Mood stabilisers for schizoaffective disorder
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To investigate the effects of mood‐stabilising agents for people with schizoaffective disorder.
Background
Description of the condition
Schizoaffective disorder is one of the serious and enduring mental illnesses characterised by a combination of schizophrenia‐like psychotic symptoms such as thought disorder, hallucinations or delusions and the depressive or manic symptoms of an affective disorder. The term 'schizoaffective' was first used by Jacob Kasanin in 1933 to describe a group of patients with acute psychoses that contained both schizophrenic and affective features (Kasanin 1994). This diagnosis has retained its place in the two most commonly used psychiatric classification systems (Diagnostic and Statistical Manual of Mental Disorders (DSM) and International Classification of Diseases (ICD)) (Levinson 1999).
In the absence of any reliable studies, the frequency of schizoaffective disorder is considered to be somewhere in the range of 0.5% to 0.8%. Of those people admitted to psychiatric wards for functional psychosis, a sizeable proportion (10% to 30%) are diagnosed with schizoaffective disorder (Malhotra 2007).
The prognosis of people with schizoaffective disorder is better than those with schizophrenic disorder but worse than those with a diagnosis of mood disorder (Levinson 1999). It is very difficult to predict the prognosis of any individual person with a diagnosis of schizoaffective disorder. Nevertheless, there are some indicators associated with poor prognosis in schizoaffective disorder such as limited premorbid functioning, an insidious onset of illness with no obvious precipitating factors, a predominant psychosis with conspicuous negative symptoms, an early onset, an unremitting course and a family history of schizophrenia. Ten per cent of people with schizoaffective disorder are reported to commit suicide, which is similar to the rate for schizophrenia (Brannon 2010).
Description of the intervention
Several medications are used to treat schizoaffective disorder and the selection of one or other treatments depends on whether the depressive or manic subtype is present. In the depressive subtype, antidepressants, antipsychotic and mood‐stabilising agents are prescribed individually or in combination. In the manic subtype, mood stabilisers and antipsychotics are given separately or simultaneously. For the purpose of this review, we will only evaluate mood‐stabilising agents as a therapeutic intervention in schizoaffective disorder.
The American Psychiatric Association's (APA) guideline for treatment of people with bipolar disorder defines mood stabilisers as "medications with both antimanic and antidepressive actions." (APA 1994). Mood‐stabilising agents are "a functional category of drugs used to normalise mood, particularly by dampening mood swings (for example lithium and some anticonvulsants, carbamazepine and valproic acid)” (Stedman 2006).
How the intervention might work
Mood‐stabilising agents are a very diverse group of chemicals with very different set of pharmacokinetic and pharmacodynamic properties. It is virtually impossible to pin them down to a single mode of action. Mood fluctuations in schizoaffective disorder are associated with wide changes in the inherent rhythmicity of the human brain and mood‐stabilising agents seem to attenuate those extreme circadian rhythms. They appear to have multiple potential sites of action that could account for their psychotropic effects. A common physiological property of mood‐stabilising agents is their anticonvulsant action and it is known to be closely associated with several neurotransmitter and ion‐channel systems.
It is proposed that lithium exerts a common effect on the overactive processes that mediate the opposite mood phases of mania and depression. Lithium is suggested to attenuate i. the increased dopaminergic or noradrenergic tone thought to be associated with mania and, ii. the depression‐related increases in acetylcholinergic tone (Jope 1999). Hence, we observe the paradox of lithium's usefulness in both extremes of mood state. Lithium may exert a neuroprotective effect at more than one site or signalling pathway within the neurons and also increase neurogenesis in the dentate gyrus area of the hippocampal region ‐ a similar change to that seen after antidepressant treatment (Chen 2000).
