Cariprazine versus placebo for schizophrenia
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the efficacy and safety of cariprazine compared to placebo for treating the symptoms of schizophrenia.
Background
Description of the condition
Schizophrenia is a serious mental health disorder affecting more than 21 million people worldwide (WHO 2015). It amounts to about 1.8% of global years lived with disability (YLDs) (Vos 2013). The symptoms of schizophrenia can be categorised into positive symptoms (e.g. hallucinations, delusions. thought disorders), negative symptoms (e.g. blunted affect, lack of motivation, social withdrawal) and cognitive symptoms (e.g. decline in new learning) (NIMH 2014). People with schizophrenia have increased mortality rates (up to 50%) compared with the general population due to a variety of comorbid medical conditions, and suicide with an approximate lifetime risk of suicide for schizophrenia in adults at 5% (NICE 2014). Schizophrenia also leaves a debilitating impact on the quality of life, leaving people living with schizophrenia struggling to not only deal with their diagnosis, but also with resulting difficult social life, employment and housing conditions (Solanki 2008).
Schizophrenia may be diagnosed using different diagnostic systems. The most widely used are the International Classification of Disease (WHO 1992) and the Diagnostic and Statistical Manual (APA 2013). According to the latter, the diagnosis of schizophrenia requires an illness duration of at least six months and at least one month of active symptoms.
Schizophrenia is classified as a multifactorial disorder as no single cause has been linked to it. Those factors can include genetics (Gejman 2010), environmental factors such as obstetric complications (Picchioni 2007), social isolation and familial support, migrant status, and urban life (Boydell 2004).
There are many pharmacological and psychosocial therapies effective for treating schizophrenia, but no cure. Most pharmacological interventions have targeted the dopamine pathways in the brain ever since people with schizophrenia were shown to have an overactivity of dopamine in the central nervous system (Miyamoto 2012).
Description of the intervention
Cariprazine is an orally active atypical antipsychotic drug. It was approved In September 2015 by the US Food and Drug Administration (FDA) for the treatment of schizophrenia and for the acute treatment of manic or mixed episodes associated with bipolar I disorder (McCormak 2015). Its starting dose is 1.5 mg on the first day and may be increased to 3 mg on the second day. Further dose adjustments can be made in 1.5 to 3 mg increments depending upon clinical response and tolerability. The dosage range is 1.5 mg to 6 mg a day.
Cariprazine is rapidly absorbed and its concentration peaks in three to four hours in the blood of a fasting patient. It accumulates with continued administration, but its concentrations stay dose proportional in the effective dose range (Caccia 2013; Citrome 2013). It significantly penetrates the blood brain barrier with a brain/plasma area under curve (AUC) ratio of 7.6:1 as shown by a study on rodents (Kiss 2010). Active metabolites of cariprazine (desmethyl‐cariprazine and didesmethyl‐cariprazine) are retrieved through the extensive hepatic metabolism of the parent compound by cytochrome P450 (CYP) (mainly by CYP3A4 and to lesser extent by CYP2D6) just like other lipophilic antipsychotics (Caccia 2013). Cariprazine's mean half‐life is long and it varies from two to five days for cariprazine, and two to three weeks for didesmethyl‐cariprazine, which makes patient exposure to didesmethyl‐cariprazine several times higher than their exposure to cariprazine (Caccia 2013).
Cariprazine has been reported to be associated with improvements in negative and positive symptoms of schizophrenia. Cariprazine is generally well‐tolerated. Its common adverse events include akathisia, restlessness, tremor, back pain, and extrapyramidal side effects (Durgam 2016; Kane 2015).
How the intervention might work
Current antipsychotic drugs mainly target D2 receptors and have clinical benefit in treating positive symptoms with no effect on negative and cognitive symptoms (Dunlop 2015). Cariprazine, on the other hand, is a potent partial agonist of dopamine D3 and D2 receptors with preferential binding to the D3 receptor. Cariprazine also has a partial agonist activity at serotonin 5‐HT1A receptors. Cariprazine's efficacy in reducing the positive and negative symptoms of schizophrenia is thought to be mediated by inhibiting overstimulated dopamine receptors (Citrome 2013).
Why it is important to do this review
Given the complexity of the treatment of schizophrenia and the variable response of patients to different treatments, new treatment options are always an advantage in the hope of finding one with maximum efficacy and minimal side effects. Thus, it is crucial to systematically assess the data available on cariprazine as a possible new effective treatment for schizophrenia.
