Atomoxetine for schizophrenia

  • Protocol
  • Intervention



This is the protocol for a review and there is no abstract. The objectives are as follows:

To examine the effects of atomoxetine on cognitive impairment in people with schizophrenia.


Description of the condition

Schizophrenia is chronic and disabling mental illness affecting approximately 1% of the population, affecting all cultures and socioeconomic groups (Fortinash 2000). Lifetime prevalence of schizophrenia and related disorders is about 5.5 per 1000, but there is significant variation between regions (Johannessen 2003). Schizophrenia is a chronic illness with 'positive' symptoms (hearing voices, other alterations of the senses, delusions, distortions in the way the world is seen) and 'negative' symptoms (such as flattening of mood, poverty of speech, lack of drive, loss of feeling, social withdrawal and decreased spontaneous movement). Based on the results of various researches, it has become abundantly clear that people with schizophrenia suffer with cognitive impairment. Generally people with schizophrenia have deficits in attention, information processing, and concentration that result in social and functional disability (Bowie 2005). Researchers have found that people with history of schizophrenia score worse on cognitive tasks as compared to general population and these deficits persist even when they are in remission (Gold 1993). Cognitive impairment is very important in determining outcome in social and functional ability. Because of cognitive impairment, people with history of schizophrenia experience difficulties with psychosocial rehabilitation in day-to-day functioning (Bellack 1992).

Description of the intervention

Atomoxetine is a non-stimulant, selective norepinephrine reuptake inhibitor. It is well known for the treatment of attention deficit hyperactivity disorder (ADHD) (Corman 2004). In rodents, atomoxetine has shown to improve memory functions significantly by releasing cortical dopamine and epinephrine (Bymaster 2002). This does not seem to occur in the striatum or nucleus accumbens. Atomoxetine has similar effects on hippocampal acetylcholine release mediated by both nor-epinephrine α1 and dopamine D1 receptor activation (Bymaster 2002; Tzavara 2006).

How the intervention might work

One known mechanism of action of atomoxetine is to increase nor-epinephrine and dopamine levels in the synapses, by specifically inhibiting reuptake of nor-epinephrine in pre-synaptic sites (Bymaster 2002). This results in indirect improvement of the prefrontal cortex function (Arnsten 2009). Atomoxetine inhibits nor-epinephrine transporter, serotonin transporter and dopamine active transporter. Atomoxetine also acts as an N-methyl D-aspartate (NMDA) receptor antagonist at clinically relevant doses (Ludolph 2010)

Why it is important to do this review

Generally antipsychotic medications do not result in marked improvement in cognition in schizophrenia. We intend to investigate whether, and to what extent, atomoxetine enhances cognitive ability in people with schizophrenia. The evidence of cognitive impairment in schizophrenia is growing but on the other hand there is no sound evidence on its pharmacological treatment. The aim of this review is to systematically locate and synthesise all available data on the efficacy of atomoxetine in cognitive impairment in schizophrenia and to grade the overall quality of the evidence in order to inform clinical practice.


To examine the effects of atomoxetine on cognitive impairment in people with schizophrenia.


Criteria for considering studies for this review

Types of studies

We will include all relevant randomised controlled trials (RCTs). If studies mention randomisation, then we will take this at its face value and then we will try to find out what type of randomisation they used. We will also check this using the Jadad scale (Jadad 1996), whether it is satisfactory. If a trial is described as 'double blind' but implies randomisation, we will include such trials in a sensitivity analysis (see Sensitivity analysis). If their inclusion does not result in a substantive difference, they will remain in the analyses. If their inclusion does result in important clinically significant but not necessarily statistically significant differences, we will not add the data from these lower quality studies to the results of the better trials, but will present such data within a subcategory. We will exclude quasi-randomised studies, such as those allocating by alternate days of the week. Where people are given additional treatments within atomoxetine, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the atomoxetine that is randomised.

Types of participants

We will consider adult participants, aged 18 to 65 years, with a diagnosis of schizophrenia, psychosis or related disorders including schizophreniform disorder, schizoaffective disorder and delusional disorder, again, by any means of diagnosis.