The literature includes theories that valproate may play a role by working as gamma‐aminobutyric acid (GABA) agonist, acting directly or indirectly by enhancing GABA receptor activity or inhibiting GABA metabolism, or both. It has also been associated with neuroprotective activity in the shape of upregulating the expression of the neuroprotective endoplasmic reticulum stress proteins and the anti‐apoptotic protein. Carbamazepine and lamotrigine are not believed to work through GABAergic mechanisms, but it is postulated that their tranquillising effect may be responsible for their mood‐stabilising properties. Topiramate is also known to augment the inhibitory neurotransmitter GABA via different mechanisms and also inhibits the excitatory neurotransmitter glutamate via the kainate/AMPA receptor. Furthermore, topiramate is known to block voltage‐sensitive sodium and calcium channels. These mechanisms have been considered therapeutically useful in the treatment of affective and schizoaffective disorder.
Besides modifications in neurotransmission and receptor regulation, mood‐stabilising agents have been theorised to bring about specific transcription factors, which in turn provide some enhancement of neuroprotection and neuronal survival (Young 2002).
When mood‐stabilising agents are combined with other medication, they introduce considerations such as drug interactions and additional side effects. The interactions are complex, often very useful, but potentially dangerous. (Freeman 1998). Almost all mood‐stabilising agents carry the risk of teratogenicity. Their use in women of child‐bearing age is controversial and poses significant clinical difficulty at times, when a woman with stabilised schizoaffective disorder taking a mood‐stabilising agent decides to plan a family. Ongoing research to identify mood‐stabilising agents with no teratogenic risk has had limited success to date. Consequently, the study of valnoctamide as a replacement for valproate is included in the review (Bersdusky 2005).
Why it is important to do this review
Whether or not a discrete ‘schizoaffective’ disease entity exists, a group of people do present in clinical practice with a combination of psychotic and affective symptoms (depression or elated mood) and it appears logical to address both sets of symptoms simultaneously. Anecdotal evidence suggests that mood‐stabilising agents are frequently used in those circumstances. However, use of mood‐stabilising agents exposes patients to the risk of additional adverse effects and possibility of undesirable interaction with other drugs. It is essential to quantify their therapeutic advantages to weigh the risk/benefit ratio in helping people make informed decisions about the management of their illness.
According to our search, there are no published systematic reviews or meta‐analyses that specifically address the role of mood‐stabilising agents in the management of schizoaffective disorder. This systematic review has been planned with a view to fill this evidence gap by reviewing the need and comparative efficacy of mood‐stabilising agents as sole medication or adjunctive treatment in schizoaffective disorder.
Objectives
To investigate the effects of mood‐stabilising agents for people with schizoaffective disorder.
Methods
Criteria for considering studies for this review
Types of studies
All relevant randomised controlled trials. If a trial is described as 'double blind' but implies randomisation, we will include such trials in a sensitivity analysis (see Sensitivity analysis). If their inclusion does not result in a substantive difference, they will remain in the analyses. If their inclusion does result in 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 such as antipsychotic medications within the group receiving mood‐stabilising agents, we will only include the data if the adjunct treatment is evenly distributed between groups and it is only the mood‐stabilising agent that is randomised.
Types of participants
Adults, with schizoaffective disorder diagnosed by any means.
We are interested in making sure that information is as relevant to the current care of people with schizoaffective disorder as possible so propose to clearly highlight the current clinical state (acute, early post‐acute, partial remission, remission), current mood state (depressive, manic or mixed) 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, mood symptoms, negative symptoms, treatment‐resistant illnesses).
Types of interventions
1. Sole use of any mood‐stabilising agent*: any dose
2. Adjunctive use of any mood‐stabilising agent ‐ in combination with any antipsychotic treatment: any dose
versus
3. Placebo (or no intervention)
4. Any mood‐stabilising agent alone (other than used in the first group): any dose
5. Any antipsychotic drug alone: any dose
6. Adjunctive use of any mood‐stabilising agent (other than used in the first group) ‐ in combination with any antipsychotic treatment: any dose
7. Adjunctive use of placebo (or no intervention) ‐ in combination with any antipsychotic treatment
*Mood‐stabilising agent: Lithium or anticonvulsants such as carbamazepine, oxcarbazepine, sodium valproate, semisodium valproate valnoctamide, topiramate, phenytoin, lamotrigine, gabapentin or any other approved antiepileptic drug.
