Screening programmes for helping mental health professionals to detect violent victimisation in people with severe mental illness

  • Protocol
  • Intervention

Authors


Abstract

This is the protocol for a review and there is no abstract. The objectives are as follows:

To review the evidence for the effectiveness of screening programmes to improve health professionals' detection of, and response to, violent victimisation in people with severe mental illness. More specifically, this review aims to examine the effectiveness of the following interventions.

  1. Screening programmes that aim to improve health professionals' detection of victimisation among people with severe mental illness, followed by referral to appropriate external specialist services.

  2. Screening programmes that aim to improve health professionals' detection of victimisation among people with severe mental illness, followed by interventions within these healthcare settings to reduce the adverse health and social outcomes of this victimisation.

Background

Description of the condition

The definition of severe mental illness is based on diagnosis, duration and disability (NIMH 1987) and includes diagnoses such as schizophrenia (and related disorders), bipolar disorder and affective psychoses. The duration of severe mental illness is defined as at least two years and disability is defined as resulting in considerable impairment in daily functioning (NIMH 1987).

Violent crime is defined as any physical or sexual assault, robbery or attempted robbery, or threats of violence. People with severe mental illness are at a higher risk than the general population of being victims of all forms of violent crime, including domestic violence (perpetrated by partner or family members) and non-domestic violence (perpetrated by strangers or acquaintances) (Choe 2008; Maniglio 2009; Khalifeh 2010; Trevillion 2013). People with severe mental illness are more than 11 times more likely to report experiencing violent victimisation in the previous year than the general population (Teplin 2005). Around one-third of people with severe mental illness have experienced violence in the preceding year (Maniglio 2009).

Recent reviews have found that, compared to the general population, women with severe mental illness are at a greater risk of some types of violent victimisation than men with severe mental illness (Khalifeh 2010; Trevillion 2013). Moreover, people with severe mental illness who have experienced childhood abuse, who are homeless or who abuse substances are at particularly high risk of violent and repeat victimisation (Goodman 1997; Goodman 2001; Ehrensaft 2003; Bebbington 2011).

Violent victimisation among people with severe mental illness is shown to be associated with physical health problems, exacerbation of existing psychiatric symptoms, increased service use and hospitalisation, and poorer functioning and quality of life (Goodman 1997; Neria 2005; Mueser 2008). Victimisation is also found to increase the likelihood of re-victimisation and perpetration of violence among people with severe mental illness (Lam 1998; Hiday 2002; Swanson 2002). Despite these findings, studies have found low levels of routine enquiry about victimisation by mental health professionals, with detection rates of 10% to 30% reported in the literature (Howard 2010). Mental health professionals report low levels of knowledge about domestic violence support services and inadequate referral resources (Nyame 2013).

Description of the intervention

This review will examine interventions aimed at increasing the detection by health professionals of victimisation among people with severe mental illness, followed by either increased referral to external specialist agencies or the provision of appropriate support within the healthcare setting where the screening was conducted.

How the intervention might work

In high-income countries, most people with severe mental illness come to the attention of mental healthcare professionals. Interventions for victims of violence within these settings would have the following aims: (a) to identify people who have been victims of violence (b) to make onward referrals for victims where this is needed and wanted, for example, to advocacy services (c) to provide appropriate support for victims within the mental healthcare setting itself, for example, psychological interventions to address post-traumatic stress, or interventions aimed at addressing risk factors for re-victimisation such as substance misuse. The ultimate aim of these interventions would be to decrease the risk of re-victimisation and improve victims’ health and quality of life (WHO 2013). The existing evidence on interventions within healthcare settings to identify and support victims of violence is largely based in primary and antenatal care settings, with a focus on intimate partner violence (IPV). In those settings, routine screening for IPV increases identification, but there is insufficient evidence that this leads to increased specialist referrals, or to improved health outcomes for victims (Taft 2013; Feder 2009). These findings relate to universal screening of asymptomatic women in primary or obstetric healthcare settings. Universal screening may be appropriate for those presenting with mental health problems within primary or antenatal setting, and to those presenting to mental healthcare services, since this population is at increased risk of IPV and other forms of violence (Oram 2013; Hughes 2012). This is in line with recent World Health Organization (WHO) guidelines, which recommend routine enquiry for IPV in women presenting with depression (WHO 2013). Whether screening is universal or targeted, healthcare professionals need training to help them identify and respond to IPV safely and effectively. In primary care settings, there is evidence that training programmes linked with referral pathways can increase identification of IPV and subsequent referrals to domestic violence advocacy services (Feder 2011). There is preliminary evidence that similar interventions, which comprise training for health professionals, the introduction of a screening tool, and the integration of advocacy workers into mental healthcare teams, are effective at improving detection and external referral in mental healthcare settings.

