Non‐clozapine antipsychotic combinations for treatment‐resistant schizophrenia
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the effects (benefits and harms) of non‐clozapine antipsychotic combinations for people with treatment‐resistant schizophrenia.
Background
Description of the condition
Schizophrenia is a chronic, relapsing and debilitating neuropsychiatric disorder. Antipsychotic medication remains the mainstay of treatment, however of those on adequate antipsychotic therapy, about one third fail to respond, and persist with positive symptoms such as hallucinations and delusions, and negative symptoms such as apathy or poor social functioning (Meltzer 1997). These patients are often described as having treatment‐resistant schizophrenia (TRS). Despite the concept being clinically intuitive, attempts at operationalising the criteria for TRS have yielded disparate definitions. Most are iterations of the definition endorsed by the World Federation of Societies of Biological Psychiatry, which defines TRS as the lack of significant improvement of psychopathology and/or target symptoms despite treatment with two different antipsychotics from at least two different chemical classes (at least one should be an atypical antipsychotic) at the recommended dosages for a period of at least 2 to 8 weeks per drug (Hasan 2012). Another often accepted operational definition of TRS used in clinical trials is one to three failed antipsychotic attempts, with each having a duration of more than 4 to 6 weeks at the dose equivalent to 400 to 1000 mg of chlorpromazine, which is similar to the Kane criteria based on his landmark clozapine trial (Kane 1988; Suzuki 2012).
TRS affects about 7.8 million people worldwide, with clozapine refractory TRS affecting about 4.68 million (Eaton 2008; Kane 1988). Its significance cannot be understated, with close to 60% of people with schizophrenia failing to achieve response after 23 weeks of antipsychotic therapy, and mean quality of life about 20% lower than that of patients in remission (Kennedy 2014). A recent published Global Burden of Disease Study placed it in the top 20 diseases for mean years lost to disability (YLD), with a significant jump of 52% from the 1990s baseline (Global Burden 2015). Patients experiencing TRS can continue to hear voices or contend with ongoing delusional beliefs. Whilst the positive symptoms are easier to elicit, persistence of negative symptoms and cognitive deficits are harder to elicit and most patients do not spontaneously report these unless specifically looked for. These, however, lead to significant decline in functional outcomes. A recent survey in Australia ‐ the Survey of High Impact Psychosis (SHIP) demonstrated that more than 40% of patients who were adequately treated remained symptomatic, and life expectancy is reduced by at least 10 years due to risk of suicide alone, not withstanding the devastating effects of smoking and metabolic syndrome (Morgan 2012). Patients with TRS showed the poorest achievements in functional milestones of everyday living compared to those with other chronic psychiatric conditions, with most being unemployed, unable to live independently, and lacking any sentimental relationships (Iasevoli 2015). TRS is also very costly, costing 3 to 11 times more per patient for care than other patients with schizophrenia (Kennedy 2014).
Description of the intervention
For patients with TRS, when clozapine is either not an option or has not worked, the common alternatives considered are combination antipsychotics. This usually involves combining a first‐generation antipsychotic (FGA) with a second‐generation antipsychotic (SGA), followed by other combinations such as FGA + FGA, then SGA + SGA (Correll 2012). One of the hypotheses for this rationale is to combine serotonin blocking agents with dopamine blockers. A recent review documented 19 studies on SGA + SGA, 4 studies on FGA + FGA, 3 studies on SGA + FGA and 2 studies on FGA + SGA, excluding clozapine for the treatment of patients with schizophrenia (Galling 2016). Commonly used SGA + SGA in that review were aripiprazole plus risperidone and sulpiride plus olanzapine. With no single accepted non‐clozapine antipyschotic combination therapy (NCCAT) demonstrating significant and sustained benifit, different combinations are often trialled and tried in patients with schizophrenia. For example, aripiprazole has been combined with either quetiapine or risperidone and studied for efficacy and tolerability in patients with schizophrenia (Kane 2009). Another study compared aripiprazole plus haloperidol to haloperidol alone, showing amelioration of prior hyperprolactinemia (Shim 2007). Other studies have combined olanzapine with ziprasidone where there was no significant improvement observed for fasting glucose, insulin resistance, hyperlipidaemia and obesity, compared to clozapine plus ziprasidone (Henderson 2009). Seven different combinations were reported in case studies for a review, including amisulpiride plus olanzapine, olanzapine plus risperidone, and quetiapine plus risperidone (Chan 2007). Given the broad chemical and pharmacological heterogeneity of antipsychotic agents, many different NCCAT are used in clinical studies and in practice.