We are interested in making sure that information is as relevant to the current care of people with psychosis as possible so propose to clearly highlight the current clinical state (acute, early post-acute, partial remission, remission) as well as the stage (prodromal, first episode, early illness, persistent) and as to whether the studies primarily focused on people with particular problems (for example, negative symptoms, treatment-resistant illnesses).

Types of interventions

1. Atomoxetine

Atomoxetine is a non-stimulant medication that is traditionally used to help as part of the treatment for the symptoms of hyperactivity or attention deficit hyperactivity disorder. It may be used for educational, social, functional and psychological help. Atomoxetine helps the people’s abilities to concentrate and to reduce hyperactivity and impulsive behaviour (Corman 2004).

We will take all RCTs where atomoxetine has been part of a comparator either in itself or in combination against any other pharmaceutical intervention or placebo.

Treatment of schizophrenia is primarily antipsychotic medications, so we suspect that most of the RCTs will have been done with antipsychotics and placebo as a comparator but if there are any RCTs where the comparator arm is other than antipsychotics or placebo we will include those studies as well.

2. Antipsychotic medication: atypcial or typical antipyschotics - any dose, any form of administration
3. Placebo

Types of outcome measures

We will divide all outcomes into short-term (less than six months), medium-term (7-12 months) and long-term (over one year). We will group outcomes according to primary and secondary outcomes.

Primary outcomes
1. Global state

1.1 Clinical significant improvement in global state.

2. Cognitive Response

2.1 Clinical significant improvement in cognitive outcomes and working memory.

3. Specific cognitive domain (memory, attention, speed of processing and abstraction levels

3.1 Improvement or deterioration on the specific cognitive domain.
3.2 Average change (endpoint-baseline) or endpoint score on the specific cognitive domain

4. Mental state

4.1 Clinical significant improvement in mental state

Secondary outcomes
1. Death: suicide or natural causes
2. Leaving the study early
3. Service utilisation outcomes

3.1 Hospital admission
3.2 Days in hospital
3.3 Change in hospital status i,e transfer from intensive care ward to general open ward

4. Social functioning

4.1 Average score/change in social functioning

5. General functioning

5.1 Clinically important change in general or specific functioning such as social or life skills

6. Adverse effects

6.1 Extra pyramidal adverse effects
6.2 Other adverse effects

7. Behaviour

7.1 Clinically important change in general or specific behaviours

8. Economic outcomes

8.1 For the family
8.2 For the hospital

9. Quality of life/satisfaction with care for either recipients of care or carers

9.1 Significant change in quality of life/satisfaction
9.2 Average score/change in quality of life/satisfaction

10. Summary of Findings' table

We will use the Grading of Recommendations Assessment, Development and Evaluation (GRADE) approach to interpret findings (Schünemann 2011), and use the GRADE software to import data from the Cochrane Collaboration's statistical software, REVMAN, to create a 'Summary of Findings' table. 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:

  1. Global state (clinical significant improvement in global state as described by each of the studies)

  2. Cognitive response (clinical significant improvement in cognitive outcomes - as described by each of the studies)

  3. Adverse effects (any reported adverse effects as described by each of the studies)

  4. Service utilisation outcomes (hospital admission, as described by each of the studies)

Search methods for identification of studies

Electronic searches

1. Cochrane Schizophrenia Group's Trials Register

The Trials search Coordinator will search Cochrane Schizophrenia Groups Specialised Register (until September 25, 2013) applying the following search strategy:

  • (Atomoxetine or Tomoxetine or Strattera):ti or (Atomoxetine or Tomoxetine or Strattera):ab or (Atomoxetine or Tomoxetine or Strattera):kw in REFERENCE or (Atomoxetine or Tomoxetine or Strattera):sin in STUDY

The Cochrane Schizophrenia Group's Specialised Register is compiled by systematic searches of major databases and their monthly updates, handsearches and conference proceedings, for details of databases searched please see group module (Adams 2013).

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

MA and ZJ individually will inspect all citations of studies identified by the search. Where disagreement occur we will resolve it by discussion, or, when there is still a doubt, we will acquire the full article for further inspection. If doubt remain AK will decide whether they met review criteria and the discussion will be documented.

