Lurasidone versus placebo for schizophrenia
This is the protocol for a review and there is no abstract. The objectives are as follows:
To review the effects of lurasidone compared with placebo for people with schizophrenia.
Description of the condition
Schizophrenia is a psychiatric disorder that is characterised by psychotic symptoms, including hallucinations, delusions, amotivation, changes in affect and cognitive deficits. For most people onset is at adolescence or early adulthood with a variable course of illness - 14% to 20% of people with schizophrenia recover fully from an initial episode (NICE 2009); however, the majority experience relapse and a remitting course (Nadeem 2004) and many people experience some decline in social functioning over time. Mortality amongst people with schizophrenia is approximately 50% above the general population, partly related to high suicide rates, violent deaths and increased risk of physical health problems (NICE 2009).
There is a 1% chance of developing schizophrenia over a lifetime (NICE 2009). The causes of schizophrenia are unclear and are likely to involve the interaction of multiple factors (Broome 2005); however, there is an increased risk of developing the disorder in those with affected relatives (Gottesman 1991). Antipsychotic medication remains the mainstay of treatment for schizophrenia, and are broadly classified as first generation including chlorpromazine, haloperidol, sulpiride and zuclopenthixol and second generation including clozapine, olanzapine, risperidone, amisulpiride, aripiprazole and lurasidone. The heterogeneity of second generation antipsychotics is considerable (Davis 2003), however, the distinction from first generation agents is referred to in clinical guidelines (NICE 2009). The effects of these drugs on the natural history of the disorder have been brought into question in recent years (Jablensky 2000).
Description of the intervention
Lurasidone is a new antipsychotic, approved by the US Food and Drug Administration (FDA) for the treatment of schizophrenia in adults in October 2008. As well as treating positive symptoms of schizophrenia, such as delusions and hallucinations, it is also thought to treat the cognitive deficits and memory problems associated with schizophrenia. It is reported to be well-tolerated in terms of side-effects with minimal effects on body weight, glucose tolerance and lipid profiles (Citrome 2011). The most commonly reported adverse effects with lurasidone are akathisia (sensations of inner restlessness - an inability to sit still or remain motionless) (15%), nausea (12%) and sedation (12%) (Samalin 2011).
Recommended dosing schedules for lurasidone range from 40 to 160 mg per day in a single dose. Its clinical use was launched in the USA in February 2011; it is also available in Puerto Rico. In addition, it has been accepted for review by Health Canada and there are phase III clinical trials ongoing in the United Kingdom and European Union. Lurasidone is a relatively expensive antipsychotic with the average price of a 30-day supply quoted as USD $475.98 (Nolan 2012).
How the intervention might work
Lurasidone is classified as a benzisothiazol derivative. Its action is most similar to risperidone and paliperidone and it is thought to be mediated through a combination of central dopamine type 2 and serotonin type 2 receptor antagonism. Its most prominent pharmacological property is a strong affinity at the 5HT7 receptor (Nolan 2012). Lurasidone is metabolised primarily in the liver via the cytochrome P450 3A4 pathway thus use of strong inhibitors or inducers of cytochrome P450 are contraindicated for concomitant use with lurasidone. The drug has two active metabolites, however, most of the pharmacological action is derived from the primary drug (Hussar 2011).
Why it is important to do this review
Lurasidone is a relatively new antipsychotic medication. It is marketed as having a different mechanism of action with less metabolic side effects and therefore. lower associated iatrogenic morbidity compared with other antipsychotics. This makes it both clinically and economically important to accurately review the positive and negative effects of this new to the market antipsychotic agent. This is an initial review which will look at the available evidence for the efficacy of this novel agent, compared with placebo, for the treatment of schizophrenia.
To review the effects of lurasidone compared with placebo for people with schizophrenia.
Criteria for considering studies for this review
Types of studies
All relevant randomised controlled trials. If a trial is described as 'double blind' but implies randomisation, we will include such trials 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 concurrent with lurasidone or placebo, we will only include data if the adjunct treatment is on an 'as required' basis and is evenly distributed between groups and it is only the treatment with lurasidone and placebo that is randomised. We will exclude trials where adjunctive medication is used regularly. Randomised cross-over studies are eligible, but only data up to the point of first cross-over because of the instability of the problem behaviours and the likely carry-over effects of all treatments.
Types of participants
Adults, however defined, with schizophrenia or related disorders, including schizophreniform disorder, schizoaffective disorder and delusional disorder, again, by any means of diagnosis.
We are interested in making sure that information is as relevant to the current care of people with schizophrenia as possible so propose to clearly highlight the current clinical state (acute, early post-acute, partial remission, remission) as well as the stage (prodromal, first episode, early illness, persistent) and as to whether the studies primarily focused on people with particular problems (for example, negative symptoms, treatment-resistant illnesses).
Types of interventions
Any dose/ form of application compared with placebo.
Types of outcome measures
We will group outcomes into acute (up to one week), short term (up to 12 weeks), medium term (13 to 26 weeks) and long term (more than 26 weeks).
