Quetiapine versus placebo for schizophrenia
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To determine the clinical effects of quetiapine for schizophrenia and schizophrenia‐like illnesses in comparison with placebo.
Background
Description of the condition
Schizophrenia is a major mental illness characterised by a diverse range of signs and symptoms which include distortions of thinking, perception, blunted affect and cognitive impairments. These abnormalities are differentially expressed between people and throughout the course of the illness. Core features include both positive and negative symptoms. The positive symptoms are delusions and hallucinations, and the negative include social withdrawal, loss of motivation and decreased ability to experience pleasure. Together these symptoms lead to significant social and occupational dysfunction.
People with schizophrenia have a significantly reduced life expectancy compared with the general population (Tiihonen 2009). This is due to increased mortality for both un‐natural deaths (such as suicide and accidents) and physical comorbidity (such as heart disease, endocrine diseases, respiratory disease and infectious diseases) (Saha 2007).
The onset of schizophrenia tends to be in adolescence or early adulthood. The incidence is around 15.2/100,000 population with a greater distribution in men than women (M:F ratio 1.4, McGrath 2004). The onset of illness is usually around early adult life and is chronic in nature (Saha 2005). Pharmacological intervention is a mainstay for treatment of this illness or group of illnesses and its advent has greatly changed the outlook for people with this illness (Turner 2007). Some people, however, continue to experience symptoms in spite of medication and may also develop undesirable adverse effects. Choosing the most appropriate, effective and tolerable antipsychotic/neuroleptic medication for people with schizophrenia is key to maximising treatment outcomes.
Description of the intervention
First‐generation (typical) antipsychotics have been used to treat schizophrenia since the 1950's (Turner 2007). These drugs tended to cause tremors, muscular stiffness, slowing of movements, restlessness and abnormal involuntary movements. Also, about one‐third of people with schizophrenia do not really respond to this set of drugs. Since 1988 a newer generation of antipsychotic drugs have become available. These are classed as ‘atypical' antipsychotics due to effectiveness in treating negative symptoms but a low propensity to induce extrapyramidal side effects (Kerwin 1994). It is acknowledged that clozapine may be more effective than typical antipsychotics (Essali 2009).
How the intervention might work
The efficacy and safety of quetiapine were promising in early (phase II) clinical trials. It has been suggested that quetiapine is effective for treating both positive and negative symptoms of schizophrenia and that it is generally well tolerated. In addition, its propensity to induce movement disorders is low and reputedly no different to that of placebo (Borison 1996).
Pharmacodynamics of quetiapine: behavioural, electrophysiological and biochemical studies have indicated that quetiapine is a clozapine‐like atypical antipsychotic (Goldstein 1993; Migler 1993; Saller 1993). It is similar to clozapine in having only moderate affinities (< 500 nM) (Goldstein 1995) to both D2 and 5‐HT2A receptors (Kapur 2000) and has a high affinity for histamine receptors (< 50 nM).
Why it is important to do this review
Relative effects of quetiapine, when compared with other drugs, are important but not a focus of this review (Table 1). Comparing quetiapine with placebo will highlight the degree of placebo‐response (recent schizophrenia trials comparing treatment with placebo have reported mean response rate of 25% (range 0% to 41%, Kinon 2011) and establish whether claims regarding its low propensity to induce movement disorders is well‐founded (Borison 1996).
| Title | Link | Notes | |
| Directly related | Quetiapine versus other atypical antipsychotics for schizophrenia | ||
| Quetiapine for schizophrenia | This review is currently not maintained and is being split into other directly related reviews | ||
| Indirectly related | Atypical antipsychotics for people with both schizophrenia and depression | These reviews contain data on quetiapine | |
| Antipsychotic switching for people with schizophrenia who have neuroleptic‐induced weight or metabolic problems | |||
| New generation antipsychotics for first episode schizophrenia | |||
| Newer atypical antipsychotic medication versus clozapine for schizophrenia |
This is one of a series of related Cochrane Reviews relevant to the use of quetiapine (Table 1).