Objectives
To assess the efficacy and safety of cariprazine compared to placebo for treating the symptoms of 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). We will exclude quasi‐randomised studies, such as those allocating by alternate days of the week. Where people are given additional treatments in addition to cariprazine or to placebo, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the cariprazine and placebo 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 not exclude people with comorbid disorders, however it is highly unlikely to come across such people because they are usually excluded from trials of antipsychotic medication.
Types of interventions
1. Cariprazine: any dose, any means of administration
2. Placebo: (active or inactive)
Types of outcome measures
As schizophrenia is often a lifelong illness and cariprazine is used as an ongoing treatment, we aim to divide all outcomes into short term (less than six months), medium term (seven to 12 months) and long term (over one year).
Primary outcomes
1. Global state
1.1 Clinically important change in global state, as defined by each study.
1.2 Relapse, as defined by each study.
1.3 Any improvement, as defined by each study.
1.4 Average endpoint/change score global state scale.
2. Social functioning
2.1 Clinically important change in social functioning, as defined by each study.
2.2 Any improvement, as defined by each study.
2.3 Average endpoint/change score social functioning scale.
3. Quality of life/satisfaction with care for either recipients of care or caregivers
3.1 Clinically important change in quality of life/satisfaction, as defined by each study.
3.2 Average endpoint/change score quality of life/satisfaction scale.
3.3 Any change in employment status, as defined by each study.
4. Adverse effects/events
4.1 Cardiovascular effects.
4.2 Death
4.3 Extrapyramidal effects (including use of antiparkinson drugs).
4.4 Genitourinary effects.
4.5 Gastrointestinal effects.
4.6 Central nervous system effects.
4.7 Respiratory effects.
4.8 Weight change.
4.9 Laboratory tests.
4.10 Various other specific effects.
4.11 Any general adverse event/effect.
4.12 Average endpoint/change score adverse effect/event scale.
Secondary outcomes
1. Service utilisation outcomes
1.1 Hospital admission.
1.2 Days in hospital.
2. Behaviour
2.1 Clinically important change in behaviour, as defined by each study.
2.2 Average endpoint/change score behaviour scale.
2.3 Aggression/violence.
3. Mental state
3.1 Clinically important change in overall mental state, as defined by each study.
3.2 Any improvement in overall mental state, as defined by each study.
3.3 Average endpoint/change score in overall mental state.
3.4 Positive symptoms.
3.4.1 Clinically important change in positive symptoms, as defined by each study.
3.4.2 Average endpoint/change score positive symptom scale.
3.5 Negative symptoms.
3.5.1 Clinically important change in negative symptoms, as defined by each study.
3.5.2 Average endpoint/change score negative symptom scale.
4. Cognitive functioning
4.1 Clinically important change in cognitive functioning, as defined by each study.
4.2 Any change in cognitive functioning, as defined by each study.
4.3 Average endpoint/change score cognitive functioning scale.
5. Economic outcomes
5.1 Costs due to treatment, as defined by each study.
5.2 Savings due to treatment, as defined by each study.
6. Leaving the study early
6.1 Due to relapse.
6.2 Due to adverse effects.
6.3 For any reason.
'Summary of findings' tables
We will use the GRADE approach to interpret findings (Schünemann 2008) and will use GRADE profiler (GRADEPRO) to import data from RevMan 5 (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' tables
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Global state: relapse, as defined by each study (medium term).
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Social functioning: clinically important change, as defined by each study.
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Quality of life: clinically important change in quality of life, as defined by each study.
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Adverse effects: extrapyramidal ‐ parkinsonism rigidity (medium term).
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Adverse effects: metabolic ‐ weight change (medium term).
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Mental state: clinically important change in overall mental state, as defined by each study (medium term).
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Mental state: any improvement in overall mental state, as defined by each study (medium term).
Search methods for identification of studies
Electronic searches
Cochrane Schizophrenia Group’s Trials Register
The Information Specialist of the Cochrane Schizophrenia Group will search their Study‐Based Register of Trials using the following search strategy:
*Cariprazine* in Intervention Field of STUDY
In such a study‐based register, searching the major concept retrieves all the synonym keywords and relevant studies because all the studies have already been organised based on their interventions and linked to the relevant topics.
The Cochrane Schizophrenia Group’s Register of Trials is compiled by systematic searches of major resources (including AMED, BIOSIS, CINAHL, Embase, MEDLINE, PsycINFO, PubMed, and registries of clinical trials) and their monthly updates, handsearches, grey literature, and conference proceedings (see Group’s Module). There is no language, date, document type, or publication status limitations for inclusion of records into the register.