1. Relapse (as defined in the individual studies) - long term
1.2 Natural cause.
2. Relapse (as defined in the individual studies)
3. Global state
3.1 Poor compliance with study protocol.
3.2 Needing additional antipsychotic medication.
3.3 Needing additional benzodiazepines.
3.4 Average change score in global state.
3.5 Average endpoint score in global state.
4. Mental state
4.1 Clinically important change in general mental state.
4.2 Average endpoint general mental state score.
4.3 Average change in general mental state scores.
4.4 Clinically important change in specific symptoms.
4.5 Average endpoint specific symptom score.
4.6 Average change in specific symptom scores.
5. General functioning
5.1 Clinically important change in general functioning.
5.2 Average endpoint general functioning score.
5.3 Average change in general functioning scores.
5.4 Clinically important change in specific aspects of functioning.
5.5 Average endpoint specific aspects of functioning.
5.6 Average change in specific aspects of functioning.
6.1 Clinically important change in general behaviour.
6.2 Average endpoint general behaviour score.
6.3 Average change in general behaviour scores.
6.4 Clinically important change in specific aspects of behaviour.
6.5 Average endpoint specific aspects of behaviour.
6.6 Average change in specific aspects of behaviour.
7. Adverse effects
7.1 Clinically important general adverse effects.
7.2 Average endpoint general adverse effect score.
7.3 Average change in general adverse effect score.
7.4 Clinically important specific adverse effects.
7.5 Average endpoint specific adverse effects.
7.6 Average change in specific adverse effects.
8. Sevice Utilisation
8.1 Hospital admission.
8.2 Length of stay.
8.3 Utilisation of outpatient resources (as defined in individual studies).
8.4 Mental Health Act assessments.
8.5 Accident and Emergency attendance.
9. Satisfaction with treatment
9.1 Leaving the study early (due to any reason, inefficacy and adverse events).
9.2 Recipient of care not satisfied with treatment.
9.3 Recipient of care average satisfaction score.
9.4 Recipient of care average change in satisfaction scores.
9.5 Carer not satisfied with treatment.
9.6 Carer average satisfaction score.
9.7 Carer average change in satisfaction scores.
10. Quality of life
10.1 Clinically important change in quality of life.
10.2 Average endpoint quality of life score.
10.3 Average change in quality of life scores.
10.4 Clinically important change in specific aspects of quality of life.
10.5 Average endpoint specific aspects of quality of life.
10.6 Average change in specific aspects of quality of life.
11. Cognitive functioning
11.1 Clinically important change in cognitive functioning.
11.2 Average endpoint cognitive functioning score.
11.3 Average change in cognitive functioning scores.
11.4 Clinically important change in specific aspects of cognitive functioning.
11.5 Average endpoint specific aspects of cognitive functioning.
11.6 Average change in specific aspects of cognitive functioning.
12. Economic outcomes
12.1 Direct costs (as defined in individual studies).
12.2 Indirect costs (as defined in individual studies).
12.3 Cost-effectiveness (as defined in individual studies).
13. 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 rate as important to patient-care and decision making. We aim to select the following main outcomes for inclusion in the 'Summary of findings' table:
Relapse (as defined in individual studies) - long term.
Clinically important change in general functioning - short term.
Clinically important specific adverse effects - weight gain - long term.
Clinically important specific adverse effects - glucose tolerance - long term.
Clinically important specific adverse effects - sedation - short term.
Clinically important specific adverse effects - akathisia - short term.
Average change in cognitive functioning scores - long term.
Search methods for identification of studies
Cochrane Schizophrenia Group Trials Register
1. The Trials Search Co-ordinator will search the Cochrane Schizophrenia Group’s Trials Register using the terms:
[((*Lurasidone* OR *SM?13496* OR *SM-13496* OR *SM13496* OR *MK 3756* OR *SMP 13496*) AND *placebo*) in title, abstract and index terms of REFERENCE or interventions of STUDY)].
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 references 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 author LD will independently inspect citations from the searches and identify relevant abstracts. A random 20% sample will be independently re-inspected by review author SS to ensure reliability. Where disputes arise, the full report will be acquired for more detailed scrutiny. Full reports of the abstracts meeting the review criteria will be obtained and inspected by LD. Again, a random 20% of reports will be re-inspected by SS 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
Review author LD will extract data from all included studies. In addition, to ensure reliability, SS will independently extract data from a random sample of these studies, comprising 10% of the total. Again, any disagreement will be discussed, decisions documented and, if necessary, we will contact authors of studies for clarification. With any remaining problems HJ will help clarify issues and these final decisions will be documented. Data presented only in graphs and figures will be extracted whenever possible, but included only if both 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.
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 trialists for that particular trial.
Ideally, the measuring instrument should either be i. a self-report or ii. completed by an independent rater or relative (not the therapist). We realise that this is not often reported clearly, in 'Description of studies' we will note 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. Endpoint and change data will be combined in the analysis as we will use mean differences (MD) rather than standardised mean differences (SMD) throughout (Higgins 2011).
