PROTOCOL: Service brokerage for improving health outcomes in exprisoners

3.1.1 Types of studies

We will include RCTs, cluster RCTs, quasi-RCTs, controlled before-and-after studies (where intervention and outcome measurements are contemporaneous) and interrupted time series studies. Interrupted time series must have a clearly identifiable time point at which the intervention occurred and must include measurements for at least three time points before and after the intervention. Studies where groups are allocated must have at least two groups in each arm of the study. Our reasons for including non-RCT designs are that (a) ethical considerations sometimes necessitate other study designs and (b) interventions in this area are usually delivered by mandated service providers rather than researchers, such that the evaluation design must align with service provision requirements. Process evaluations associated with the included studies (including qualitative data) will be included to provide context for the findings (Popay 2006).

3.1.2 Types of participants

Participants will be adult and juvenile ex-prisoners. For the purposes of this review, ex-prisoners are defined as people who have spent a period of time held against their will in a juvenile or adult prison (or jail) (including pre-trial detention) and who have been released from a juvenile or adult prison (or jail) into the community, without any limits being ascribed to length of time served in custody. Individuals held against their will in psychiatric facilities or other primarily therapeutic contexts will be excluded from this definition. People released into hospitals, including psychiatric hospitals, will also be excluded from this definition. Individuals held against their will in other punitive environments, such as the 06 ‘compulsory drug rehabilitation’ centres in Vietnam (Jürgens 2010) will be included if suitable studies are found.

There will be no limits on geographic location; this review will consider international studies, including studies from developing countries, if available.

3.1.3 Types of interventions

Included interventions will be those that include a component designed to facilitate access to or utilisation of health or psychosocial services (or both) in the community, including, for example, housing or employment services. Examples of eligible interventions include (a) providing prisoners or ex-prisoners with written information about community-based services, (b) ‘in-reach’ whereby community services visit prisons and engage with prisoners prior to release, and (c) ‘case management’ whereby a worker in a prison or community setting assists a prisoner/ex-prisoner to access community services by making appointments on their behalf or accompanying them to such services. Interventions may have multiple components, including direct service provision, but must include a service brokerage component. Interventions may include direct or indirect financial incentives or subsidies to increase the affordability of services, but interventions with no such incentive or subsidy will also be included. Interventions delivered in prison, those delivered postrelease, and those with both pre-release and post-release components will be included.

The control/comparator intervention is ‘usual care‘, which may vary between studies. Heterogeneity of the comparator groups will be considered during the review. There will be no restrictions on dose, frequency, intensity or duration of the intervention, although these variables will be considered in specific comparisons.

3.1.4 Types of outcome measures

The focus of this review will be health outcomes so, to be included, studies must report on one or more health-related outcomes, even if these are not the primary focus of the study. Specifically, our primary outcome measures are substance use (a key predictor of both poor health outcomes and recidivism in this population) and health-related quality of life. Secondary outcomes will include health, health service utilisation and recidivism. Qualitative data obtained from process evaluations associated with the included studies and information on cost/resource requirements of the intervention will be collected to provide context for the findings.

For the purposes of this review, we adopt the World Health Organization (WHO) definition of health: “…a state of complete physical, mental and social well-being and not merely the absence of disease or infirmity” (WHO 1948). With this definition in mind, our secondary health outcomes fall into three broad categories: physical health, mental health and health risk behaviours. To explore the links between health and offending behaviour, we include recidivism as a secondary outcome.

Although we anticipate considerable heterogeneity in outcome measures, under each of the sub-categories below we will select the most frequently reported outcome measure to represent that outcome sub-category in data synthesis. Where the same underlying construct is measured using multiple measures (e.g. health-related quality of life measured by the short form-36 (SF-36) and Symptom Checklist-90 (SCL-90)), we will treat these measures as comparable for the purposes of taking a median effect size.