Types of outcome measures
We will group outcomes into short‐term (up to 12 weeks), medium‐term (13 to 26 weeks) and long‐term (over 26 weeks).
Primary outcomes
1. Global state
1.1 Clinically important change in global state
Clinically important response as defined by individual studies (e.g. global impression much improved or more than 50% reduction on a rating scale).
Secondary outcomes
1. Leaving the study early
1.1 For specific reasons
1.2 For general reasons
2. Service utilisation
2.1 Hospital admission
2.2 Days in hospital
2.3 Any change in hospital status
3. Global state
3.1 Relapse ‐ as defined by each of the studies
3.2 Time to relapse
3.3 Any change in global state
3.4 Average endpoint global state score
3.5 Average change in global state scores
4. Mental state
4.1 General mental state
4.1.1 Clinically important change in general mental state ‐ as defined by each of the studies
4.1.2 Any change in general mental state
4.1.3 Average endpoint general mental state score
4.1.4 Average change in general mental state scores
4.2 Specific aspects of mental state
4.2.1 Clinically significant response in positive symptoms ‐ as defined by each of the studies
4.2.2 Any change in positive symptoms
4.2.3 Average endpoint positive symptom score
4.2.4 Average change in positive symptom scores
4.2.5 Clinically significant response in negative symptoms ‐ as defined by each of the studies
4.2.6 Any change in negative symptoms
4.2.7 Average endpoint negative symptom score
4.2.8 Average change in negative symptom scores
4.2.9 Clinically significant response in depressive symptoms ‐ as defined by each of the studies
4.2.10 Any change in depressive symptoms
4.2.11 Average endpoint depressive symptom score
4.2.12 Average change in depressive symptom scores
4.2.13 Clinically significant response in manic symptoms ‐ as defined by each of the studies
4.2.14 Any change in manic symptoms
4.2.15 Average endpoint manic symptom score
4.2.16 Average change in manic symptom scores
5. Behaviour
5.1 General behaviour
5.1.1 Clinically important change in general behaviour
5.1.2 Any change in general behaviour
5.1.3 Average endpoint general behaviour score
5.1.4 Average change in general behaviour scores
5.1.5 Compulsory administrations of treatment
5.1.6 Use of adjunctive medication
5.2 Specific behaviours
5.2.1 Self‐harm, including suicide
5.2.2 Injury to others
5.2.3 Aggression
5.2.3.1 Clinically important change in aggression
5.2.3.2 Any change in aggression
5.2.3.3 Average endpoint aggression score
5.2.3.4 Average change in aggression scores
5.2.4 Self care
5.2.4.1 Clinically important change in self care
5.2.4.2 Any change in self care
5.2.4.3 Average endpoint self care score
5.2.4.4 Average change in self care scores
5.2.5 Compliance
5.2.5.1 Clinically important change in compliance
5.2.5.2 Any change in compliance
5.2.5.3 Average endpoint compliance score
5.2.5.4 Average change in compliance scores
6. Social functioning
6.1 Clinically important effects for social function
6.2 Any effects for social function
6.3 Average endpoint social functioning score
6.4 Average change social functioning scores
6.5 Employment status during trial (employed/unemployed)
7. Adverse effects
7.1 Clinically important general adverse effects
7.2 Any general adverse effects
7.3 Average endpoint general adverse effect score
7.4 Average change in general adverse effect scores
7.5 Clinically important change in specific adverse effects such as movement disorders
7.6 Any change in specific adverse effects
7.7 Average endpoint specific adverse effects
7.8 Average change in specific adverse effects
7.9 Use of antiparkinsonian treatment
8. Sudden and unexpected death
9. Economic outcomes
9.1 Direct costs
9.2 Indirect costs
10. Satisfaction with treatment
10.1 Recipient of care satisfied with treatment
10.2 Recipient of care average satisfaction score
10.3 Recipient of care average change in satisfaction scores
10.4 Carer satisfied with treatment
10.5 Carer average satisfaction score
10.6 Carer average change in satisfaction scores
11. Quality of life
11.1 Clinically important change in quality of life
11.2 Any change in quality of life
11.3 Average endpoint quality of life score
11.4 Average change in quality of life scores
11.5 Clinically important change in specific aspects of quality of life
11.6 Any change in specific aspects of quality of life
11.7 Average endpoint specific aspects of quality of life
11.8 Average change in specific aspects of quality of life
12. Pharmacokinetic interactions
12.1 Any change of plasma levels of other psychotropic medication
Search methods for identification of studies
We will not apply any language restrictions within the limitations of the search tools.