There is some evidence that individual psychological treatments (such as trauma-focused cognitive behaviour therapy (CBT)) can reduce the adverse psychological or psychiatric consequences of IPV (Feder 2009; Ramsay 2005). Whilst non-mental healthcare settings would refer victims for psychological treatment where appropriate, secondary mental health services would be expected to provide such treatment internally. Mental health service users are a heterogeneous population, and include those with severe affective disorders, psychotic illnesses, personality disorders and substance misuse problems. Whilst the risk of victimisation is high for all diagnostic groups (Trevillion 2012), psychological interventions may not be equally available to all, and indeed is known to be limited for those with psychotic disorders (The Schizophrenia Commission 2012). However, there is evidence that the adverse psychological effects of victimisation can be addressed in people with schizophrenia and related disorders with individual CBT treatment (Mueser 2008). Therefore, enabling access to these treatments is important for those who screen positive for trauma within mental healthcare settings.

As well as providing specialist psychological treatment, mental healthcare professionals are well-placed to co-ordinate a multi-professional response focused on protecting vulnerable patients from further abuse or violence. In the UK, this is expected to be carried out within the ‘Safeguarding Adults’ framework (Mandelstam 2011). Therefore, screening for victimisation within mental healthcare settings needs to be linked to effective use of ‘Safeguarding’ or similar frameworks for multi-agency responses where appropriate.

In summary, we will focus on the effectiveness of screening interventions that aim to increase the detection of victimisation among people with severe mental illness by healthcare professionals (through the use of universal or targeted screening); followed by either (i) increased referral to external specialist agencies such as advocacy services or domestic violence shelters (ii) the provision of support within mental health services to improve health and outcomes among violence victims; such as the provision of specialist psychological treatments or the use of safeguarding procedures.

Why it is important to do this review

Victimisation among people with severe mental illness is highly prevalent and associated with significant psychosocial morbidity (Walsh 2003; Silver 2005; Teplin 2005). This is a considerable public health problem as it is associated with an increase in pre-existing severe mental illness symptoms and a reduction in overall functioning, in addition to the direct physical and emotional impact of violent victimisation and an increased risk of crime perpetration (Pease 1998; Ratcliffe 1998). Despite the high prevalence of violent victimisation among people with severe mental illness, levels of routine enquiry by mental health professionals about victimisation are low (Howard 2010). Detection is an important first step towards intervention and we aim to assess the effectiveness of screening interventions in improving detection rates of victimisation among people with severe mental illness. The effectiveness of screening programmes in decreasing re-victimisation and improving health outcomes for victims are determined not only by whether more cases are detected, but crucially by whether health professionals respond adequately to disclosures of violence (Feder 2013). We will therefore assess the effectiveness of screening followed by external referral or by the provision of support within the healthcare setting where the screening took place. Whilst there are existing systematic reviews of screening for IPV within primary care or antenatal settings, no past systematic reviews have focused on victimisation interventions for people with severe mental illness or within mental healthcare settings. This review aims to address this gap in the literature. Knowledge of such interventions would be invaluable for mental health clinicians, in addition to informing the design of services and allocation of funds within mental health services.

