Haloperidol discontinuation for schizophrenia
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To review the effects of haloperidol discontinuation in people with schizophrenia who are stable on haloperidol.
Background
Description of the condition
Schizophrenia is often a chronic and disabling psychiatric disorder. It afflicts approximately one percent of the population world‐wide with little gender differences (Berger 2003). The median incidence of schizophrenia was 15.2/100,000 persons (McGrath 2008). The typical manifestations of schizophrenia are 'positive' symptoms such as fixed, false beliefs (delusions) and perceptions without cause (hallucinations); 'negative' symptoms such as apathy and lack of drive, disorganisation of behaviour and thought; and catatonic symptoms such as mannerisms and bizarre posturing (Carpenter 1994). The degree of suffering and disability is considerable, with 80% to 90% not working (Marvaha 2004), and up to 10% dying by suicide (Tsuang 1978).
Description of the intervention
Haloperidol is one of the most frequently used antipsychotic compounds (Lohse 2009). It is a first‐generation ('typical', 'conventional') antipsychotic drug with very high antidopaminergic activity. Its mean elimination half‐life has been reported to range from 15 to 37 hours and its bioavailability is 60% to 70% (Kudo 1999). Haloperidol is highly effective in treating schizophrenia, but the downside is that it is associated with severe extrapyramidal side effects. The most predominant among these extrapyramidal side effects are dystonia, parkinsonian‐like syndrome, and tardive dyskinesia. Other side effects include anticholinergic effects (e.g. constipation, dry mouth, blurred vision, and urinary hesitancy), sexual dysfunction, elevations in serum prolactin, sedation and there could even be shown a relationship with sudden death. Therefore, clinicians and people with schizophrenia often face a trade‐off between protection against psychotic episodes and adverse effects.
Haloperidol is effective in treating the acute phases of schizophrenia (Irving 2006). However, it remains unclear how long haloperidol treatment should continue after the acute phase of the illness subsides. The intervention studied in this review is the discontinuation of haloperidol in people with schizophrenia who have already responded to haloperidol treatment.
How the intervention might work
Haloperidol is one of the butyrophenone family of antipsychotic (neuroleptic) drugs (López‐Munoz 2009). It is thought that haloperidol prevents the occurrence of delusions and hallucinations by blocking the dopamine D2 receptors in the meso‐cortico‐limbic system. A similar antidopaminergic activity in the dorsolateral striatum may contribute to the adverse extrapyramidal effects that are associated with haloperidol treatment (Xiberas 2001).
Why it is important to do this review
Although schizophrenia is generally thought to be a lifelong disorder requiring long‐term pharmacological treatment (Essali 1993), the course of schizophrenia varies, and may follow one of four patterns (Shepherd 1989):
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13% may have a single episode with no subsequent impairment;
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30% may have several episodes with no or minimal impairment;
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10% may suffer impairment following the first episode with occasional exacerbation of symptoms and no return to normality;
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47% show impairment increasing after each exacerbation.
Presently, it is impossible to predict the course of schizophrenia. Medication cessation studies may help identify the characteristics of those patients who will have a single episode and not require maintenance drug treatment, those who will follow a relapsing course and may benefit from intermittent treatment, and those who require indefinite maintenance drug treatment. In this review, we aim to investigate the quantitative effects of stopping haloperidol for people stable on this drug by reviewing available trial‐based evidence.
Objectives
To review the effects of haloperidol discontinuation in people with schizophrenia who are stable on haloperidol.
Methods
Criteria for considering studies for this review
Types of studies
All relevant randomised controlled trials (RCTs).
If a trial is described as 'double blind' but implies randomisation, we will include such trials in a sensitivity analysis (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, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the haloperidol 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, who are on stable doses of haloperidol (oral or injection).
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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Discontinuation of haloperidol treatment, however this is done in the trials, e.g. gradually, abruptly or under cover of placebo
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Continuation of haloperidol treatment at any dose or mode of administration (oral or by injection)
Types of outcome measures
We will divide all outcomes into short‐term (up to three months), medium‐term (over three and up to six months) and long‐term (over six months).