Objectives
To determine the clinical effects of quetiapine for schizophrenia and schizophrenia‐like illnesses in comparison with placebo.
Methods
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 interventions by alternate days of the week.
Types of participants
Adults (with the majority aged 16‐65 years) with schizophrenia, schizoaffective disorder or schizophreniform disorders. We will accept any means of diagnosis but recognise that the operational criteria are particularly useful to define people who have the illness (e.g. International Classification of Diseases (ICD) or Diagnostic Statistical Manual (DSM)).
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
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Quetiapine: oral administration, any dose, means/timing of delivery.
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Placebo: oral administration, any dose, means/timing of delivery.
Types of outcome measures
All outcomes will be reported for the short term (up to 12 weeks), medium term (13‐26 weeks), and long term (more than 26 weeks) effects. The outcome measures include either dichotomous or continuous outcomes based on rating scales and also as defined by individual studies.
Primary outcomes
1. Global state
1.1 Clinically significant response in global state, as defined by each study
2. Extrapyramidal adverse effects
2.1 Clinically significant extrapyramidal adverse effects based on relevant rating scales
3. Behaviour
3.1 Clinically significant agitation as defined by each study
Secondary outcomes
1. Global state
1.1 Average score/change in global state
1.2 Relapse
2. Mental state
2.1 Clinically significant response in psychotic symptoms
2.2 Average score/change in psychotic symptoms
2.3 Clinically significant response in positive symptoms
2.4 Average score/change in positive symptoms
2.5 Clinically significant response in negative symptoms
2.6 Average score/change in negative symptoms
3. Leaving the study early
4. Extrapyramidal adverse effects
4.1 Use of any antiparkinsonism drugs
4.2 Average score/change in extrapyramidal adverse effects
4.3 Tardive dyskinesia
4.4 Acute dystonia
4.5 Akasthesia
5. Other adverse effects/event, general and specific
5.1 Death
6. Hospital and service utilisation outcomes
6.1 Hospital admission
6.2 Average change in days in hospital
6.3 Improvement in hospital status (for example: change from formal to informal admission status, use of seclusion, level of observation)
7. Economic outcomes
7.1 Average change in total cost of medical and mental health care
7.2 Total indirect and direct costs
8. Quality of life/satisfaction with care for either recipients of care or caregivers
8.1. Significant change in quality of life/satisfaction
8.2 Average score/change in quality of life/satisfaction
9. Behaviour
9.1 Use of adjunctive medication for sedation
9.2 Aggression to self or others
10. Cognitive response
10.1 Clinically important change
10.2 Any change, general and specific
11. 'Summary of findings' table
We will use the GRADE approach to interpret findings (Schünemann 2008) and use GRADE profiler (GRADE PRO) 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 will select the following main outcomes for inclusion in the 'Summary of findings' table.
1. Global state
1.1 Clinically significant response in global state, as defined by each study
2. Behaviour
2.1 Clinically significant agitation as defined by each study
3. Mental state
3.1 Clinically significant response on psychotic symptoms (defined by each study)
3.2 Clinically significant response on negative symptoms (defined by each study)
4. Leaving the study early
5. Extrapyramidal adverse effects
5.1 Incidence of use of antiparkinson drugs
5.2 Clinically significant EPSE ‐ as defined by each of the studies
6. Other adverse effects/events, general and specific
6.1 Death ‐ any cause
Search methods for identification of studies
Electronic searches
1. Cochrane Schizophrenia Group Trials Register
We will search the register using the phrase:
[(*quetiapine* or *seroquel* or *ICI‐204636* or (ICI and 204636) or *ICI204636* in interventions of STUDY) AND (*placebo* in interventions of STUDY]
This register is compiled by systematic searches of major databases, handsearches and conference proceedings (see Group module).
For a previous search strategy used in the original Quetiapine for schizophrenia review (Srisurapanont 2004), please see Appendix 1.
