Description of the condition
Schizophrenia is a chronic mental health condition that is associated with significant morbidity and mortality. It is characterised by psychotic symptoms, alterations in motivation and volition, neurochemical imbalances and irregularities of emotion. The diagnosis of this condition is based on clinical interview with the patient and observation of their mental state and comparison of this with diagnostic criteria, such as the ICD-10 (International Classification of Diseases) (Jablensky 2010).
Life-time prevalence of schizophrenia is estimated to be 0.33% to- 0.66% and the incidence is somewhere between 10 and 22 per 100,000 (Jablensky 1992). Schizophrenia commonly presents in early adulthood or late adolescence. Men have an earlier age of onset than women, and also seem to have a worse prognosis (Picchioni 2007). The incidence of schizophrenia is not uniform across different research sites but it is present and identifiable throughout the world (McGrath 2006).
Schizophrenia is estimated to reduce lifespan by 10 to 15 years, partly due to poor access to health care, stigma and increase in co-morbid physical health problems (Van Os 2009). The National Confidential Enquiry (NCI 2012) states schizophrenia leads to an increased risk of suicide compared to the general population and also contributes to an increase in overall mortality. Schizophrenia causes more loss of life-years than some cancers and physical illnesses (WHO 2004). Given that it is a disabling condition that contributes to a high burden of illness to the person suffering from it and carers, it is of vital importance to investigate further its causes and effective treatment options.
Description of the intervention
Antipsychotic medication has remained the mainstay of treatment for schizophrenia ever since chlorpromazine was introduced. Zuclopenthixol is one of the earlier typical antipsychotics, first introduced in 1962 and has remained in use. Clinicians seem to find it convenient to use and patients seem to tolerate it reasonably well (Owens 2012). Zuclopenthixol is commonly known by the name of Clopixol, although this usage in clinical parlance can lead to confusion because of the different formulations that exist. Essentially zuclopenthixol is available in three formulations. Zuclopenthixol dihydrochloride is the tablet form and has a half life of approximately 20 hours (Lundbeck 2011). Zuclopenthixol acetate (Acuphase) is an option if it is anticipated that a patient will be disturbed over a longer time period (NICE 2005) and is also used as the initial medication prior to initiating longer acting depot antipsychotic treatments. Acuphase reaches a peak plasma concentration at 36 hours. The longer-acting zuclopenthixol decanoate is used as a depot preparation and has the convenience in terms of frequency of administering which can vary between weekly and monthly administration. Zuclopenthixol decanoate has a half life of 19 days (Lundbeck 2011).
How the intervention might work
Antipsychotic drugs, especially the earlier generations are hypothesised to work by blocking dopamine receptors in the brain, especially around the mesolimbic dopamine pathway. There are several theories relating to dopamine as the neurotransmitter implicated in symptom causation. As a neurotransmitter, dopamine is involved in four main pathways in the brain. The mesolimbic and mesocortical pathways are related to salience of perceptions, motivation and reward. These pathways are deranged in schizophrenia and are the target of many antipsychotics (Kapur 2005). The nigrostriatal pathway is involved in the control of movement and can be affected by some, especially typical, antipsychotics leading to movement disorders as a common side effect (Miyamoto 2005). The final pathway is the tuberoinfundibular pathway that is involved in prolactin secretion. Hence, many antipsychotics can interfere with prolactin metabolism and lead to hyperprolactinaemia (Owens 2012).
Zuclopenthixol belongs to a class of chemical compounds called the thioxanthenes. These all have a common three-ringed structure and include zuclopenthixol and fluphentixol. Zuclopenthixol primarily works by blocking the D2 receptors but has also been shown to have serotonergic-blocking properties, a high affinity for alpha-adrenoreceptors and some antihistamine properties (Lundbeck 2011). The side effects of zuclopenthixol use are common to many antipsychotics and include sedation, extra pyramidal side effects and it may cause some abnormalities of liver function.
