Asenapine versus typical antipsychotics for schizophrenia
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To review the efficacy of asenapine compared with other typical antipsychotic drugs for people with schizophrenia.
Background
Description of the condition
Schizophrenia is a major psychiatric disorder that alters an individual's perception, thoughts, affect and behaviour and is generally associated with significant social and occupational dysfunction. Worldwide, it has been estimated that schizophrenia falls into the top 10 medical disorders causing disability (WHO 1990). It is one of the major contributors to the global burden of diseases (Murray 1997).
The incidence of the schizophrenia is relatively low with a median value of 15.2 per 100,000 persons per year (McGrath 2008). The lifetime prevalence of schizophrenia is between 0.4% to 1.4% (Cannon 1996). Schizophrenia is characterised by positive and negative symptoms (APA 2000). Around 70% of patients also experience cognitive problems and often have depression (Kurtz 2005; Moller 2005). It is typically preceded by a prodromal period (initial phase when symptoms develop), which is characterised by deterioration in personal functioning. This prodromal period is followed by an acute phase characterised by positive symptoms of delusions, hallucinations and behavioural symptoms. Following resolution of the acute phase generally by some treatment, positive symptoms disappear or diminish, sometimes followed by negative symptoms not unlike the early prodromal period. Although this is a common pattern, the course of schizophrenia varies considerably.
Individuals possess different levels of vulnerability to schizophrenia, which are determined by a combination of biological, social and psychological factors as described by the “vulnerability stress” model (Nuechterlein 1984). There are biological hypotheses about brain biochemistry and pathology (Broome 2005), and attempts are being made to identify genes that confer susceptibility (Craddock 2005). The biochemical theory “dopamine hypothesis” argues that schizophrenia might be related to problems in the regulation of the neurotransmitter dopamine in the prefrontal cortex (Kapur 2003).
Description of the intervention
Antipsychotics have been the mainstay of treatment of schizophrenia since the 1950s, within both hospital and community settings. They are effective in both the treatment of acute episodes and relapse prevention (Janicak 1993) as well as for the emergency treatment of acute behavioural disturbance (rapid tranquillisation) and for symptom reduction. However, around 40% of patients have a poor response to conventional antipsychotic medication (Kane 1996; Klein 1969).
The introduction of atypical antipsychotic medications represented advances in the treatment of schizophrenia comparable to that of typical antipsychotic medications but with a lower propensity to cause extrapyramidal symptoms (Kerwin 1994).
The primary pharmacological action of antipsychotic drugs is their antagonistic effect on the D2 dopamine receptors. The potency of a drug’s antipsychotic effect is at least in part determined by its affinity for the D2 receptor (Agid 2007; Kapur 2001; Snyder 1974), a fact which led to the “dopamine hypothesis” of schizophrenia. Hyperactivity in the mesolimbic dopamine pathway is thought to cause psychosis and the positive symptoms of schizophrenia such as hallucinations and delusions. The mesocortical pathway is thought to control cognitive function, and dopamine deficiency in this pathway may be responsible for the negative and cognitive symptoms of schizophrenia (Stahl 2003). In other words, an agent would have to decrease dopamine in the mesolimbic pathway to alleviate positive symptoms but increase it in the mesocortical pathway to treat negative and cognitive symptoms (Stahl 2008). Asenapine is one of the newer antipsychotics that works by acting on D2 receptors (Potkin 2007).
How the intervention might work
Asenapine is a novel atypical antipsychotic medication and was initially approved by the US Food and Drug Administration (FDA) in 2009 for the treatment of schizophrenia and bipolar illness (Citrome 2009). Asenapine displays a unique rank order of binding affinities for various subtypes of serotonin (5HT2C > 5HT2A > 5HT7 > 5HT2B > 5HT6), adrenergic (alpha‐1, alpha‐2), dopamine (D1, D2, D3, D4) and histamine (H1, H2) receptors, with notable lack of affinity for muscarinic (M1) receptors (Shahid 2009). Although the precise mechanism of action of asenapine in the treatment of schizophrenia is unknown, it is thought that antagonism at the dopamine D2 and serotonin 5HT2A receptor mediates antipsychotic activity, asenapine is shown to occupy > 65% of D2 receptors at 6 mg/day (Potkin 2007).
Asenapine is administered sublingually due to high first pass metabolism in liver (FDA 2009). It is metabolised primarily by direct glucuronidation and oxidative metabolism by cytochrome P450 (CYP) isoenzymes, predominantly CYP1A2. It has a large volume of distribution (approximately 20–25 L/kg) and is highly bound (95%) to plasma proteins. Peak plasma levels occur rapidly in 30‐90 minutes and the mean terminal half‐life is approximately 24 hours (FDA 2009). Asenapine is said to cause a mean weight gain of less than 1 kg over a one‐year period, can cause sedation and extrapyramidal side effects but have no significant impact on QTc prolongation (Chapel 2009; Citrome 2011).