Searching other resources
1. Reference searching
We will inspect references of all included and excluded 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 RG will independently inspect citations from the searches and identify relevant abstracts. A random 20% sample will be independently re‐inspected by SL to ensure reliability. Where disputes arise, we will acquire the full report for a more detailed scrutiny. Full reports of the abstracts meeting the review criteria will be obtained and inspected by SL. Again, a random 20% of reports will be re‐inspected by SL 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 author RG will extract data from all included studies. In addition, to ensure reliability, SL 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 the authors of studies for clarification. With any remaining problems, SL will help clarify issues and these final decisions will be documented. We will extract data presented only in graphs and figures whenever possible, but include only if both review authors independently have the same result. Attempts will be made 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 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, and we will note if this is the case or not in Description of studies tables.
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 will only use change data if the former are not available. We will combine endpoint and change data 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) which can have values from 30 to 210), we will modify the calculation described above 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 in ‘Additional tables’ rather than in 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 enter change data, regardless of sample size, into 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 PANSS (Kay 1986), this could be considered as a clinically significant response ( Leucht 2005a; Leucht 2005b). 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 quetiapine. Where keeping to this makes it impossible to avoid outcome titles with clumsy double‐negatives (e.g. 'Not improved') we will report data so 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
Both review authors (SL and RG) will work independently to assess risk of bias by using the 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. 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, resolution will be made 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 statistically significant results, we will use 'Summary of findings' tables to calculate the number needed to treat to provide benefit /to induce harm statistic and its 95% CI.
2. Continuous data
For continuous outcomes, we will estimate the MD between groups. We would prefer not to calculate effect size measures (SMD). However, if scales of very considerable similarity are 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, 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. We will seek to contact first authors of studies to obtain intra‐class correlation coefficients 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 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 intra‐class correlation coefficient (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 them 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 Systemic reviews of Interventions (Higgins 2011). Where the additional treatment arms are not relevant, we will not present 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 present 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 mark such data with (*) to indicate that such a result may well be prone to bias.
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 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.
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 present and use these data.
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 are 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 formula for estimating SDs from P values, t or F values, confidence intervals, ranges or other statistics. If these formula 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 reproduce 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 Cochrane Handbook for Systemic reviews of Interventions ‐ 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 Systemic reviews of Interventions (Higgins 2011). We will try to locate protocols of included randomised trials. If the protocol is available, we will compare outcomes in the protocol and in the published report. If the protocol is not available, we will compare outcomes listed in the methods section of the trial report 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). Again, 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 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 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
We propose to undertake this review and provide an overview of the effects of quetiapine treatment for people with schizophrenia in general. In addition, however, if data are available, we will try to report data on subgroups of people in the same clinical state, stage and with similar problems for the primary outcomes only.
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 remove outlying studies to see if homogeneity is restored. For this review we have decided that should this occur with data contributing to the summary findings of no more than around 10% of the total weighting, we will present the data. If not, these data will not be pooled and we will 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. 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 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 and when we use data only from people who complete the study to that point. A sensitivity analysis will be undertaken testing how prone results are to change when completer‐only data only 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 do 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.
4. Imputed values
We will also undertake a sensitivity analysis to assess the effects of including data from trials where we use 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‐effect and random‐effects models
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 the greater weights assigned to larger trials with greater event rates, alter the significance of the results compared with the more evenly distributed weights in the random‐effects model.
| Title | Link | Notes | |
| Directly related | Quetiapine versus other atypical antipsychotics for schizophrenia | ||
| Quetiapine for schizophrenia | This review is currently not maintained and is being split into other directly related reviews | ||
| Indirectly related | Atypical antipsychotics for people with both schizophrenia and depression | These reviews contain data on quetiapine | |
| Antipsychotic switching for people with schizophrenia who have neuroleptic‐induced weight or metabolic problems | |||
| New generation antipsychotics for first episode schizophrenia | |||
| Newer atypical antipsychotic medication versus clozapine for schizophrenia |