Why it is important to do this review
Zuclopenthixol is a widely used drug around the world. There have been numerous studies over the years comparing it with other drugs and placebos. There are three Cochrane reviews that have evaluated the efficacy of zuclopenthixol, (da Silva 1999; Jayakody 2012; Kumar 2005). The reviews of zuclopenthixol dihydrochloride and decanoate did include placebo interventions in their review, however, the review of zuclopenthixol acetate did not. Over the years there has been widespread debate over the ethics of placebo-controlled studies especially when well known proven treatments exist. Some researchers also argue that placebo trials provide the purest form of evidence when evaluating a particular drug (Vallance 2006). Given the widespread use of this drug, it is essential to evaluate the effectiveness of all three formulations of this commonly used drug comparing it with a placebo so that clinicians, policy makers and recipients of care can make better informed choices of interventions.
To evaluate the effectiveness of all formulations of zuclopenthixol when compared with a placebo.
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. If people are given additional treatments along with zuclopenthixol (any formulation), we will only include data if the adjunctive treatment is evenly distributed between groups and randomised exactly the same way as the intervention was randomised at the start of the trial.
Types of participants
Adults, however defined by authors of studies, with a diagnosis of schizophrenia or schizophreniform disorder, schizoaffective disorder and delusional disorder, again, by any means of diagnosis as defined by authors. 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). If possible, we will exclude children, and people with dementing illnesses, depression and primary problems associated with substance misuse.
If a study described the participant group as suffering from 'serious mental illnesses' and did not give a particular diagnostic grouping, we will include these trials assuming that most people will have suffered from schizophrenia. The exception to this rule will be when the majority of those randomised clearly did not have a functional non-affective psychotic illness.
Types of interventions
- Zuclopenthixol acetate in any form or at any dose compared with placebo
- Zuclopenthixol decanoate in any form or at any dose compared with placebo
- Zuclopenthixol dihydrochloride in any form or at any dose compared with placebo
Types of outcome measures
We will define the outcome periods depending on the type of formulation of zuclopenthixol. For zuclopenthixol decanoate and dihydrochloride, we have predefined trial duration as short term for those between zero and 12 weeks, medium term as those between 13 to 26 weeks and long term as those longer than 26 weeks. For zuclopenthixol acetate, given that the indications for its use are different and it has a different half life, we will consider trials as being short term if the duration was between zero to six hours, medium term from seven to 36 hours, and long term greater than 36 hours.
1. Clinically significant response on global state - as defined by each of the studies
1.1 Death - not suicide
2. Leaving the study early
3. Global state
3.1 Average score in global state
3.2 Average change in global state
3.3 Relapse as defined by the studies
4. Mental state
4.1 Clinically significant response on psychotic symptoms - as defined by each of the studies
4.2 Average score on psychotic symptoms
4.3 Average change in psychotic symptoms
4.4 Clinically significant response on positive symptoms - as defined by each of the studies
4.5 Average score in positive symptoms
4.6 Average change in positive symptoms
4.7 Clinically significant response on negative symptoms - as defined by each of the studies
4.8 Average score on negative symptoms
4.9 Average change in negative symptoms
5. Other adverse effects, general and specific
6. Service utilisation outcomes
6.1 Hospital admission
6.2 Compulsory hospital admission
6.3 Readmission- as defined by each of the studies
7. Quality of life/satisfaction with care for either recipients of care or carers
7.1 Significant change in quality of life/satisfaction - as defined by each of the studies
7.2 Average score in quality of life/satisfaction
7.3 Average change in quality of life/satisfaction
8. Economic outcomes
9. '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 5.2 (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:
- Clinically significant response on global state - as defined by each of the studies
- Clinically significant response on psychotic symptoms - as defined by each of the studies.