Objectives

To review the evidence for the effectiveness of screening programmes to improve health professionals' detection of, and response to, violent victimisation in people with severe mental illness. More specifically, this review aims to examine the effectiveness of the following interventions.

  1. Screening programmes that aim to improve health professionals' detection of victimisation among people with severe mental illness, followed by referral to appropriate external specialist services.

  2. Screening programmes that aim to improve health professionals' detection of victimisation among people with severe mental illness, followed by interventions within these healthcare settings to reduce the adverse health and social outcomes of this victimisation.

Methods

Criteria for considering studies for this review

Types of studies

All relevant randomised controlled trials. We will include screening and intervention programmes that aim to improve health professionals' detection of - and response to - violent victimisation in people with severe mental illness. If trials are described as 'double-blind' but imply randomisation, we will include these in a sensitivity analysis (see Sensitivity analysis). If their inclusion does not result in a substantive difference, they will remain in the analyses. If their inclusion does result in important clinically significant, but not necessarily statistically significant differences, we will not add the data from these lower-quality studies to the results of the better trials, but will present such data within a subcategory. We will exclude quasi-randomised studies, such as those allocating by alternate days of the week. Where people are given additional treatments within the crime-related interventions, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the crime-related intervention that is randomised.

Types of participants

  1. Health professionals working in any adult health setting or adult mental health setting.

  2. Adults, however defined, with severe mental illness (schizophrenia or related disorders, including schizophreniform disorder, schizoaffective disorder, affective psychosis and delusional disorder, again, by any means of diagnosis), who have been victims of any form of violent crime in the preceding three years and which is known to have occurred after the onset of mental illness, being treated in any setting. We will only include trials where the majority of participants are people with severe mental illness (however defined).

Types of interventions

1. Intervention

Any screening programme that aims to improve health professionals' detection of (and/or support for and/or referral for support for) violent victimisation in people with severe mental illness. This includes interventions aimed at increasing detection of victimisation, external referral for victims, or the provision of support within the healthcare setting where the screening took place.

2. Control conditions

No intervention, usual care or any other intervention (including another type of screening programme or a screening programme with another type of intervention to prevent re-victimisation).

Types of outcome measures

Primary outcomes

For screening programmes which aim to improve detection followed by external referral, the primary outcomes will be the following.

1. Identification of violence victimisation by health professionals
2. Referrals to external support agencies by healthcare professionals
3. Re-victimisation

For screening programmes which aim to improve detection followed by provision of support within the setting where screening took place, the primary outcomes will be the following.

1. Identification of victimisation by health professionals
2. Re-victimisation
Secondary outcomes

For all screening programmes, secondary outcomes will be the following.

1. Mental health outcomes

1.1 Severity of symptoms of pre-existing mental illness

1.2 Post-traumatic stress

1.3 Substance misuse

1.4 Quality of life

2. Social functioning

2.1 Social impairment

2.2 Employment status (employed/unemployed)

2.3 Work-related activities

2.4 Unable to live independently

2.5 Imprisonment

3. Economic outcomes

3.1 Direct costs

3.2 Indirect costs

3.3 Cost of care

4. Crime perpetration
5. Death - suicide and natural causes
6. Where external referral has been made: uptake of referral by service user
7. 'Summary of findings' table

We will use the GRADE approach to interpret findings (Schünemann 2008) and will use GRADE profiler (GRADEPRO) to import data from RevMan 5.1 (Review Manager) to create 'Summary of findings' tables. These tables provide outcome-specific information concerning the overall quality of evidence from each included study in the comparison, the magnitude of effect of the interventions examined, and the sum of available data on all outcomes we rated as important to patient care and decision making. We aim to select the following main outcomes for inclusion in the 'Summary of findings' table.

1. Identification of victimisation by health professionals

2. Re-victimisation

3. Mental health outcomes

4. Social functioning

5. Economic outcomes

6. Crime perpetration

7. Death: suicide and natural causes

8. Where external referral has been made: uptake of referral by service user

Search methods for identification of studies

Electronic searches

1. Cochrane Schizophrenia Group Trials Register

The Trials Search Co-ordinator will search the Cochrane Schizophrenia Group's Trials Register.