Where one study provides data on multiple outcomes, each outcome will be considered in the appropriate analysis. Where outcomes are measured at multiple time points, the time point that is measured immediately post-intervention will be the primary measure since this will be most commonly measured in other studies and therefore expected to be the most comparable. Subsequent time points will be considered in assessing the sustainability of interventions. We will consider time points during or within three months of cessation of the intervention to be short-term; time points four to 12 months post-intervention will be considered medium-term, and time points > 12 months' post-intervention will be considered long-term.

3.2.1 Electronic searches

We will search the following electronic databases: •

Cochrane Central Register of Controlled Trials (CENTRAL);

We will also search the Cochrane Public Health Group (CPHG) Specialised Register and the Effective Practice and Organisation of Care (EPOC) Group Specialised Register, and the Campbell Collaboration Social, Psychological, Educational & Criminological Trials Register (C2-SPECTR) bibliography for studies published in 2003 or earlier.

For all electronic searches, the following outline of a search strategy for PubMed will be tailored for each database. Given that relatively few studies have examined health outcomes in ex-prisoners, that interventions may be intended primarily to reduce recidivism (rather than improve health), and that there is no consensus in the literature regarding appropriate terminology to describe service brokerage interventions for this population, the search will not be filtered by intervention terms. Similarly, given that some studies may report health outcomes only incidentally, the search will initially identify studies based on health or recidivism outcomes, although studies that do not report at least one health-related outcome will subsequently be excluded.

3.2.2 Searching other resources

We will attempt to identify grey literature using keyword searches in Google and Google Scholar, searches of government and non-government websites (e.g. WHO, United Nations Office on Drugs and Crime (UNODC), and Correctional Service of Canada), and online clearing houses such as the Lloyd Society's Justice Health Library (thelloydsociety.org/work/current_projects/jhl/) and the Offender Health section of the Australian Indigenous Health Clearinghouse (www.healthinfonet.ecu.edu.au/population-groups/offender-health).

We will search the international clinical trials registry platform (ICTRP) and the ANZ Clinical Trials Registry (ANZCTR) to identify ongoing or planned studies. Potential studies will also be identified through consultation with Review Advisory Group (RAG) members.

We will also handsearch the reference lists of included studies and other relevant papers and handsearch key journals for the past 12 months to identify studies that may not yet be indexed in databases.

3.3.1 Selection of studies

All potential studies identified from the searches will be downloaded into reference management software and duplicates removed. The titles and abstracts of identified studies will be screened independently by two review authors to determine eligibility according to the inclusion and exclusion criteria listed above. Full copies of all eligible papers will be retrieved. When a title or abstract cannot be rejected with certainty, the full text of the article will be obtained for further evaluation. If there is disagreement between the two review authors at any stage, this will be resolved by discussion, and if necessary, consultation with a third review author. Multiple reports related to the same study will be linked together. Studies that appear to be relevant but do not meet the inclusion criteria will be listed in the table of excluded studies with reasons given for exclusion.

3.3.2 Data extraction and management

Data will be extracted independently by two review authors using a data extraction form based on the template provided by the Cochrane Public Health Group. Any disagreements will be resolved by discussion and, if necessary, consultation with a third review author. Study information to be extracted, where available, will include: •

year of publication;

Data from multiple reports of the same study will be collated into one data extraction form pertaining to the study. Data will be entered into Review Manager (RevMan 2011) software and checked for accuracy.

3.3.3 Assessment of risk of bias in included studies

Risk of bias of included studies, with the exception of interrupted time series, will be assessed using the Cochrane EPOC (Effective Practice and Organisation of Care) ‘Risk of bias’ tool for studies with a separate control group. This includes the assessment of sequence generation; allocation concealment; confounding; incomplete outcome data; blinding of participants, personnel and outcome assessors; contamination; selective outcome reporting and other sources of bias.