Electronic searches
1. Cochrane Schizophrenia Group Trials Register
We will search the register using the phrase:
[((*schizoaffective* or *schizo‐affective* in title in REFERENCE) OR (*schizoaffective* in Health Care Conditions of STUDY)) AND (*lithium* OR *Valproate* OR *Valproic acid* OR *carbamazepine* OR *oxcarbazepine* OR *lamotrigine* OR *topiramate* OR *phenytoin* OR *mood stabili* in interventions of STUDY)].
This register is compiled by systematic searches of major databases, handsearches and conference proceedings (see group module).
Searching other resources
1. Reference searching
We will search all references of articles selected for inclusion for further relevant trials.
2. Personal contact
We will try to contact the first author of all included studies and some excluded studies to seek any information regarding unpublished trials.
Data collection and analysis
Selection of studies
One review author (RA) will independently inspect citations from the searches and identify relevant abstracts. A second review author (VN) will independently re‐inspect a random 20% sample to ensure reliability. Where disputes arise, we will acquire the full report for more detailed scrutiny. RA will obtain and inspect full reports of the abstracts meeting the review criteria. Again, VN will re‐inspect a random 20% of 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 author RA will extract data from all included studies. In addition, to ensure reliability, VN will independently extract data from a random sample of these studies, 20% of the total. Again, we will discuss any disagreement and document our decisions and, if necessary, we will contact the authors of studies for clarification. With remaining problems, VN will help clarify issues and we will document these final decisions. Whenever possible, we will extract data presented only in graphs and figures, but we will only include the data 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 will use mean differences (MD) rather than standardised mean differences (SMD) throughout (Higgins 2011, Chapter 9.4.5.2 ).
2.4 Skewed data
Continuous data on clinical and social outcomes are often not normally distributed. To avoid the pitfall of applying parametric tests to non‐parametric data, we aim to apply the following standards to all data before inclusion: a) standard deviations (SDs) and means are reported in the paper or obtainable from the authors; b) when a scale starts from the finite number zero, the SD, when multiplied by two, is less than the mean (as otherwise the mean is unlikely to be an appropriate measure of the centre of the distribution, (Altman 1996); c) if a scale started from a positive value (such as the Positive and Negative Syndrome Scale (PANSS) which can have values from 30 to 210), we will modify the calculation described above to take the scale starting point into account. In these cases skew is present if 2 SD > (S‐S min), where S is the mean score and S min is the minimum score. Endpoint scores on scales often have a finite start and endpoint and these rules can be applied. When continuous data are presented on a scale that includes a possibility of negative values (such as change data), it is difficult to tell whether data are skewed or not. We will enter skewed data from studies of less than 200 participants in additional tables rather than into an analysis. Skewed data pose less of a problem when looking at means if the sample size is large and entered into syntheses.
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 convert outcome measures to dichotomous data. This can be done by identifying cut‐off points on rating scales and dividing participants accordingly into 'clinically improved' or 'not clinically improved'. It is generally assumed that if there is a 50% reduction in a scale‐derived score such as the Brief Psychiatric Rating Scale (BPRS, Overall 1962) or the PANSS (Kay 1986), this could be considered as a clinically significant response (Leucht 2005; Leucht 2005a). If data based on these thresholds are not available, we will use the primary cut‐off presented by the original authors.