1.1 Title, abstract and indexing terms search

These fields will be searched using the phrase:

[(*crime* or *criminal* or *victim* or *fraud* or *homicide* or *sex offen* or *rape* or *theft* or *assault* or *mugg* or *robb* or *burglar* or *vandalis*) or ((*aggress* or *abus* or *violence* or *batter* or *beat*) AND (*victim* or *crime* or *criminal* or *domestic* or *partner* OR *famil* OR *spouse* or *carer*))]

1.2 Intervention search

The 'health care condition' field will be searched using the phrase:

*crime* or *criminal* or *victim*

The Cochrane Schizophrenia Group's Trials Register is compiled by systematic searches of major databases, handsearches of journals and conference proceedings (see Group Module). Incoming trials are assigned to relevant existing or new review titles.

Searching other resources

1. Reference searching

We will inspect the reference lists of all included studies for further relevant studies.

2. Personal contact

We will contact the first author of each included study for information regarding unpublished trials.

Data collection and analysis

Selection of studies

Review authors RB and HK will independently inspect citations from the searches and identify relevant abstracts. KT will independently re-inspect a random 20% sample to ensure reliability. Where disputes arise, we will acquire the full report for more detailed scrutiny. RB and HK will obtain and inspect full reports of the abstracts meeting the review criteria. Again, KT will re-inspect a random 20% of reports in order to ensure reliable selection. Where it is not possible to resolve disagreement by discussion, we will attempt to contact the authors of the study for clarification.

Data extraction and management

1. Extraction

Review authors RB and HK will extract data from all included studies. In addition, to ensure reliability, LH will independently extract data from a random sample of these studies, comprising 10% of the total. Again, we will discuss any disagreement, document decisions and, if necessary, contact authors of studies for clarification. With remaining problems, PM will help clarify issues and we will document these final decisions. We will extract data presented only in graphs and figures whenever possible, but include only if two review authors independently have the same result. We will attempt to contact authors through an open-ended request in order to obtain missing information or for clarification whenever necessary. If studies are multi-centre, where possible, we will extract data relevant to each component centre separately.

2. Management
2.1 Forms

We will extract data onto standard, simple forms.

2.2 Scale-derived data

We will include continuous data from rating scales only if:

a) the psychometric properties of the measuring instrument have been described in a peer-reviewed journal (Marshall 2000); and
b) the measuring instrument has not been written or modified by one of the trial authors of that particular trial.

Ideally, the measuring instrument should either be i) self-report or ii) completed by an independent rater or relative (not the therapist). We realise that this is not often reported clearly; we will note in 'Description of studies' if this is the case or not.

2.3 Endpoint versus change data

There are advantages of both endpoint and change data. Change data can remove a component of between-person variability from the analysis. On the other hand, calculation of change needs two assessments (baseline and endpoint), which can be difficult in unstable and difficult to measure conditions such as schizophrenia. We have decided primarily to use endpoint data and only use change data if the former are not available.

2.4 Skewed data

Continuous data on clinical and social outcomes are often not normally distributed. To avoid the pitfall of applying parametric tests to non-parametric data, we aim to apply the following standards to all data before inclusion:

a) standard deviations (SDs) and means are reported in the paper or obtainable from the authors;
b) when a scale starts from the finite number zero, the SD, when multiplied by two, is less than the mean (as otherwise the mean is unlikely to be an appropriate measure of the centre of the distribution (Altman 1996);
c) if a scale started from a positive value (such as the Positive and Negative Syndrome Scale (PANSS) (Kay 1986), which can have values from 30 to 210), the calculation described above will be modified to take the scale starting point into account. In these cases skew is present if 2 SD > (S-S min), where S is the mean score and 'S min' is the minimum score.