Risk of bias for interrupted time series designs will be assessed using the Cochrane EPOC ‘Risk of bias’ tool for such designs. This includes the assessment of whether the intervention was independent of other changes, unlikely to affect data collection; and whether the shape of the intervention effect was pre-specified. Also included is the assessment of blinding of participants, personnel and outcome assessors; incomplete outcome data; selective outcome reporting and other sources of bias.

Risk of bias will be assessed independently by two review authors and any discrepancies will be resolved by discussion or consultation with a third review author if necessary.

3.3.4 Measures of treatment effect

Dichotomous outcomes will be reported as mean risk ratios (RR) with 95% confidence intervals (CI). Continuous outcomes will be presented as the difference in mean values with 95% CIs. If studies use different measures for the same outcome, we will use standardised mean difference (SMD) as a relative measure for continuous outcomes, where appropriate. No re-calculations of means will be performed; however, if standard deviations are not reported, they will be derived from the reported standard error of the mean, or 95% CIs using the equations provided in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Ordinal outcome measures may be analysed as either dichotomous or continuous data and reported in the corresponding format described above. Where possible, based on reporting and analysis in primary studies, effect sizes derived from interrupted time series designs will be reported as the change in the level of outcome at the first measurement point after the introduction of the intervention or the change in the slopes of the regression lines (post-intervention minus pre-intervention slope), or both (Ramsay 2003). Either of these effect sizes will be considered as evidence of intervention effect, if deemed significant. Qualitative process data will be used to assess intervention intensity and provide context for the findings.

3.3.5 Unit of analysis issues

3.3.6 Dealing with missing data

For missing summary data, we will contact study investigators for clarification, or if possible, we will estimate missing summary data using other information provided in the publication. We will carry out analyses, as far as possible, on an intention-to-treat basis, analysing participants in the group to which they were allocated regardless of whether or not they received the allocated intervention. It is also recognised that not all intervention group participants may receive the same ‘dosage’ of intervention; accordingly, we will conduct an intention-to-treat analysis wherever possible.

3.3.7 Assessment of heterogeneity

Heterogeneity will initially be considered in terms of meaningful variation in the participants, interventions and outcomes measured in included studies, sometimes known as clinical heterogeneity. Methodological heterogeneity will also be considered in terms of the variation in the study designs of included studies. If meta-analyses are appropriate, we will conduct a visual assessment of all forest plots and generate Chi² and I² statistics to quantify the level of statistical heterogeneity, which may be a consequence of clinical or methodological heterogeneity or both. We will not combine results from different types of study designs together in a meta-analysis. We expect considerable heterogeneity due to the broad scope of this review, and we plan to group studies by population, interventions and outcomes where it might be more meaningful to do so, based on clinical heterogeneity. We also plan to use a random-effects model for meta-analyses to incorporate likely statistical heterogeneity. If we find that I² < 30 (along with a high P value from the Chi² test), we will consider using a fixed-effect model as the primary model. Depending on the number of available studies, we will explore potential causes of heterogeneity, based on the pre-specified subgroup analyses listed below. Caution will be taken in the interpretation of results with a high level of unexplained heterogeneity.

3.3.8 Assessment of reporting biases

If more than 10 studies are identified that report the same outcome of interest, we will explore publication bias using funnel plots to assess the relationship between effect size and study precision. If meta-analyses have been conducted and we are concerned about small study effects, we will compare the fixed- and random-effects estimate of the intervention effect in a sensitivity analysis to identify the level of impact caused by different effect estimates in small studies. A random-effects meta-analysis weights the studies more equally than a fixed-effect analysis, therefore in the case where the intervention effect is more beneficial in smaller studies, the random-effects estimate will be expected to be more beneficial than the fixed-effect estimate (Poole 1999). If we find that there is a large difference between the random-effects estimate and the fixed-effect estimate, we will examine whether there are consistent differences between the smaller and larger studies in risk of bias, population or intervention (according to our pre-specified groupings identified in the Data synthesis and Subgroup analysis and investigation of heterogeneity sections) to determine possible causes and to decide on the most appropriate way to present studies in meta-analyses. For example, if the larger studies were generally assessed to be at a lower risk of bias and were conducted in circumstances that reflect the more typical or appropriate use of the intervention in practice, meta-analyses may be restricted to those larger studies.