How the intervention might work
The lack of any pharmacological rationale for combining antipsychotics with the same putative antipsychotic dopamine D2 receptor blockade has been criticised (Correll 2012). However, the efficacy of clozapine in spite of its modest D2 blockade and the activity of different antipsychotics on a variety of non‐D2 receptors suggest the possibility that efficacy of antipsychotic combination treatment may relate to a more optimal suite of action on such a spectrum of receptors. Moreover, employing lower doses of two antipsychotics may mitigate unpleasant or harmful side effects, given the different side‐effect profile of the antipsychotics. For example, the addition of either amisulpride or risperidone to olanzapine or quetiapine may result in improvement in the D2 receptor antagonism but with a better side‐effect profile, as olanzapine or quetiapine have a reduced tendency to cause extrapyramidal side effects or prolactin elevation (Chan 2007).
Why it is important to do this review
The current mainstay treatment for TRS is the antipyschotic clozapine (Hasan 2012). However, 40% to 70% of TRS patients are resistant to clozapine (Chakos 2001). In addition, of those on clozapine, 17% discontinue due to intolerance to clozapine’s side effects (Young 1998). For those who have been challenged again with clozapine after life‐threatening adverse effects, failure rate remains high for agranulocytosis and myocarditis (Manu 2012). It is also contraindicated in patients with multiple comorbidities such as active liver disease and pre‐existing cardiovascular diseases, which are common in people with schizophrenia (Chwastiak 2014; Naheed 2001). The mandatory, frequent haematological monitoring in some countries can also cause much inconvenience to some patients (Alvir 1994).
Clinicians then need to consider NCCAT as a last‐line solution for TRS.
Indeed, the fact that antipsychotic combination treatment has been estimated to be prescribed to 10% to 50% of patients (Hasan 2012), is testament to both the prevalence of TRS and the inadequacy of monotherapy. Furthermore, clozapine displays both partial dopaminergic antagonism and serotonergic antagonism which are postulated to be implicated in its efficacy in TRS (Meltzer 1989). Thus NCCAT can be employed for patients who are intolerant to, contraindicated or who have refused clozapine, by optimisation of the two neurotransmission pathways, leading to better efficacy and reduced side effects.
Reviews to date have largely focused on clozapine antipsychotic combination treatments in TRS (Cipriani 2009) or antipsychotic combination treatments in schizophrenia in general (Correll 2012). Consequently, there is a lack of good quality evidence regarding the efficacy or tolerability of non‐clozapine combinations in TRS. This review will address this gap.
Objectives
To assess the effects (benefits and harms) of non‐clozapine antipsychotic combinations for people with treatment‐resistant 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.
Types of participants
Adults, aged over 18 years, however defined, with treatment‐resistant schizophrenia.
We are interested in making sure that information is as relevant to the current care of people with schizophrenia as possible, and aim to highlight the current clinical state (acute, early post‐acute, partial remission, remission), and the stage (prodromal, first episode, early illness, persistent) of participants. We also aim, where possible, to highlight studies with people having a particular problem (for example, negative symptoms).
Types of interventions
1. Intervention
Antipsychotic combination: treatment that involves more than one antipsychotic medication, none of which is clozapine: any dose, any route of delivery.
2. Comparator
Treatment with either placebo or one or more antipsychotic medications with or without additional placebo medications: any dose, any route of delivery.
Types of outcome measures
We aim to divide outcomes into short term (less than 6 months), medium term (7 to 12 months) and long term (over 1 year).