- Significant change in quality of life/satisfaction - as defined by each of the studies
Search methods for identification of studies
Cochrane Schizophrenia Group Trials Register
The Trials Search Co-ordinator, will search the Cochrane Schizophrenia Group’s Trials Register
1.1 Intervention search
The ‘Intervention’ field will be searched using the phrase:
((*zuclopenthix* or *ciatyl* or *cisordinol* or *clopenthixol* or *clopixol* or *sordinol*) AND *placebo*)
The Cochrane Schizophrenia Group’s Trials Register is compiled by systematic searches of major databases, handsearches and conference proceedings (see Group Module).
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.
3. Further searching of trials registers.
We will also inspect web sites to see if other trials have been registered. We will inspect the United States National Institute of Health website, (http://www.clinicaltrials.gov/). We will also inspect the WHO international clinical trials registry platform (http://www.who.int/ictrp/en/).
Data collection and analysis
Selection of studies
Review author ML will independently inspect citations from the searches and identify relevant abstracts. A random 20% sample will be independently re-inspected by review author CE 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 ML. Again, a random 20% of reports will be re-inspected by CE, 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 ML will extract data from all included studies. In addition, to ensure reliability, CE 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, authors of studies will be contacted for clarification. With remaining problems, the third review author (MJ) 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 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.
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 aimed 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 less 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, 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 (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 zuclopenthixol. 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 ML and CE will work independently to assess risk of bias by using criteria described in the Cochrane Handbook for Systemic 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 (MJ). 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. 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). The Number Needed to Treat/Harm (NNTB/NNTH) 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). For binary data presented in the 'Summary of findings' table/s, where possible, we will calculate illustrative comparative risks. When presenting data on graphs, we will aim to keep the graphs to read from left to right. This makes the graphs as clear as possible. In order to do this it maybe necessary to change outcomes that are worded positively to their negative equivalent.
2. Continuous data
For continuous outcomes, we will estimateMD between groups. We would prefer not to calculate effect size measures (SMD). However, if scales of very considerable similarity were used, we will presume there was 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, CIs 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 126.96.36.199 (Combining groups) of the Cochrane Handbook for Systemic 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% to 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 to test how prone the primary outcomes are to change when data only from people who complete the study to that point are compared with 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 CIs 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, CIs, 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 I
Heterogeneity between studies will be investigated by considering the I
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 (Egger 1997). These are described in section 10.1 of the Cochrane Handbook for Systemic reviews of Interventions (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
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 will choose to use the random-effects model for all analyses.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses
1.1 Primary outcomes
As there are three different formulations for Zuclopenthixol, we anticipate there may be different effects from each as they commonly have different indications for use. We will therefore undertake a subgroup analysis of the different formulations if there is significant heterogeneity.
1.2 Clinical state, stage or problem
We propose to undertake this review and provide an overview of the effects of zuclopenthixol 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 if possible.
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, we will visually inspect the graph and outlying studies will be successively removed to see if homogeneity is restored. For this review, we have 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 assumption/s 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 people who complete the study to that point. A sensitivity analysis will be undertaken to test how prone results are to change when completer-only data only are compared to 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 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 there is a difference between the fixed-effect and random-effects models then we will consider whether it is reasonable to conclude that the intervention was more effective in the smaller studies as the fixed-effect model gives a greater weight to smaller studies.
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 term was developed by the Trial Search Co-ordinator of the Cochrane Schizophrenia Group, Samantha Roberts and the contact author of this protocol. We would also like to thank Shaimaa AbouDamaa for peer reviewing this protocol.
Contributions of authors
ML - Came up with the concept, devised and drafted the protocol.
MJ - Helped with revising the protocol.
CE- Helped revise the protocol.
Declarations of interest
ML - None known.
MJ - None known.
CE - None known.
Sources of support
- Leeds and York Partnerhships NHS Foundation Trust, UK.Both authors are employed by this organisation
- University of Leeds, UK.ML is undertaking a masters degree with this organisation and has access to their resources. An adapted version of this review will be submitted as ML's masters dissertation
- Cochrane Collaboration Programme Grant 2011, Reference number: 10/4001/15, UK.