3.3.9 Data synthesis

Where studies are sufficiently similar in terms of population, intervention and comparisons, pooled estimates of effectiveness will be generated for similar outcomes, as appropriate. This will be conducted by meta-analysing the data using a random-effects model as the default method where I² > 30 (see Assessment of heterogeneity).

For analysis, studies will be grouped by intervention type. While this will depend on what is found in included studies, this will most likely be based on the point of delivery or the timing of the intervention (in custody (i.e. pre-release), post-release, both pre- and postrelease components) and whether or not the intervention is ‘tailored’ or personalised for individual circumstances, characteristics, needs, or a combination of these.

Within each intervention type, studies will be grouped by study design with RCTs and cluster RCTs in one group, quasi-RCTs and controlled before-and-after studies in a second group and interrupted time series in a third group. Outcomes will be reported in the review according to the primary and secondary review outcomes and within those categories, will be grouped as follows: substance use, health-related quality of life, physical health, mental health, health service utilisation, sexual risk behaviour and recidivism.

Qualitative data will be used to provide context for the findings and information about intervention implementation. Where appropriate, this will be used to guide risk of bias assessment as well as assessment of the intensity of interventions. If sufficient information related to the implementation of interventions in included studies is available, this will be tabulated separately in the review alongside information about cost/resource requirements to assist readers in their assessment of applicability and transferability.

For each study, we will capture whether or not outcomes are reported by any of the socio-demographic characteristics known to be important from an equity perspective based on the PROGRESS-Plus framework. Where outcomes are reported by any of the PROGRESS-Plus factors, we will highlight narratively whether or not the primary authors found differences in the impact of interventions by those factors. Selected factors have been nominated below for subgroup analyses (gender, racial/ethnic minority status).

The main findings of the review will be set out in a ‘Summary of findings' table that will incorporate findings for the primary review outcomes as well as the secondary review outcome, health service utilisation (the hypothesised proximate outcome), along with number of participants and studies. The number of studies reporting at least one adverse outcome will also be reported in the ‘Summary of findings' table; however, due to expected heterogeneity in potential adverse outcomes, this will not be disaggregated by specific adverse outcome type. The overall quality of the body of evidence for primary outcomes will be summarised at the outcome level according to the GRADE criteria: study limitations, inconsistency, imprecision, indirectness and publication bias.

3.3.10 Subgroup analysis and investigation of heterogeneity

Subject to data availability, we will conduct the following subgroup analyses: 1.

demographic characteristics: does the treatment effect differ as a function of (a) age (< 25 years vs. ≥ 25 years), (b) gender (male vs. female), or (c) racial/ethnic minority group status (minority vs. not, recognising the limitations of aggregating diverse cultural groups)?

These subgroup analyses will be applied to our two primary outcomes and one secondary outcome (health service utilisation) as the hypothesised ‘proximate’ outcome. Each analysis is comparing only two subgroups (based on derived binary exposure variables), so we will examine differences between subgroups by inspection of the CIs for the summary estimates in the two groups, where non-overlapping CIs will indicate a statistically significant difference between the summary estimate in each group.

3.3.11 Sensitivity analysis

Studies judged to be at high risk of bias will be excluded in a sensitivity analysis. Studies where participation in the intervention was mandatory (vs. voluntary) will be excluded in a second sensitivity analysis. If meta-analyses have been conducted and we are concerned about small study effects, we will compare the fixed- and random-effects estimate of the intervention effect in a third sensitivity analysis. All sensitivity analyses will be conducted on our two primary outcomes and one secondary outcome, health service utilisation, as the hypothesis ‘proximate’ outcome.