Primary outcomes
1. Leaving the study early
2. Global state
2.1 Clinically‐important change in global state ‐ as defined by each of the studies
2.2 Relapse ‐ as defined by each of the studies
Secondary outcomes
1. Global state
1.1 Any change in global state
1.2 Average endpoint/change score in global state scale
2. Mental state
2.1 Clinically‐important change in mental state ‐ as defined by individual studies
2.2 Any change in mental state ‐ as defined by individual studies
2.3 Average endpoint/change score in mental state scales
2.4 Clinically‐important change in positive symptoms ‐ as defined by individual studies
2.5 Average endpoint/change score in positive symptoms scales
2.6 Clinically‐important change in negative symptoms ‐ as defined by individual studies
2.7 Average endpoint/change score in negative symptoms scales
2.8 Clinically‐important change in aggression/agitation symptoms ‐ as defined by individual studies
2.9 Average endpoint/change score in aggression/agitation symptoms scales
3. Service use
3.1 Hospital admission
3.2 Days in hospital
3.3 Change in hospital status
4. Behaviour
4.1 Clinically‐important change in behaviour ‐ as defined by individual studies
4.2 Any change in behaviour ‐ as defined by individual studies
4.3 Average endpoint/change score in behaviour scales
4.4 Specific behaviours
4.4.1 Employment status during trial (employed/unemployed)
4.4.2 Occurrence of violent incidents (to self, others, or property)
4.4.3 Level of substance abuse
5. Social functioning
5.1 Clinically‐important change in social functioning ‐ as defined by individual studies
5.2 Any change in social functioning ‐ as defined by individual studies
5.3 Average endpoint/change score in social functioning scales
6. Adverse effects
6.1 Any serious adverse events
6.2 Adverse events requiring hospitalisation
6.3 Specific adverse effects
6.3.1 Allergic reactions
6.3.2 Blood dyscrasia such as agranulocytosis
6.3.3 Central nervous system (ataxia, nystagmus, drowsiness, fits, diplopia, tremor)
6.3.4 Death (suicide and non‐suicide deaths)
6.3.5 Endocrinological dysfunction (hyperprolactinaemia)
6.3.6 Weight gain
6.3.7 Movement disorders (extrapyramidal side effects)
7. Quality of life
7.1 Clinically‐important change in quality of life ‐ as defined by individual studies
7.2 Any change in quality of life ‐ as defined by individual studies
7.3 Average endpoint/change score in quality of life scales
8. Economic (cost of care)
8.1 Direct costs
8.2 Indirect costs
'Summary of findings' table
We will use the GRADE approach to interpret findings (Schünemann 2011) 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 rated as important to patient care and decision making. We aim to select the following main outcomes for inclusion in the 'Summary of findings' table.
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Leaving the study early.
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Global state: clinically‐important change ‐ as defined by individual studies.
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Global state: relapse ‐ as defined by individual studies.
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Mental state: clinically‐important change ‐ as defined by individual studies.
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Adverse effects ‐ any serious adverse event.
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Adverse effects ‐ specific: movement disorders.
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Quality of life ‐ clinically‐important change ‐ as defined by individual studies.
Search methods for identification of studies
Electronic searches
Cochrane Schizophrenia Group's Study‐Based Register of Trials
The information specialist will search the Cochrane Schizophrenia Group's Study‐Based Register of Trials using the following search strategy:
*Treatment Resistant* in Healthcare Conditions of STUDY
In such a study‐based register, searching the major concept retrieves all the synonym keywords and relevant studies because all of 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 are 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. We will note the outcome of this contact in the tables 'Characteristics of included studies' or 'Characteristics of studies awaiting classification'.
Data collection and analysis
Selection of studies
AY will independently inspect all citations from the searches and identify relevant abstracts. A random 20% sample will be independently inspected by MJ to ensure reliability. Where disputes arise, we will acquire the full report for more detailed scrutiny. AY will obtain and inspect full reports of the abstracts meeting the review criteria. Again, MJ will also inspect a random 20% of these 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
AY will extract data from all included studies. In addition, to ensure reliability, MJ will independently extract data from a random sample of these studies, comprising 10% of the total. Again, we will discuss and document any disagreement and, if necessary, will contact authors of studies for clarification. With remaining problems MJ 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. 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 multicentre, 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 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 prefer to use mean differences (MD) rather than standardised mean differences (SMD) throughout (Higgins 2011b).