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 endpoint data from studies of less than 200 participants will be entered in additional tables rather than into an analysis. However, skewed data pose less of a problem when looking at means if the sample size is large and skewed endpoint data from trials with over 200 participants will be entered into syntheses.
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. Skewed change data will be entered into syntheses.
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, efforts will be made 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 PANSS, 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 treatment with lurasidone. 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. This will be noted in the relevant graphs.
Assessment of risk of bias in included studies
Again review authors LD and SS 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. Where inadequate details of randomisation and other characteristics of trials are provided, we will contact authors of the studies in order to obtain further information. Non-concurrence in quality assessment will be reported, but if disputes arise as to which category a trial is to be allocated, again, we will resolve by discussion.
The level of risk of bias will be noted 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 as the Number Needed to Treat/Harm (NNT/H) statistic with its confidence intervals is intuitively attractive to clinicians but is problematic both in its accurate calculation in meta-analyses and interpretation (Hutton 2009).
2. Continuous data
For continuous outcomes, we will estimate MD between groups. We prefer not to calculate effect size measures (SMD). However, if scales of very considerable similarity are used, we will presume there is a small difference in measurement, and we will calculate effect size and transform the effect back to the units of one or more of the specific instruments.
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 of the first phase of cross-over studies.
3. Studies with multiple treatment groups
Where a study involves more than two treatment arms, if relevant, the additional treatment arms will be presented in comparisons. If data are binary, these will be simply added and combined within the two-by-two table. If data are continuous, we will combine data following the formula in section 220.127.116.11 (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 of 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 down-rating quality. Finally, we will also downgrade quality within the Summary of Findings table/s should loss be 25-50% in total.
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 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 testing how prone the primary outcomes are to change when data only from people who complete the study to that point are compared to the intention to treat analysis using the above assumptions.
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 (SDs)
If 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 available for group means, and either 'P' value or 't' value available for differences in mean, we can calculate them according to the rules described in the Cochrane Handbook for Systemic 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 Systemic 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, these will be fully discussed.
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 these will be fully discussed.
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
Heterogeneity between studies will be investigated by considering the I2 method alongside the Chi2 'P' value. The I2 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. magnitude and direction of effects and ii. strength of evidence for heterogeneity (e.g. 'P' value from Chi2 test, or a confidence interval for I2). An I2 estimate greater than or equal to around 50% accompanied by a statistically significant Chi2 statistic, will be interpreted as evidence of substantial levels of heterogeneity (Section 9.5.2 - Higgins 2011). When substantial levels of heterogeneity are found in the primary outcome, we will explore 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 Intervention (Higgins 2011). We will try to locate protocols of included randomised trials. If the protocol is available, outcomes in the protocol and in the published report will be compared. If the protocol is not available, outcomes listed in the methods section of the trial report will be compared with actually reported results.
2. Funnel plot
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997). These are again 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.
We understand that there is no closed argument for preference for 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 fixed-effect model for all analyses. The reader is, however, able to choose to inspect the data using the random-effects model.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses
1.1 Primary outcomes
We do not anticipate any subgroup analysis.
1.2 Clinical state, stage or problem
We propose to undertake this review and provide an overview of the effects of lurasidone for people with schizophrenia 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.
2. Investigation of heterogeneity
If inconsistency is high, this will be reported. First, we will investigate whether data have been entered correctly. Second, if data are correct, the graph will be visually inspected and outlying studies will be successively removed to see if homogeneity is restored. For this review, we decided that should this occur with data contributing to the summary finding of no more than around 10% of the total weighting, data will be presented. If not, data will not be pooled and issues will be discussed. 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.
1. Implication of randomisation
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 all data will be employed 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 results and discuss them but will continue to employ our assumption.
Where assumptions have to be made regarding missing SDs 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 studies which presented these data. A sensitivity analysis will be undertaken testing how prone results are to change when completer-only data are compared with the imputed data using the above assumption. If there is a substantial difference, we will report results and discuss them but will continue to employ our assumption.
3. 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 data from these trials will be included in the analysis.
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 ICC 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- and random-effects
All data will be synthesised using a fixed-effect model, however, we will also synthesise data for the primary outcome using a random-effects model to evaluate whether this alters the significance of the results.
Thanks to Professor Clive Adams, Lindsey Air and Samantha Roberts, Claire Irving and the editorial team at the Nottingham University Cochrane Schizophrenia Group for their support in completing this review. We would also like to thank and acknowledge the contribution and advice from Hannah Jones during the writing of this protocol.
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.
Contributions of authors
Lorna Donnelly - protocol development, data extraction, analysis, writing review.
Stephanie Sampson - protocol development, data extraction, analysis, writing review.
Declarations of interest
Lorna Donnelly - none.
Stephanie Sampson - none.
Sources of support
Norfolk and Suffolk Foundation Trust, UK.
Special Interest day of primary author granted to Cochrane Schizophrenia Group
National Institute for Health Research (NIHR), UK.
UK Cochrane Collaboration Programme Grant 2011