2.7 Direction of graphs
Where possible, we will enter data in such a way that the area to the left of the line of no effect indicates a favourable outcome for mood‐stabilising agents. 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.
2.8 Summary of findings table
We will use the GRADE approach to interpret findings (Schunemann 2008) and use the GRADE profiler (GRADE PRO) 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 will rate as important to patient‐care and decision making. We plan to select the following main outcomes for inclusion in the summary of findings table,
1. Leaving the study early
2. Service Utilisation
2.1 Hospitalisation
3. Global response
3.1 Global state
3.1 Relapse
4. Mental state change
5. Adverse effects
5.1 Any adverse effect
5.2 Change in body weight
Assessment of risk of bias in included studies
Again RA and JR will independently 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, we will make the final rating by consensus, with the involvement of another member of the review group. Where inadequate details of randomisation and other characteristics of trials are provided, we will contact the authors of the studies 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 them 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). For statistically significant results, we plan to calculate the number needed to treat to provide benefit /to induce harm statistic (NNTB/H), and its 95% CI rate in the control group.
2. Continuous data
For continuous outcomes, we will estimate 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, CIs 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 attempt to contact the first authors of studies to obtain intra‐class correlation coefficients (ICC) 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 ICC and relevant data documented in the report, synthesis with other studies will be possible using the generic inverse variance technique.
2. Cross‐over trials
A major concern of cross‐over trials is the carry‐over effect. It occurs if an effect (e.g. pharmacological, physiological or psychological) of the treatment in the first phase is carried over to the second phase. As a consequence on entry to the second phase the participants can differ systematically from their initial state despite a wash‐out phase. For the same reason cross‐over trials are not appropriate if the condition of interest is unstable (Elbourne 2002). As both effects are very likely in severe mental illness, we will only use data from the first phase of cross‐over studies.
3. Studies with multiple treatment groups
Where a study involves more than two treatment arms, if relevant, we will present the additional treatment arms in comparisons. If the data are binary, we will simply add and combine them within the two‐by‐two table. If data are continuous, we will combine the 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 reproduce 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 30% of data be unaccounted for, we will not reproduce these data or use them within analyses, except for the outcome of leaving the study early. If, however, more than 30% of those in one arm of a study are lost, but the total loss was less than 30%, we will mark such data with (*) to indicate that such a result may well be prone to bias.
2. Binary
In the case where attrition for a binary outcome is between 0% and 50% and where these data are not clearly described, we will present these 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 stayed in the study ‐ in that particular arm of the trial ‐ will be used for those who did not. We will undertake a sensitivity analysis to test how prone the primary outcomes are to change when 'completer' data only are compared with the intention‐to‐treat analysis using the above assumptions.
3. Continuous
3.1 Attrition
In the case where attrition for a continuous outcome is between 0% and 30% and completer‐only data will be reported, we will reproduce these.
3.2 Standard deviations
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 are available for group means, and either P or t values are 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 formulas for estimating SDs from P, t or F values, CIs, ranges or other statistics. If these formulas 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. Nevertheless,we will examine the validity of the imputations in a sensitivity analysis excluding imputed values.
3.3 Last observation carried forward
We anticipate that in some studies the method of last observation carried forward (LOCF) will be employed within the study report. As with all methods of imputation to deal with missing data, LOCF introduces uncertainty about the reliability of the results (Leucht 2007). Therefore, where LOCF data have been used in the trial, if less than 50% of the data have been assumed, we will reproduce these data and indicate that they are the product of LOCF assumptions.
Assessment of heterogeneity
1. Clinical heterogeneity
We will consider all included studies initially, without seeing comparison data, to judge clinical heterogeneity. We will simply inspect all studies for clearly outlying people or situations which we had not predicted would arise. When such situations or participant groups arise, these will be fully discussed.
2. Methodological heterogeneity
We will consider all included studies initially, without seeing comparison data, to judge methodological heterogeneity. We will simply inspect all studies for clearly outlying methods which we had not predicted would arise. When such methodological outliers arise, these will be fully discussed.