Endpoint scores on scales often have a finite start and end point and these rules can be applied. Skewed data pose less of a problem when looking at means if the sample size is large (> 200) and we will enter these into the syntheses. We will present skewed endpoint data from studies of fewer than 200 participants as other data within the data and analyses section rather than enter such data into statistical analyses. When continuous data are presented on a scale that includes a possibility of negative values (such as change data), it is difficult to tell whether data are skewed or not. We will present and enter change data into statistical analyses.

2.5 Common measure

To facilitate comparison between trials, we intend to convert variables that can be reported in different metrics, such as days in hospital (mean days per year, per week or per month) to a common metric (e.g. mean days per month).

2.6 Conversion of continuous to binary

Where possible, we will make efforts to convert outcome measures to dichotomous data. This can be done by identifying cut-off points on rating scales and dividing participants accordingly into 'clinically improved' or 'not clinically improved'. It is generally assumed that if there is a 50% reduction in a scale-derived score such as the Brief Psychiatric Rating Scale (BPRS, Overall 1962) or the Positive and Negative Syndrome Scale (PANSS, Kay 1986), this could be considered as a clinically significant response (Leucht 2005; Leucht 2005a). If data based on these thresholds are not available, we will use the primary cut-off presented by the original authors.

2.7 Direction of graphs

Where possible, we will enter data in such a way that the area to the left of the line of no effect indicates a favourable outcome for the crime-related intervention. Where keeping to this makes it impossible to avoid outcome titles with clumsy double-negatives (e.g. 'Not improved') we will report data where the left of the line indicates an unfavourable outcome. We will note this in the relevant graphs.

Assessment of risk of bias in included studies

Again, review authors RB and HK will work independently to assess risk of bias by using criteria described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) to assess trial quality. This set of criteria is based on evidence of associations between overestimate of effect and high risk of bias of the article such as sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting.

If the raters disagree, the final rating will be made by consensus, with the involvement of another member of the review group (KT). Where inadequate details of randomisation and other characteristics of trials are provided, we will contact the authors of the studies in order to obtain further information. We will report non-concurrence in quality assessment, but if disputes arise as to which category a trial is to be allocated, again we will resolve by discussion. We will note the level of risk of bias in both the text of the review and in the 'Summary of findings' table.

Measures of treatment effect

1. Binary data

For binary outcomes we will calculate a standard estimation of the risk ratio (RR) and its 95% confidence interval (CI). It has been shown that RR is more intuitive (Boissel 1999) than odds ratios and that odds ratios tend to be interpreted as RR by clinicians (Deeks 2000). For binary data presented in the 'Summary of findings' table, where possible, we will calculate illustrative comparative risks, instead of the number needed to treat/harm (NNT/H) statistic with its confidence intervals that, while intuitively attractive to clinicians, is problematic, both in its accurate calculation in meta-analyses, and interpretation (Hutton 2009).

2. Continuous data

For continuous outcomes we will estimate the mean difference (MD) between groups. If studies assess the same outcome but measure it in a variety of ways (for example, use different psychometric scales, then we will combine these continuous outcomes using the standardised mean difference (SMD).

Unit of analysis issues

1. Cluster trials

Studies increasingly employ 'cluster randomisation' (such as randomisation by clinician or practice) but analysis and pooling of clustered data poses problems. Firstly, authors often fail to account for intra-class correlation in clustered studies, leading to a 'unit of analysis' error (Divine 1992) whereby P values are spuriously low, confidence intervals unduly narrow and statistical significance overestimated. This causes type I errors (Bland 1997; Gulliford 1999).

Where clustering is not accounted for in primary studies, we will present data in a table, with a (*) symbol to indicate the presence of a probable unit of analysis error. In subsequent versions of this review we will seek to contact first authors of studies to obtain intra-class correlation coefficients (ICCs) for their clustered data and to adjust for this by using accepted methods (Gulliford 1999). Where clustering has been incorporated into the analysis of primary studies, we will present these data as if from a non cluster-randomised study, but adjust for the clustering effect.