Why it is important to do this review
There is ongoing debate about whether second‐generation atypical antipsychotic drugs are better than first‐generation typical antipsychotic drugs (Leucht 2009). The objective of this review is to compare the efficacy and safety of an atypical antipsychotic, asenapine in comparison with typical antipsychotic drugs in the treatment of schizophrenia. To date there has been no systematic review to compare asenapine with typical antipsychotics.
Objectives
To review the efficacy of asenapine compared with other typical antipsychotic drugs for people with schizophrenia.
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 by alternate days of the week. Where people are given additional treatments within the intervention arm (i.e. asenapine), we will only include data if the adjunct treatment is evenly distributed between groups and it is only the asenapine that is randomised.
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 will only include trials where the majority of participants have a diagnosis of schizophrenia.
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
1. Intervention:
Asenapine oral form.
2. Control:
Other typical antipsychotics e.g. chlorpromazine, haloperidol, flupentixol, pericyazine, perphenazine, pimozide, prochlorperazine, sulpride, trifluoperazine, zuclopenthixol.
Types of outcome measures
All outcomes will be divided into short term (up to 12 weeks), medium term (13 to 26 weeks) and long term (over 26 weeks).
Primary outcomes
1. Clinical Response
1.1. Clinically significant response of psychotic symptoms as defined in each study e.g. 50% reduction in average endpoint scores on rating scales
Secondary outcomes
1. Adverse Effects
1.1 Number of participants with at least one adverse effect
1.2 Clinically important specific adverse effects (cardiac effects, death, movement disorders, sedation, seizures, weight gain, effects on white blood cell count etc.)
1.3 Average endpoint in specific adverse effects
1.4 Average change in specific adverse effects
1.5 Adverse effects judged related to study drug
1.6 Serious adverse effects (hospitalisation or death)
2. Global State
2.1 Clinically important change in global state (as defined by individual study)
2.2 Relapse (as defined by the individual study)
2.3 Average endpoint global state score
2.4 Average change in global state scores
3. General functioning
3.1 Clinically important change in general functioning
3.2 Average endpoint general functioning score
3.3 Average change in general functioning score
4. Leaving the study early
4.1 Any reason
5. Satisfaction with treatment
5.1 Recipient of care satisfied with treatment
5.2 Recipient of care average satisfaction score
5.3 Recipient of care average change in satisfaction scores
5.4 Caregiver satisfied with treatment
5.5 Caregiver average satisfaction score
5.6 Caregiver average change in satisfaction scores
6. Quality of life
6.1 Clinically important change in quality of life
6.2 Average quality of life endpoint score
6.3 Average change of quality of life score
6.4 Clinically important change in specific aspects of quality of life
6.5 Average endpoint specific aspects of quality of life score
6.6 Average change in specific aspects of quality of life score
7. General functioning
7.1 Clinically important change in general functioning
7.2 Average endpoint general functioning score
7.3 Average change in general functioning score
8. 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.
-
Clinical response
-
Global state
-
Adverse effects
-
Service use
-
Leaving the study early
-
Quality of life
-
General functioning
Search methods for identification of studies
Electronic searches
Cochrane Schizophrenia Group Trials Register
The Trials Search Co‐ordinator will search the Cochrane Schizophrenia Group’s Trials Register.
Intervention search
The ‘Intervention’ field will be searched using the phrase: *asenapine*
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.
Data collection and analysis
Selection of studies
Review authors MN, HR and MM will independently inspect citations from the searches and identify relevant abstracts. A random 20% sample will be independently re‐inspected by AK 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 MN, HR and MM. Again, a random 20% of reports will be re‐inspected by AK in order to ensure reliable selection. Where it is not possible to resolve disagreement by discussion, we will attempt to contact the authors of the study for clarification.
Data extraction and management
1. Extraction
Review authors MN, HR and MM will extract data from all included studies. In addition, to ensure reliability, AK 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 AK 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.
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, 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) 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. Skewed endpoint data pose less of a problem when looking at means if the sample size is large (over 200 participants) and 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 and skewed change data will be entered into synthesis from both large and small trials.
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 asenapine. 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 MN, HR and MM 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 AK. 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 these 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). We will not calculate the Number Needed to Treat/Harm (NNT/H). The NNT/H statistic with its CIs 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.
2. Continuous data
For continuous outcomes, we will estimate the 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. 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 the 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 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 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, (except for the outcome 'leaving the study early'). 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 to 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 reproduce these.
3.2 Standard deviations
If standard deviations (SDs) are not reported, we will first try to obtain the missing values from the authors. If these are 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 the 'P' value or 't' value is 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 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). These are again described in Section 10 of the Cochrane Handbook for Systemic 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 to use the random‐effects model for all analyses. The reader is, however, able to choose to inspect the data using the fixed‐effect model.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses
1.1 Primary outcomes
No sub‐group analyses are anticipated for the primary outcomes.
1.2 Clinical state, stage or problem
We propose to undertake this review and provide an overview of the effects of asenapine 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, 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 finding of no more than around 10% of the total weighting, data will be presented. If not, data will not be pooled but we will discuss the relevant 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 outcome, 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 outcome 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 outcome 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 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 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.