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 standards described below to all data before inclusion.
Please note, we will enter data from studies of at least 200 participants, in the analysis irrespective of the following rules, because skewed data pose less of a problem in large studies. 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.
For 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. If this value is lower than one, it strongly suggests a skew and we will exclude such data. If this ratio is higher than one but below two, 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 two we will include these data because skew is less likely (Altman 1996; Higgins 2011b);
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 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.
2.5 Common measure
To facilitate comparison between trials, we aim 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 PANSS (Kay 1986), this could be considered as a clinically‐significant response (Leucht 2005a; Leucht 2005b). If data based on these thresholds are not available, we will use the primary cut‐off presented by the original authors.
2.7 Direction of graphs
Where possible, we will enter data in such a way that the area to the left of the line of no effect indicates a favourable outcome for non‐clozapine combination therapy. 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
AY and MJ will assess risk of bias by using criteria described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). This set of criteria is based on evidence of associations between overestimate of effect and high risk of bias of the study in domains such as sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting.
If the raters disagree, we will make the final rating 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 'Risk of bias' assessment, but if disputes arise as to which rating 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 (ORs) and that ORs tend to be interpreted as RRs by clinicians (Deeks 2000). 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 (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 contact authors of such 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 obtained statistical advice 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 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, 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). If for any particular outcome, more than 50% of data are 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 downgrading quality. Finally, we will also downgrade quality within the 'Summary of findings' table/s should loss be 255 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 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 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
If standard deviations 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 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 standard error (SE) is reported, standard deviations (SDs) are calculated by the formula SD = SE * square root (n). Chapters 7.7.3 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) present detailed formula for estimating SDs from Pvalues, t or F values, confidence intervals, ranges or other statistics. If these formula do not apply, we will calculate the SDs according to a validated imputation method which is based on the SDs of the other included studies (Furukawa 2006). Although some of these imputation strategies can introduce error, the alternative would be to exclude a given study’s outcome and thus to lose information. We nevertheless will examine the validity of the imputations in a sensitivity analysis excluding imputed values.
3.3 Assumptions about participants who left the trials early or were lost to follow‐up
Various methods are available to account for participants who left the trials early or were lost to follow‐up. Some trials just present the results of study completers, others use the method of last observation carried forward (LOCF), while more recently methods such as multiple imputation or mixed effects models for repeated measurements (MMRM) have become more of a standard. While the latter methods seem to be somewhat better than LOCF (Leon 2006), we feel that the high percentage of participants leaving the studies early and differences in the reasons for leaving the studies early between groups is often the core problem in randomised schizophrenia trials. We will therefore not exclude studies based on the statistical approach used. However, we will preferably use the more sophisticated approaches. For example, we will prefer to use MMRM or multiple imputation to LOCF and will only present completer analyses if some kind of ITT data are not available at all. Moreover, we will address this issue in the item 'incomplete outcome data' of the 'Risk of bias' tool.
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 fully 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. 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 value, as evidence of substantial levels of heterogeneity (Section 9.5.2, Higgins 2011b). 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 (Sterne 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 the results that were actually reported.
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 (Sterne 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 will use the random‐effects model for all analyses.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses
1.1 Primary outcomes
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Dose of antipsychotic
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Choice of comparison
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Setting
1.2 Clinical state, stage or problem
We propose to undertake this review and provide an overview of the effects of antipsychotic combinations 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
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 studies outside of the company of the rest 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, and will discuss 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 outcomes if inclusion of their data 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 (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumption/s and when we use data only from people who complete the study to that point. A sensitivity analysis will be undertaken testing 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 primary outcome. If the exclusion of data from trials at high risk of bias does not substantially alter the direction of effect or the precision of the effect estimates, then these 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‐effect and random‐effects
We aim to synthesise all data 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 result.
