder is unsure about a study's eligibility for inclusion (e.g., criteria for inclusion are not detailed enough or are too vague to render a decision), the coder will render a preliminary decision and ask the other coder to review and code the article independently as a “cross-check” on reliability. In the event that the lead and corresponding author cannot reach consensus, the third author will make the determination. The number and outcome of these reliability cross-checks will be recorded and reported. As a final failsafe, each coder will also independently code a random sample of 5% of the total studies included in the other coder's group, and appropriate reliability coefficients for agreement (kappa for categorical variables and ICC for continuous variables) will be computed. In the event that the prespecified eligibility criteria are adjusted by the team according to unanticipated issues that may arise during the search or coding stages, the team will document these suggested changes (in place of making ad hoc decisions about inclusion that stray from the protocol) and perform sensitivity analyses with and without these studies that may no longer meet the eligibility criteria.

Data extraction and management

The Egli et al. (2009) team created a coding protocol for the original review that provided for a systematic method of extracting information regarding each study's research design, program, nature of the outcome measures, and outcome data. This protocol was provided to the current research team in order to promote consistency and structure in the coding procedures used in the updated review. The current research team then updated this coding protocol to reflect the changes from the original to the current review. The updated coding protocol includes the systematic extraction of information regarding the study identification, content and methodological inclusion criteria and rigor, control and treatment sample descriptive information, actions taken upon the control and treatment samples, treatment characteristics, the types and measurement of outcome data, and effect size information. See Appendix A for the updated coding protocol. Coding reliability will be established through the use of multiple coders (i.e., at least two for any given study) to independently code each study. Discrepancies in coding will be brought to an additional coder to make the final coding decision.

Assessment of risk of bias in included studies

We will use two tools to assess risk-of-bias in our included studies: (a) The Revised Cochrane risk-of-bias tool for randomized trials (RoB 2); and (b) The Risk of Bias in Nonrandomized Studies−of Interventions (ROBINS-I) assessment tool.

The necessary steps will be taken to assess the risk of bias in randomized trials using the RoB 2. First, as part of the preliminary considerations two independent coders will document the important characteristics of each study and the sources that are used to confirm these characteristics using the standard template provided in the tool. Then, using the appropriate version of the RoB 2 (given the type of randomized trial), signaling questions, criteria, response options, and scoring algorithm for each domain we will determine which studies are at “low risk of bias,” “high risk of bias,” or present “some concerns of bias.” If at least one domain is determined to present “some concerns” or “high risk of bias,” then the study will maintain this risk-of-bias rating overall. All domains will be assessed for each study even after one domain may be rated as “some concern” or “high risk of bias.” The domains include: (a) bias arising from the randomization process; (b) bias due to deviations from intended interventions; (c) bias due to missing outcome data; (d) bias in measurement of the outcome; and (e) bias in selection of the reported result. Additionally, cluster-randomized trials will be assessed for bias arising from identification or recruitment of individual participants within clusters. Judgments will be overridden only in the event that the full authorship team is in agreement that it is appropriate. Domain-level consensus judgments will be displayed in a table in the main document and the answers and justifications for each signaling question will be provided in an appendix.

The ROBINS-I tool will be used to assess risk-of-bias in nonrandomized studies of the effects of interventions (NSRIs) and will follow the same general process as the RoB 2 described above, but with necessary emphasis on content expertise. In preparation for assessing risk-of-bias within NSRIs, a preliminary specification of the anticipated key confounders and cointerventions for each study will be identified in consideration of the review's essential research questions. Target trials (i.e., hypothetical randomized trials whose results mimic those of the specific NSRI) will also be specified. Then, using the ROBINS-I signaling questions, criteria, response options, and scoring algorithms we will assess risk-of-bias across its seven domains: (a) bias due to confounding; (b) bias in the selection of participants into the study; (c) bias in classification of interventions; (d) bias due to deviations from intended interventions; (e) bias due to missing data; (f) bias in the measurement of outcomes; and (g) bias in the selection of the reported result. Each domain will be rated one of the following: “low risk of bias,” “moderate risk of bias,” “serious risk of bias,” “critical risk of bias,” and “no information,” with accompanying text for justification. Studies will assume the overall risk level of the “riskiest” domain. Attempts will be made to determine the magnitude and potential direction of biases. Upon all determinations, the studies’ overall strengths and weaknesses will be compared and contrasted to determine the degree to which intervention effects might be considered causal. As with the RoB 2, all domain-level consensus judgments will be displayed in a table in the main document and the answers and justifications for each signaling question will be provided in an appendix.