3. Statistical heterogeneity
3.1 Visual inspection
We will visually inspect graphs to investigate the possibility of statistical heterogeneity.
3.2 Employing the I2 statistic
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 CI 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 the heterogeneity (Subgroup analysis and investigation of heterogeneity). If severe heterogeneity is present (I2 ≥ 75%) and could not be explained by differences across the trials in terms of clinical or methodological features or by subgroup analyses, we will not combine the trials in a meta‐analysis, but present the results in a forest plot (Higgins 2011).
Assessment of reporting biases
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997). These are described in Section 10 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We are aware that funnel plots may be useful in investigating reporting biases but are of limited power to detect small‐study effects. We will not use funnel plots for outcomes where there are 10 or fewer studies, or where all studies are of similar sizes. In other cases, where funnel plots are possible, we will seek statistical advice in their interpretation.
Data synthesis
We understand that there is no closed argument for preference for use of fixed‐effect or random‐effects models. The random‐effects method incorporates an assumption that the different studies are estimating different, yet related, intervention effects. This often seems to be true to us and the random‐effects model takes into account differences between studies even if there is no statistically significant heterogeneity. There is, however, a disadvantage to the random‐effects model. It puts added weight onto small studies which often are the most biased ones. Depending on the direction of effect, these studies can either inflate or deflate the effect size. Therefore, we plan to use the fixed‐effect model for all analyses. If the I2 statistic indicates substantial heterogeneity (values 50% or greater), we will present the results using fixed‐effect and random‐effects meta‐analysis and we will assess the impact of both models on the direction and precision of the effect estimate. 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 ‐ only primary outcomes
1.1 People with schizoaffective disorder presenting in a depressed, manic or mixed state
We anticipate that we will perform sub‐group analyses investigating response to treatment with mood‐stabilising agents in different mood states of schizoaffective disorder.
1.2 Clinical state, stage or management settings
We propose to undertake this review and provide an overview of the effects of mood‐stabilising agents for people with schizoaffective disorder in general. In addition, however, we will try to report data on subgroups of people in the same clinical state, stage and with similar management settings i.e. inpatient or outpatient.
2. Investigation of heterogeneity
If inconsistency is high, this will be reported. First, we will investigate whether data have been entered correctly. Second, if data are correct, we will inspect the graph visually and we will remove outlying studies to see if heterogeneity is restored. For this review, we intend that should this occur with data contributing to the summary finding of no more than around 10% of the total weighting, we will present the data. If not, we will not pool the data but rather discuss the issues in the text. We know of no supporting research for this 10% cut‐off but are investigating use of prediction intervals as an alternative to this unsatisfactory state.
When unanticipated clinical or methodological heterogeneity are obvious, we will simply state hypotheses regarding these for future reviews or versions of this review. We do not anticipate undertaking analyses relating to these.
Sensitivity analysis
1. Implication of randomisation
We aim to include trials in a sensitivity analysis if they are described in some way as to imply randomisation. For the primary outcomes, we will include these studies and if there is no substantive difference when the implied randomised studies are added to those with better description of randomisation, then we will use all data from these studies.
2. Assumptions for lost binary data
Where assumptions have to be made regarding people lost to follow‐up (see Dealing with missing data), we will compare the findings of the primary outcome when we use our assumption compared with completer data only. If there is a substantial difference, we will report results and discuss them but 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 on the primary outcome when we use our assumption compared with complete data only. We will undertake a sensitivity analysis to test how prone the results are to change when 'completer' data only are compared with the imputed data using the above assumption. If there is a substantial difference, we will report results and discuss them but 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 but with no further details available) allocation concealment, blinding and outcome reporting for the meta‐analysis of the primary outcome. If the exclusion of trials at high risk of bias does not substantially alter the direction of effect or the precision of the effect estimates, then 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 and random effects
We will 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 the greater weights assigned to larger trials with greater event rates, altered the significance of the results compared with the more evenly distributed weights in the random‐effects model.
6. Diagnostic criteria used
We aim to compare the studies that used operational criteria for diagnoses with those that did not.