We have sought statistical advice and have been advised that the binary data as presented in a report should be divided by a 'design effect'. This is calculated using the mean number of participants per cluster (m) and the ICC (design effect = 1+(m-1)*ICC) (Donner 2002). If the ICC is not reported, it will be assumed to be 0.1 (Ukoumunne 1999).

If cluster studies have been appropriately analysed taking into account ICCs and relevant data documented in the report, synthesis with other studies will be possible using the generic inverse variance technique.

2. Cross-over trials

A major concern of cross-over trials is the carry-over effect. It occurs if an effect (e.g. pharmacological, physiological or psychological) of the treatment in the first phase is carried over to the second phase. As a consequence, on entry to the second phase the participants can differ systematically from their initial state despite a wash-out phase. For the same reason cross-over trials are not appropriate if the condition of interest is unstable (Elbourne 2002). As both effects are very likely in severe mental illness, we will only use data from the first phase of cross-over studies.

3. Studies with multiple treatment groups

Where a study involves more than two treatment arms, if relevant, we will present the additional treatment arms in comparisons. If data are binary we will simply add and combine these within the two-by-two table. If data are continuous we will combine data following the formula in section 7.7.3.8  (Combining groups) of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Where the additional treatment arms are not relevant, we will not use these data.

Dealing with missing data

1. Overall loss of credibility

At some degree of loss to follow-up, data must lose credibility (Xia 2009). We choose that, for any particular outcome, should more than 50% of data be unaccounted for, we will not reproduce these data or use them within analyses. If, however, more than 50% of those in one arm of a study are lost, but the total loss is less than 50%, we will address this within the 'Summary of findings' table/s by downgrading quality. Finally, we will also downgrade quality within the 'Summary of findings' table/s should loss be 25% to 50% in total.

2. Binary

In the case where attrition for a binary outcome is between 0% and 50% and where these data are not clearly described, we will present data on a 'once randomised always analyse' basis (an intention-to-treat (ITT) analysis). Those leaving the study early are all assumed to have the same rates of negative outcome as those who completed, with the exception of the outcome of death and adverse effects. For these outcomes, the rate of those who stay in the study - in that particular arm of the trial - will be used for those who did not. We will undertake a sensitivity analysis to test how prone the primary outcomes are to change when data only from people who complete the study to that point are compared to the ITT analysis using the above assumptions.

3. Continuous
3.1 Attrition

In the case where attrition for a continuous outcome is between 0% and 50%, and data only from people who complete the study to that point are reported, we will reproduce these.

3.2 Standard deviations

If standard deviations (SDs) are not reported, we will first try to obtain the missing values from the authors. If not available, where there are missing measures of variance for continuous data, but an exact standard error (SE) and confidence intervals are available for group means, and either the P value or 't' value are available for differences in mean, we can calculate them according to the rules described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). When only the SE is reported, SDs are calculated by the formula SD = SE * square root (n). Chapters 7.7.3 and 16.1.3 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) present detailed formulae for estimating SDs from P values, t or F values, confidence intervals, ranges or other statistics. If these formulae do not apply, we will calculate the SDs according to a validated imputation method which is based on the SDs of the other included studies (Furukawa 2006). Although some of these imputation strategies can introduce error, the alternative would be to exclude a given study's outcome and thus to lose information. We nevertheless will examine the validity of the imputations in a sensitivity analysis excluding imputed values.

3.3 Last observation carried forward

We anticipate that in some studies the method of last observation carried forward (LOCF) will be employed within the study report. As with all methods of imputation to deal with missing data, LOCF introduces uncertainty about the reliability of the results (Leucht 2007). Therefore, where LOCF data have been used in the trial, if less than 50% of the data have been assumed, we will present and use these data and indicate that they are the product of LOCF assumptions.

Assessment of heterogeneity

1. Clinical heterogeneity

We will consider all included studies initially, without seeing comparison data, to judge clinical heterogeneity. We will simply inspect all studies for clearly outlying people or situations which we had not predicted would arise. When such situations or participant groups arise, we will fully discuss these.