Measures of treatment effect

The statistical procedures and conventions will align closely with those that were used in Egli et al.'s (2009) review, as the types of studies and outcomes that were included will be similar. The most detailed numerical data will be collected in order to facilitate similar analyses across the included studies. For binary offending outcomes (e.g., arrest, conviction, incarceration, specialty court failure, mandated treatment failure, or community supervision failure) and overdose outcomes, odds ratios will be computed, which are typical and well-suited for dichotomous outcomes. For continuous or quasi-continuous measures of these outcomes (e.g., total number of arrests), a standardized mean difference type effect size will be computed, and then transformed into an odds ratio (Egli et al., 2009; Lipsey & Wilson, 2001).

In multiarm studies, in which there is more than one comparator condition and the additional comparator conditions are determined to be eligible for this systematic review, researchers will attempt to combine intervention and comparator conditions so that only a single pairwise comparison is computed, in line with recommendations from Higgins et al. (2019). This prevents an intervention group from being “double-counted” and inflating the unit of analysis error (Higgins et al., 2019). Also, consistent with MECCIR Conduct Standards, all intervention groups, regardless of inclusion, will be detailed in the Section 3.1 (Higgins et al., 2019).

Dealing with missing data

It is possible that missing data from the original studies can preclude either (a) sound decision-making concerning study eligibility and selection for inclusion and/or (b) ability to compute an effect size. In both instances, the researchers will attempt to obtain the relevant data necessary from the original study authors. If this is not possible, the researchers will include the studies in the summary of studies in a narrative form and will detail why they were not included in the meta-analysis.

Assessment of heterogeneity

To assess heterogeneity, we will use the χ ² test that goes with the forest plot. A p value of .10 will be set as the cutoff, because higher quality studies are likely to have smaller sample sizes. Consistent with Cochrane analytic guidelines, we will also compute the I ² statistic, which “describes the percentage of the variability in effect estimates that is due to heterogeneity rather than sampling error (chance)” (Deeks et al., 2019).

Data synthesis

The current review will comply with the standards of meta-analysis as specified in Practical Meta-Analysis by Lipsey and Wilson (2001) and will use SPSS for the analyses. The two types of studies to be included (RCTs and quasi-experiments) will be meta-analyzed together using meta-analysis software. In the event that studies include multiple treatment arms, we will combine eligible multiple treatment versus comparator conditions so that there is only one pairwise comparison made, in the manner detailed below: 1.

Synthesis for MAT v placebo/no treatment/waitlist control.

In line with Egli et al. (2009), effect size outliers (considered greater than or equal to 3 standard deviations above or below the mean) will be winsorized to the next highest observation that is not judged to be an outlier. This will prevent bias from extreme observations from entering the results. No data will be imputed for missing values.

In order to compute mean-effect sizes, the inverse variance weight method of the meta-analysis will be used (Lipsey & Wilson, 2001). A random-effect model will be assumed a priori.

Subgroup analysis and investigation of heterogeneity

The a priori determined potential moderators of the effectiveness of opioid-specific MATs on criminal justice and overdose outcomes that will be explored include design type (experimental or quasi-experimental), whether or not the opioid-specific MAT prescription was coupled with talk therapy (e.g., CBT or non-CBT individual or group counseling), the level of medication adherence, dosage, follow-up period, and/or treatment length. Each of these potential moderators may contribute to or subtract from the “ideal” treatment conditions as experienced by study subjects. For example, MATs may have a stronger impact over longer periods of time as subjects learn to manage side effects and get into a routine of adherence. In this scenario, studies with shorter follow-up periods may not capture the full impact of MAT on criminal justice and overdose outcomes.

Other potential moderation analyses will be conducted using metaregression techniques (e.g., Deeks et al., 2019) to examine effects across specific subgroups based on demographics characteristics of gender, race, and age, as well as location/context of treatment (e.g., jail, prison, community, court), and “era” (i.e., did the treatment occur before or after the onset of the opioid crisis). These secondary potential moderators capture the nuances with which criminal justice or overdose outcomes under MAT may vary. For example, MAT may be more effective when implemented in jail versus the community, as administering the medication is in that context the responsibility of the correctional staff, and not the subject.

In the incident where clustering is present in a given study—that is, when multiple cohorts are included in the same treatment arm—we will make adjustments consistent with Cochrane recommendations (Higgins et al., 2019).

Sensitivity analysis

Sensitivity analyses will be conducted post hoc in order to test the robustness of the results. To this end, we will use metaregression to directly examine the impact of small versus large sample sizes (as recommended by Deeks et al. (2019).