MA and ZJ will independently inspect citations from the searches and identify relevant abstracts. A random 20% sample will be independently checked by AK to ensure reliability. Where disputes arise, the full-text reports will be acquired for more detailed scrutiny. Full reports of the abstracts meeting the review criteria will be obtained and inspected by MA and ZJ. Again, a random 20% of reports will be checked by AK in order to ensure reliable selection. Where it is not possible to resolve disagreement by discussion and we are unable to obtain the full text articles, we will attempt to contact the authors of the study for clarification and categorise the study as "study awaiting classification" until the issue is resolved.

Data extraction and management

1. Extraction

MA and ZJ will extract data from all included studies. In addition, to ensure reliability AK will independently extract data from a random sample of these studies, comprising 20% of the total. Again, any disagreement will be discussed, decisions documented and, if necessary, authors of studies will be contacted for clarification. With any remaining problems, AK will help clarify issues and these final decisions will be documented. Data presented only in graphs and figures will be extracted whenever possible, but included only if the two authors (MA and ZJ) 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 data extraction forms.

2.2. Scale-derived data

We will include continuous data from rating scales only if:

  • the psychometric properties of the measuring instrument have been described in a peer-reviewed journal (Marshall 2000); and

  • 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. We will note this under the 'Description of studies' section.

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. Endpoint and change data will be combined in the analysis as we will use weighted 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:

  • we will enter data from studies of at least 200 participants, for example, 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:

  • when a scale starts from the finite number zero, we will subtract the lowest possible value from the mean, and divided this by the standard deviation. If this value is lower than 1, it strongly suggests a skew and the study will be excluded. If this ratio is higher than one but below 2, there is suggestion of skew. We will enter the study and test whether its inclusion or exclusion would change the results substantially. Finally, if the ratio is larger than 2 the study will be included, because skew is less likely (Altman 1996; Higgins 2011);

  • if a scale starts from a positive value (such as the Positive and Negative Syndrome Scale (PANSS). which can have values from 30 to 210) (Kay 1986), the calculation described above will be modified to take the scale starting point into account. In these cases skew is present if 2 standard deviation (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 intend to convert variables that can be reported in different metrics, such as days in hospital (mean days per year, per week or per month) to a common metric (e.g. mean days per month).

2.6. Conversion of continuous to binary

Where possible, efforts will be made to convert outcome measures to dichotomous data. This can be done by identifying cut-off points on rating scales and dividing participants accordingly into 'clinically improved' or 'not clinically improved'. It is generally assumed that if there is a 50% reduction in a scale-derived score such as the Brief Psychiatric Rating Scale (BPRS) or the Positive and Negative Syndrome Scale (PANSS)(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 atomoxetine. Where keeping to this makes it impossible to avoid outcome titles with clumsy double-negatives (e.g. 'Not improved') we will report data where the left of the line indicates an unfavourable outcome. This will be noted in the relevant graphs.

Assessment of risk of bias in included studies

Two authors (MA and ZJ) will work independently to assess risk of bias by using criteria described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) to assess trial quality. This set of criteria is based on evidence of associations between overestimate of effect and high risk of bias of the article such as sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting.

If the raters disagree, the final rating will be made by consensus, with the involvement of another author (AK). Where inadequate details of randomisation and other characteristics of trials are provided, authors of the studies will be contacted in order to obtain further information. Non-concurrence in quality assessment will be reported, but if disputes arise as to which category a trial is to be allocated, again, we will resolve by discussion.

We will illustrate the level of risk of bias as 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 the standard estimation of the risk ratios (RRs) and their 95% confidence interval (CIs). It has been shown that RRs are more intuitive than odds ratios (ORs) (Boissel 1999), and that ORs tend to be interpreted as RRs by clinicians (Deeks 2000). The numbers needed to treat to benefit/harm (NNTB/NNTH) statistic with their 95% CIs are intuitively attractive to clinicians but is problematic both in its accurate calculation in meta-analyses and interpretation (Hutton 2009). For binary data presented in the 'Summary of Findings' table(s), where possible, we will calculate illustrative comparative risks.

2. Continuous data

For continuous outcomes, we will estimate 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.

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 'unit of analysis' errors whereby the P values are spuriously low, CIs are unduly narrow and statistical significances are overestimated (Divine 1992). These in turn lead to 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. In this and subsequent versions of this review we will seek to contact first authors of such studies to obtain intra-class correlation coefficients 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 intra-class correlation coefficient (ICC) [Design effect = 1+(m-1)*ICC] (Donner 2002). If the ICC is not reported it will be assumed to be 0.1 (Ukoumunne 1999).