Primary outcomes
1. Global state
1.1 Global state improvement
1.2 Relapse ‐ as defined by each study
Secondary outcomes
1. Death ‐ suicide and natural causes
2. Global state
2.1 Average endpoint global state score
2.2 Average change in global state scores
3. Service outcomes
3.1 Hospitalisation
3.2 Inability to be discharged from hospital
4. Mental state (with particular reference to the positive and negative symptoms of schizophrenia)
4.1 Clinically important change in general mental state
4.2 Average endpoint general mental state score
4.3 Average change in general mental state scores
4.4 Clinically important change in specific symptoms (positive symptoms of schizophrenia, negative symptoms of schizophrenia, depression, mania)
4.5 Average endpoint specific symptom score
4.6 Average change in specific symptom scores
5. General functioning
5.1 Clinically important change in general functioning including working ability
5.2 Average endpoint general functioning score
5.3 Average change in general functioning scores
5.4 Clinically important change in specific aspects of functioning, such as social or life skills
5.5 Average endpoint specific aspects of functioning, such as social or life skills
5.6 Average change in specific aspects of functioning, such as social or life skills
6. Behaviour
6.1 Clinically important change in general behaviour
6.2 Average endpoint general behaviour score
6.3 Average change in general behaviour scores
6.4 Clinically important change in specific aspects of behaviour
6.5 Average endpoint specific aspects of behaviour
6.6 Average change in specific aspects of behaviour
7. Adverse effects ‐ general and specific (Important adverse effects included movement disorders, weight gain, fits and blood reactions leading to therapy discontinuation)
7.1 Clinically important general adverse effects
7.2 Average endpoint general adverse effect score
7.3 Average change in general adverse effect scores
7.4 Clinically important specific adverse effects
7.5 Average endpoint specific adverse effects
7.6 Average change in specific adverse effects
8. Satisfaction with treatment (including subjective well‐being and family burden)
8.1 Leaving the studies early
8.2 Recipient of care not satisfied with treatment
8.3 Recipient of care average satisfaction score
8.4 Recipient of care average change in satisfaction scores
8.5 Carer not satisfied with treatment
8.6 Carer average satisfaction score
8.7 Carer average change in satisfaction scores
9. Quality of life
9.1 Clinically important change in quality of life
9.2 Average endpoint quality of life score
9.3 Average change in quality of life scores
9.4 Clinically important change in specific aspects of quality of life
9.5 Average endpoint specific aspects of quality of life
9.6 Average change in specific aspects of quality of life
10. Economic outcomes
10.1 Direct costs
10.2 Indirect costs
11. Cognitive functioning
11.1 Clinically important change in cognitive functioning
11.2 Average endpoint cognitive functioning score
11.3 Average change in cognitive functioning scores
11.4 Clinically important change in specific aspects of cognitive functioning
11.5 Average endpoint specific aspects of cognitive functioning
11.6 Average change in specific aspects of cognitive functioning
12. Summary of findings table
We will use the Grading of Recommendations Assessment, Development and Evaluation (GRADE) approach to interpret findings (Schünemann 2011). We will use the software GRADEpro (GRADEpro) to import data from the Cochrane Collaboration statistical software, Review Manager (RevMan), 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.
1. Global state
1.1 Global state improvement (any time frame).
1.2 Relapse as defined by each study (any time frame).
2 . Mental state
2.1 Clinically important change in general mental state (any time frame).
3. General functioning
3.1 Clinically important change in general functioning including working ability (any time frame).
4. General behaviour
4.1 Clinically important change in general behaviour (any time frame).
5. Quality of life
5.1 Clinically important change in quality of life (any time frame).
Search methods for identification of studies
Electronic searches
1. Cochrane Schizophrenia Group Specialised Register
The Trials Search Co‐ordinator of the Cochrane Schizophrenia Group will search the Group's Specialised Register (http://onlinelibrary.wiley.com/o/cochrane/clabout/articles/SCHIZ/frame.html) using the following search terms:
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(haloperi* or R‐1625 or haldol* or alased* or aloperidi* or bioperido* or buterid* or ceree* or dozic* or duraperido* or fortuna* or serena* or serenel* or seviu* or sigaperid* or sylad* or zafri*) in Title or Abstract of REFERENCE or (haloperi* or R‐1625 or haldol* or alased* or aloperidi* or bioperido* or buterid* or ceree* or dozic* or duraperido* or fortuna* or serena* or serenel* or seviu* or sigaperid* or sylad* or zafri*) in Intervention of STUDY
The Cochrane Schizophrenia Group'ss Specialised Register 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, hand‐searches, grey literature, and conference proceedings.
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
All seven review authors will independently scrutinise the abstracts of retrieved studies. Where disputes arise, we will acquire the full reports for more detailed scrutiny. All seven authors will inspect the full reports of the abstracts meeting the review criteria will be inspected by all seven review authors in order to ensure reliable selection. Where it is not possible to resolve disagreement by discussion, one author (AE) will act as the final arbiter and we will attempt to contact the authors of the study for clarification.
Data extraction and management
1. Extraction
Four authors (KT, SAD, AAD, MRDA) will extract data from all included studies. In addition, to ensure reliability, two authors (MEM, NAM) will independently extract data from all included studies. We will discuss any disagreement will be discussed, decisions documented and, if necessary, we will contact the authors of studies for clarification. With any remaining problems, one author (AE) will help clarify issues and we will document these final decisions.
We will extract data presented only in graphs and figures wherever possible, but they will only be included if two authors independently reach 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. For Multicentre studies, 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:
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the psychometric properties of the measuring instrument have been described in a peer‐reviewed journal (Marshall 2000); and
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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 a self‐report or completed by an independent rater or relative (not the therapist). We realise that this is not often reported clearly, and we will include the relevant information in the 'Description of studies' section in the full review.