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 NE and IH will independently inspect citations from the searches and identify relevant abstracts. A random 20% sample will be independently re‐inspected by AE to ensure reliability. Where disputes arise, we will acquire the full report acquired for more detailed scrutiny. NE and IH will obtain and inspect full reports of the abstracts meeting the review criteria. Again, AE will re‐inspect a random 20% of the full reports in order to ensure reliable selection. Where it is not possible to resolve disagreement by discussion, we will attempt to contact the authors of the study for clarification.
Data extraction and management
1. Extraction
Review authors NE and IH will extract data from all included studies. In addition, to ensure reliability, AE will independently extract data from a random sample of these studies, comprising 10% of the total. Again, we will discuss any disagreement, document decisions and, if necessary, contact authors of studies for clarification. With any remaining problems, AE will help clarify issues and we will document these final decisions. We will attempt to extract data presented only in graphs and figures whenever possible, but include such data 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. We will combine endpoint and change data in the analysis as we aim to 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:
Endpoint data N > 200
We will enter data from studies of at least 200 participants, in analyses irrespective of the following rules, because skewed data pose less of a problem in large studies.
Change data
We will also enter change data as 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
Endpoint data N < 200
(a) when a scale starts from the finite number zero, we will subtract the lowest possible value from the mean, and divide this by the standard deviation (SD). If this value is lower than 1, it strongly suggests a skew and we will exclude these data. If this ratio is higher than 1 but below 2, there is suggestion of skew. We will enter these data and test whether their inclusion or exclusion would change the results substantially. Finally, if the ratio is larger than 2, we can include such data because skew is less likely (Altman 1996; Higgins 2011).
b) if a scale starts from a positive value (such as the Positive and Negative Syndrome Scale (PANSS), (Kay 1986)), which can have values from 30 to 210), we will modify the calculation described 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.
2.5 Common measure
To facilitate comparison between trials, we plan to convert variables that can be reported in different metrics, such as days in hospital (mean days per year, per week or per month) to a common metric (e.g. mean days per month).
2.6 Conversion of continuous to binary
Where possible, we will make efforts to convert outcome measures to dichotomous data. This can be done by identifying cut‐off points on rating scales and dividing participants accordingly into 'clinically improved' or 'not clinically improved'. It is generally assumed that if there is a 50% reduction in a scale‐derived score such as the Brief Psychiatric Rating Scale (BPRS, Overall 1962) or the Positive and Negative Syndrome Scale (PANSS, Kay 1986), this could be considered as a clinically significant response (Leucht 2005; Leucht 2005a). If data based on these thresholds are not available, we will use the primary cut‐off presented by the original authors.
2.7 Direction of graphs
Where possible, we will enter data in such a way that the area to the left of the line of no effect indicates a favourable outcome for cariprazine. Where keeping to this makes it impossible to avoid outcome titles with clumsy double‐negatives (e.g. 'Not un‐improved'), we will report data where the left of the line indicates an unfavourable outcome and note this in the relevant graphs.
Assessment of risk of bias in included studies
Again, review authors NE, IH and AE will work independently to assess risk of bias by using criteria described in the Cochrane Handbook for Systematic reviews of Interventions (Higgins 2011) to assess trial quality. This set of criteria is based on evidence of associations between overestimate of effect and high risk of bias of the article such as sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting.
If the raters disagree, the final rating will be made by consensus. Where inadequate details of randomisation and other characteristics of trials are provided, we will contact authors of the studies in order to obtain further information. We will report non‐concurrence in quality assessment, but if disputes arise as to which category a trial is to be allocated, again, we will resolve by discussion.
We will note the level of risk of bias in both the text of the review and in the 'Summary of findings' table.
Measures of treatment effect
1. Binary data
For binary outcomes we will calculate a standard estimation of the risk ratio (RR) and its 95% confidence interval (CI). It has been shown that RR is more intuitive (Boissel 1999) than odds ratios and that odds ratios tend to be interpreted as RR by clinicians (Deeks 2000). The Number Needed to Treat/Harm (NNT/H) statistic with its confidence intervals is intuitively attractive to clinicians but is problematic both in its accurate calculation in meta‐analyses and interpretation (Hutton 2009). 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 mean difference (MD) between groups. We prefer not to calculate effect size measures (standardised mean difference (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, and contact first authors of studies to attempt 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 we will assume it 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 is 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, we will present the additional treatment arms in comparisons. If data are binary we will simply add these and combine within the two‐by‐two table. If data are continuous, we will combine data following the formula in section 7.7.3.8 (Combining groups) of the Cochrane Handbook for Systematic reviews of Interventions (Higgins 2011). Where the additional treatment arms are not relevant, we will not use these data.