2. Methodological heterogeneity

We will consider all included studies initially, without seeing comparison data, to judge methodological heterogeneity. We will simply inspect all studies for clearly outlying methods which we had not predicted would arise. When such methodological outliers arise we will fully discuss these.

3. Statistical heterogeneity
3.1 Visual inspection

We will visually inspect graphs to investigate the possibility of statistical heterogeneity.

3.2 Employing the I2 statistic

We will investigate heterogeneity between studies by considering the I2 statistic alongside the Chi2 test P value. The I2 statistic provides an estimate of the percentage of inconsistency thought to be due to chance (Higgins 2003). The importance of the observed value of I2 depends on i) the magnitude and direction of effects and ii) the strength of evidence for heterogeneity (e.g. P value from Chi2  test, or a confidence interval for I2). We will interpret an I2 estimate greater than or equal to around 50%, accompanied by a statistically significant Chi2 test, as evidence of substantial levels of heterogeneity (section 9.5.2 - Higgins 2011). When substantial levels of heterogeneity are found for the primary outcome, we will explore the reasons for heterogeneity (Subgroup analysis and investigation of heterogeneity).

Assessment of reporting biases

1. Protocol versus full study

Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results. These are described in section 10.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will try to locate protocols for the included randomised trials. If the protocol is available, we will compare the outcomes in the protocol and in the published report. If the protocol is not available, we will compare the outcomes listed in the methods section of the trial report with the results actually reported.

2. Funnel plot

Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997). As mentioned above, these are described in section 10 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We are aware that funnel plots may be useful in investigating reporting biases but are of limited power to detect small-study effects. We will not use funnel plots for outcomes where there are 10 or fewer studies, or where all studies are of similar sizes. In other cases, where funnel plots are possible, we will seek statistical advice in their interpretation.

Data synthesis

We understand that there is no closed argument for preference for the use of fixed-effect or random-effects models. The random-effects method incorporates an assumption that the different studies are estimating different, yet related, intervention effects. This often seems to be true to us and the random-effects model takes into account differences between studies even if there is no statistically significant heterogeneity. There is, however, a disadvantage to the random-effects model. It puts added weight onto small studies, which often are the most biased ones. Depending on the direction of effect these studies can either inflate or deflate the effect size. We choose the random-effects model for all analyses. The reader is, however, able to choose to inspect the data using the fixed-effect model.

Subgroup analysis and investigation of heterogeneity

1. Subgroup analyses
1.1 Primary outcomes

We propose to perform subgroup analyses by gender and by type of crime (e.g. non-domestic versus domestic violence).

1.2 Clinical state, stage or problem

We propose to undertake this review and provide an overview of the effects of the crime-related intervention for people with severe mental illness in general. In addition, however, we will try to report data on subgroups of people in the same clinical state, stage and with similar problems.

1.3 Duration of measurement

All outcomes will be divided into short term (less than six months), medium term (seven to 12 months) and long term (over one year) and we propose to perform subgroup analyses by these durations.

2. Investigation of heterogeneity

If inconsistency is high, we will report this. First, we will investigate whether data have been entered correctly. Second, if data are correct, we will visually inspect the graph and successively remove outlying studies to see if homogeneity is restored. For this review we have decided that should this occur with data contributing no more than around 10% of the total weighting to the summary finding, we will present the data. If not, we will not pool the data and discuss the issues. We know of no supporting research for this 10% cut-off but are investigating use of prediction intervals as an alternative to this unsatisfactory state.

When unanticipated clinical or methodological heterogeneity are obvious, we will simply state hypotheses regarding these for future reviews or versions of this review. We do not anticipate undertaking analyses relating to these.

Sensitivity analysis

1. Risk of bias

We will analyse the effects of excluding trials that are judged to be at high risk of bias across one or more of the domains of randomisation (implied as randomised with no further details available), allocation concealment, blinding and outcome reporting for the meta-analysis of the primary outcome. If the exclusion of trials at high risk of bias does not substantially alter the direction of effect or the precision of the effect estimates, then we will include data from these trials in the analysis. We aim to include trials in a sensitivity analysis if they are described in some way as to imply randomisation. For the primary outcomes we will include these studies and if there is no substantive difference when the implied randomised studies are added to those with better description of randomisation, then we will employ all data from these studies.