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 to primarily 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 will use mean differences (MDs) rather than standardised mean differences (SMDs) 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:
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standard deviations (SDs) and means are reported in the paper or obtainable from the authors;
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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);
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if a scale started from a positive value (such as the Positive and Negative Syndrome Scale) , which can have values from 30 to 210) (Kay 1986), 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 as 'other data' within the data and analyses section rather than enter such data into statistical analyses.
When continuous data are presented on a scale that includes a possibility of negative values (such as change data), it is difficult to tell whether data are skewed or not. We will present and enter change data into 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 every effort to convert outcome measures to dichotomous data. This can be achieved 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 or the Positive and Negative Syndrome Scale (Kay 1986; Overall 1962), 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 haloperidol discontinuation. 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. We will note this in the relevant graphs.
Assessment of risk of bias in included studies
Review authors (KT, SAD, AAD, MRDA, MEM and NAM) will work independently to assess risk of bias using criteria described in the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011). 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.
We will resolve any disagreement by consensus, with the involvement of an arbiter (AE). 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 a 'Summary of findings' table.
Measures of treatment effect
1. Binary data
For binary outcomes, we will calculate standard estimation of the risk ratios (RRs) and their 95% confidence intervals (CIs). It has been shown that RR is more intuitive than odds ratios (ORs) (Boissel 1999), and that ORs tend to be interpreted as RRs by clinicians (Deeks 2000). The number needed to treat (NNT) or number needed to harm (NNH) statistics with their CIs are intuitively attractive to clinicians, but they are problematic in terms of accurate calculation in meta‐analyses and their subsequent interpretation (Hutton 2009). For binary data presented in the 'Summary of findings' tables, where possible, we will calculate illustrative comparative risks.
2. Continuous data
For continuous outcomes, we will estimate MDs between groups. We prefer not to calculate effect size measures (SMDs). 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. If SMDs are used, this will only be calculated for endpoint data.
Unit of analysis issues
1. Cluster trials and cross‐over trials
We do not anticipate that drug discontinuation studies would use cluster randomisation or cross‐over designs, and in the unlikely event that we do encounter such designs, we will use methods described in the Cochrane Handbook for Systemic reviews of Interventions to avoid 'Unit of analysis' issues in data synthesis (Higgins 2011).
2. 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, these will be simply added and combined within a two‐by‐two table. If data are continuous, we will combine data following the guidance in 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 an asterisk (*) 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 testing how prone the primary outcomes are to change when data only from people who complete the study to that point are compared to the intention to treat analysis using the above assumptions.
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 (SDs)
If SDs are not reported, we will first try to obtain the missing values from the authors. If not available, where there are missing measures of variance for continuous data, but an exact standard error (SE) and CIs available for group means, and either P value or 't' value available for differences in mean, we can calculate them according to the rules described in the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011):
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when only the SE is reported, SDs are calculated by the formula: SD = SE * square root (n).
The Cochrane Handbook for Systemic reviews of Interventions presents detailed formula for estimating SDs from P values, t or F values, CIs, ranges or other statistics (Higgins 2011). 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 (LOCF)
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, we will fully 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. When such methodological outliers arise, we will discuss these in detail.
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 both the magnitude and direction of effects as well as the strength of evidence for heterogeneity (e.g. P value from Chi2 test, or CIs for I2). We will interpret I2 estimates greater than or equal to around 50% accompanied by a statistically significant Chi2 statistic as evidence of substantial levels of heterogeneity (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 greater detail in 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 to those in the published report. If the protocol is not available, we will compare outcomes listed in the 'Methods' section of the trial report with the actual 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 detail in 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 ten 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 a fixed‐effect model for all analyses. The reader is, however, able to choose to inspect the data using the random‐effects model.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses
Clinical state, stage or problem
We propose to undertake this review and provide an overview of the effects of haloperidol discontinuation for people with schizophrenia in general. In addition, 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, we will report this in the full review. First, we will investigate whether data has been entered correctly. Second, if data is correct, we will visually inspect the graph and we will remove studies outside of the company of the rest to see if homogeneity is restored.
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 we will employ all data from these studies.
2. Assumptions for lost binary data
Where assumptions have to be made regarding people lost to follow‐up (Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumptions and when we use data only from people who complete the study to that point. If there is a substantial difference, we will report results and discuss them but will continue to employ our assumption.
Where assumptions have to be made regarding missing SDs data (Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumptions and when we use data only from people who complete the study to that point. We will undertake a sensitivity analysis to test how prone results are to change when completer‐only data only are compared to the imputed data using the above assumption. If there is a substantial difference, we will report results and discuss them but will continue to employ our assumption.
3. Risk of bias
We will analyse the effects of excluding trials that are judged to be at high risk of bias across one or more of the domains of randomisation (implied as randomised with no further details available) allocation concealment, blinding and outcome reporting for the meta‐analysis of the primary outcome. If the exclusion of trials at high risk of bias does not substantially alter the direction of effect or the precision of the effect estimates, we will include data from these trials in the analysis.
4. Imputed values
We will undertake a sensitivity analysis to assess the effects of including data from trials where we used imputed values. 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 model
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.