Dealing with missing data
1. Overall loss of credibility
At some degree of loss 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.
2. Binary
In the case where attrition for a binary outcome is between 0% and 50% and where these data are not clearly described, we will present data on a 'once‐randomised‐always‐analyse' basis (an intention‐to‐treat (ITT) analysis). Those leaving the study early are all assumed to have the same rates of negative outcome as those who completed, with the exception of the outcome of death and adverse effects. For these outcomes, we will use the rate of those who stay in the study ‐ in that particular arm of the trial ‐ for those who did not. We will undertake a sensitivity analysis to test how prone the primary outcomes are to change when data only from people who complete the study to that point are compared to the ITT analysis using the above assumptions.
3. Continuous
3.1 Attrition
In the case where attrition for a continuous outcome is between 0% and 50%, and data only from people who complete the study to that point are reported, we will reproduce these.
3.2 Standard deviations
If standard deviations (SDs) are not reported, we will first try to obtain the missing values from the authors. If not available, where there are missing measures of variance for continuous data, but an exact standard error (SE) and confidence intervals 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 Systematic reviews of Interventions (Higgins 2011): When only the SE is reported, SDs are calculated by the formula SD = SE * square root (n). Chapters 7.7.3 and 16.1.3 of the Cochrane Handbook for Systematic reviews of Interventions (Higgins 2011) present detailed formulae for estimating SDs from P values, t or F values, confidence intervals, ranges or other statistics. If these formulae do not apply, we will calculate the SDs according to a validated imputation method which is based on the SDs of the other included studies (Furukawa 2006). Although some of these imputation strategies can introduce error, the alternative would be to exclude a given study’s outcome and thus to lose information. We nevertheless will examine the validity of the imputations in a sensitivity analysis excluding imputed values.
3.3 Last observation carried forward
We anticipate that in some studies the method of last observation carried forward (LOCF) will be employed within the study report. As with all methods of imputation to deal with missing data, LOCF introduces uncertainty about the reliability of the results (Leucht 2007). Therefore, where LOCF data have been used in the trial, if less than 50% of the data have been assumed, we will present and use these data and indicate that they are the product of LOCF assumptions.
Assessment of heterogeneity
1. Clinical heterogeneity
We will consider all included studies initially, without seeing comparison data, to judge clinical heterogeneity. We will simply inspect all studies for clearly outlying people or situations which we had not predicted would arise and discuss these.
2. Methodological heterogeneity
We will consider all included studies initially, without seeing comparison data, to judge methodological heterogeneity. We will simply inspect all studies for clearly outlying methods which we had not predicted would arise and discuss these.
3. Statistical heterogeneity
3.1 Visual inspection
We will visually inspect graphs to investigate the possibility of statistical heterogeneity.
3.2 Employing the I2 statistic
We will investigate heterogeneity between studies by considering the I2 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. a 'P' value from Chi2 test, or a confidence interval for I2). We will interpret an I2 estimate greater than or equal to around 50% accompanied by a statistically significant Chi2 statistic, as evidence of substantial levels of heterogeneity (Section 9.5.2 ‐ Higgins 2011). When substantial levels of heterogeneity are found in the primary outcome, we will explore reasons for heterogeneity (Subgroup analysis and investigation of heterogeneity).
Assessment of reporting biases
1. Protocol versus full study
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results. These are described in section 10.1 of the Cochrane Handbook for Systematic reviews of 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 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 size. 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 the fixed‐effect model for all analyses.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses
1.1. Clinical state, stage or problem
We are interested in making sure that information is as relevant to the current care of people with schizophrenia as possible so propose, if information is provided, 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).
2. Investigation of heterogeneity
We will report if inconsistency is high. First, we will investigate whether data have been entered correctly. Second, if data are correct, we will visually inspect the graph and successively remove outlying studies to see if homogeneity is restored. For this review we have decided that should this occur with data contributing to the summary finding of no more than around 10% of the total weighting, we will present data. If not, we will not pool data but will discuss these 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, if inclusion of data from these trials 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.
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. We will undertake a sensitivity analysis to test how prone the 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). If the exclusion of trials at high risk of bias does not substantially alter the direction of effect or the precision of the effect estimates, then we will include data from these trials in the analysis.
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‐effect and random‐effects
We will synthesise all data using a fixed‐effect model, however, we will also synthesise data for the primary outcome using a random‐effects model to evaluate whether this alters the significance of the results.