If cluster studies have been appropriately analysed taking into account 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 of the first phase of cross-over studies.

3. Studies with multiple treatment groups

Where a study involves more than two treatment arms, if relevant, the additional treatment arms will be presented in comparisons. If data are binary these will be simply added and combined within the two-by-two table. If data are continuous we will combine data following the formula in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Where the additional treatment arms are not relevant, we will not use these data.

Dealing with missing data

1. Overall loss of credibility

At some degree of loss of follow-up data must lose credibility (Xia 2009). We choose that, for any particular outcome, should more than 50% of data be unaccounted for, we will not reproduce these data or use them within analyses. If, however, more than 50% of those in one arm of a study are lost, but the total loss is less than 50%, we will address this within the 'Summary of Findings' table(s) by down-rating quality. Finally, we will also downgrade quality within the 'Summary of Findings' table(s) should loss be 25-50% in total.

2. Binary

In the case where attrition for a binary outcome is between 0 and 50% and where these data are not clearly described, we will present data on a 'once-randomised-always-analyse' basis (an intention-to-treat (ITT) analysis). Those leaving the study early are all assumed to have the same rates of negative outcome as those who completed, with the exception of the outcome of death and adverse effects. For these outcomes 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

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 values or t values 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, SDs are calculated by the formula SD = SE * square root (n). The Cochrane Handbook for Systematic Reviews of Interventions present 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. 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 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 e.g. MMRM, or multiple-imputation will be preferred to LOCF and completer analyses will only be presented 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, 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 statistic alongside the P value of the Chi2 test. 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:

  • magnitude and direction of effects; and

  • strength of evidence for heterogeneity (e.g. P value from the Chi2  test, or a CI for I2).

We will regard I2 estimates of greater than or equal to around 50% accompanied by a statistically significant Chi2 statistic (P < 0.1) 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 the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will try to locate protocols of included randomised trials. If the protocol is available, outcomes in the protocol and in the published report will be compared. If the protocol is not available, outcomes listed in the methods section of the trial report will be compared with actually reported results.

2. Funnel plot

Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997). These are again described in 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 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 analysis
1.1. Primary outcomes

We do not anticipate any subgroup analyses.

1.2. Clinical state, stage or problem

We propose to undertake this review and provide an overview of the effects of atomoxetine for people with schizophrenia in general. In addition, however, we will try to report data on subgroups of people in the same clinical state, stage and with similar problems.

2. Investigation of heterogeneity

If inconsistency is high, this will be reported. First we will investigate whether data has been entered correctly. Second, if data is correct, we will visually inspect the graph and studies outside of the company of the rest will be successively removed to see if homogeneity is restored. For this review, we decided that should this occur with data contributing to the summary finding of no more than around 10% of the total weighting, data will be presented. If not, we will not pool any data and issues will be discussed. 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 all data will be employed from these studies.

2. Assumptions for lost binary data

Where assumptions have to be made regarding people lost to follow-up (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumption(s) and when we use data only from people who complete the study to that point. If there is a substantial difference, we will report results and discuss them but will continue to employ our assumption.

Where assumptions have to be made regarding missing SDs data (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumption(s) and when we use data only from people who complete the study to that point. 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 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 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 vs. random-effects

All data will be synthesised using a random-effects model. However, we will also synthesise data for the primary outcome using a fixed-effect model to evaluate whether this alters the significance of the results.


The Cochrane Schizophrenia Group editorial base in Nottingham produces and maintains standard text for use in the Methods section of their reviews. We have used this text as the basis of what appears here and adapted it as required.

The search term has been developed by the Trial Search Co-ordinator of the Cochrane Schizophrenia Group, Farhad Shokran and the contact author of this protocol.

We would like to thank Liangtao Luo for peer reviewing this protocol.

Contributions of authors

Mohammad Ashraf - helped write the protocol.

Zunaira Javed - helped write the protocol.

Ajit Kumar - helped write the protocol.

Declarations of interest

Mohammad Ashraf - none.

Zunaira Javed - none.

Ajit Kumar - none.

Sources of support

Internal sources

  • None, Other.

External sources

  • No sources of support supplied