2. Assumptions for lost binary data

Where assumptions have to be made regarding people lost to follow-up (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumptions and when we use data only from people who complete the study to that point. If there is a substantial difference, we will report the results and discuss them but will continue to employ our assumption.

Where assumptions have to be made regarding missing SD data (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumption/s and when we use data only from people who complete the study to that point. We will undertake a sensitivity analysis to test how prone the results are to change when completer-only data are compared to the imputed data using the above assumption. If there is a substantial difference, we will report the results and discuss them but will continue to employ our assumption.

4. Imputed values

We will also undertake a sensitivity analysis to assess the effects of including data from trials where we used imputed values for ICCs in calculating the design effect in cluster-randomised trials.

If substantial differences are noted in the direction or precision of effect estimates in any of the sensitivity analyses listed above, we will not pool data from the excluded trials with the other trials contributing to the outcome, but will present them separately.

5. Fixed-effect and random-effects

We will synthesise all data using a random-effects model, however, we will also synthesise data for the primary outcome using a fixed-effect model to evaluate whether this alters the significance of the results. If the results differ when using the fixed-effect model compared to random-effects, we will exclude the results of the smaller studies. However, this will only be done if the larger studies were conducted with more methodological rigour or conducted in circumstances more typical of the use of the intervention.

Acknowledgements

The Cochrane Schizophrenia Group Editorial Base in Nottingham produces and maintains standard text for use in the Methods section of their reviews. We have used this text as the basis of what appears here and adapted it as required. The search terms were developed by the Trial Search Co-ordinator of the Cochrane Schizophrenia Group, Samantha Roberts, and the contact author of this protocol (RB). We would also like to thank Martin Downes for his helpful feedback on an earlier draft of the protocol.

Contributions of authors

Rohan Borschmann - helped write the protocol, contributed to formulating searches, study selection, data extraction and writing the review.
Hind Khalifeh - proposed the review, helped write the protocol, contributed to study selection and data extraction, and helped write the review.
Kylee Trevillion - helped write the protocol, contributed to study selection and writing the review.
Louise Howard - helped write the protocol, provided statistical advice and helped write the review.
Paul Moran - helped write the protocol, provided statistical advice and helped write the review.

Declarations of interest

Rohan Borschmann - none known.
Hind Khalifeh - none known.
Kylee Trevillion - none known.
Louise Howard is a member of the National Institute for Health and Clinical Excellence (NICE) and the Social Care Institute for Excellence (SCIE) guideline development group on guidelines for preventing domestic violence and a member of the World Health Organization (WHO) guideline and development group on preventing violence against women. She is the Principal Investigator on a National Institute for Health Research (NIHR) Programme Grant for Applied Research ('Improving the healthcare response to domestic violence'; RP-PG-0108-10084) and the joint lead applicant on an NIHR Policy Research Programme grant ('Optimising identification, referral and care of trafficked people within the NHS'; PR-IP-06-11-10011).
Paul Moran - none known.

Sources of support

Internal sources

  • King's College London, UK.

    KT, LM and PM were supported by King's College London in the form of a salary.

  • University College London, UK.

    HK was supported by University College London in the form of a salary.

External sources

  • Big Lottery, UK.

    RB was funded by a Big Lottery project grant entitled "Mental Health and Justice: Making it a Reality" (Chief Investigator: PM; Grant reference number: C247A1198).

  • National Institute for Health Research (NIHR), UK.

    LMH and KT were funded by a National Institute for Health Research (NIHR) Programme Grant for Applied Research (PI: LMH; grant no: RP-PG-0108-10084).

  • Biomedical Research Centre (BRC), UK.

    LMH was part-funded by the BRC.

  • Medical Research Council (MRC), UK.

    HK was funded by an MRC Population Health Sciences Fellowship (ref: G0802432)

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