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. 2019 Feb 13;2019(2):CD013266. doi: 10.1002/14651858.CD013266

Olanzapine dose for people with schizophrenia

Youssef Latifeh 1, Mays Mohsen 1, Sara Mohamad 1, Tarek Nassif 1,✉
PMCID: PMC6373521

Abstract

This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:

To evaluate the efficacy and safety of different doses of olanzapine for people with schizophrenia.

Background

Description of the condition

Schizophrenia is a complex and severe mental illness that has a significant impact on individuals and their families (Owen 2016). It usually starts in early adulthood and in rare cases, during childhood or old age. Slightly more men are diagnosed with schizophrenia than women and women tend to have a later onset (Abel 2010). The median incidence is 15.2 per 100,000, with a global lifetime prevalence of about 1% (McGrath 2008; Zare 2017). Nearly half the people diagnosed with schizophrenia do not receive treatment and 90% of those untreated live in lower middle‐income countries (WHO 2016). A recent review assessed data from 24 countries around the world and estimated that the economic burden of schizophrenia ranged from 0.02% to 1.65% of their gross domestic product (Chong 2016).

Schizophrenia affects how a person thinks, feels, and behaves. Its characteristics typically include positive symptoms (delusions and hallucinations), negative symptoms (apathy, absent or blunted or incongruous emotional responses, reductions in speech, social withdrawal, impaired attention, anhedonia), disorganisation of behaviour and thought and catatonic symptoms such as mannerisms and bizarre posturing (Carpenter 1994; Elis 2013). In addition, cognitive dysfunction, including a decreased ability to focus attention and deficiencies in short‐term verbal and nonverbal memory, is also a core feature of the illness, which predicts vocational and social disabilities for patients (Freedman 2003)

People with schizophrenia often experience stigma and discrimination and violation of their human rights (WHO 2016), and are more likely to be single and unemployed (Messias 2007). Studies have also found that adults with schizophrenia have more cardiovascular and chronic obstructive pulmonary diseases in addition to a higher mortality rate compared to the general population. On average, people with schizophrenia die 14.5 years earlier compared to the general population (Olfson 2015; Hjorthoej 2017).

The mainstay treatment is antipsychotic drugs with two‐thirds of patients achieving good or intermediate outcomes with antipsychotic treatment, however, one‐third do not respond to such treatment and have poor outcomes (Elkis 2016). Only a small proportion of individuals who develop schizophrenia have a favourable prognosis, with about one in seven individuals with schizophrenia achieving recovery by treatment with medication and psychosocial interventions (Jaaskelainen 2013)

Description of the intervention

Antipsychotics are the main treatment option for schizophrenia, improving positive symptoms and decreasing the risk of relapse (Duggan 2005; Leucht 2012 ), but having less efficacy for negative symptoms (Kane 1986). Antipsychotic medications also have a wide spectrum of associated side effects (such as extrapyramidal symptoms, movement disorders, sedation, weight gain and sexual dysfunctions) which can reduce adherence to treatment (Haddad 2014).

Olanzapine is a second‐generation antipsychotic drug (Figure 1), a thienobenzodiazepine derivative, and was approved by the US Food and Drug Administration in 1996. Olanzapine is available orally or as an injectable suspension and has 4 forms for administration: solution reconstituted, intramuscular (IM), oral disintegrating tablet, and extended‐release injectable suspension (Drugs 2018). The side effects associated with olanzapine use include weight gain, constipation, dry mouth, peripheral oedema, dizziness, drowsiness, orthostatic hypotension, akinesia, anticholinergic and extrapyramidal symptoms (Medsafe 2014; Drugs 2018).

Figure 1.

Figure 1

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Olanzapine structure: 2‐methyl‐4‐(4‐methyl‐1‐piperazinyl)‐10H‐thieno(2,3‐b)(1,5)benzodiazepine (PubChem Compound Database)

It is suggested that standard adult oral doses of olanzapine for schizophrenia are: 2.50 mg to 10 mg (low dose), 10 mg to 20 mg (medium dose), > 20 mg (high dose) orally once a day. IM efficacy has been demonstrated with doses from 150 mg to 300 mg every two weeks and 405 mg every four weeks (Drugs 2018).

How the intervention might work

Schizophrenia is a complex mental illness that likely spans dysfunctions across multiple circuits and neurotransmitter systems of the brain, among the most prominent being dopamine, glutamate, serotonin, and gamma‐aminobutyric acid (Gill 2016).

Olanzapine is a potent serotoniergic antagonist that is particularly potent antagonist at 5‐HT2A, 5‐HT2B, 5‐HT2C receptors, alpha 1‐adrenergic and histamine H1 receptors. It has relatively weaker potency as an antagonist at muscarinic receptors and dopamine D1 receptors (Bymaster 1999).

The mean half‐life of oral olanzapine is 33 hours (ranging from 21 hours to 54 hours). Gender and smoking have been found to be the individual factors with the largest impact on olanzapine pharmacokinetics, where smokers and men have a higher clearance of olanzapine than women and nonsmokers. Variability in the clearance and concentration of olanzapine does not appear to be associated with the severity or duration of adverse effects nor with the degree of efficacy (Bhana 2001; Callaghan 1999).

Why it is important to do this review

Olanzapine is a widely prescribed antipsychotic for schizophrenia, generally administered orally or by the IM route (Drugs 2018), and has been shown to be clinically effective with improved quality of life, lower incidence of extrapyramidal symptoms and a higher acceptance of medication compared to some other antipsychotics (Montes 2003; Phillips 2006). Achieving the best clinical effect and lowest side effect profile is a common dilemma for clinicians. It is well established that an antipsychotic's efficacy, side effect profile and mortality are dose‐dependent (Pakpoor 2014). Standard doses of olanzapine are established for routine practice (described above), however, response is varied and some people with schizophrenia may not respond to standard doses of antipsychotic drugs (Kane 2013).

It has been reported that a favourable response with olanzapine is maximised at doses of 10 mg/day to 15 mg/day (perhaps lower in nonsmoking females) (Bishara 2013). However, lower or higher doses may be used and the relationship between olanzapine dose, efficacy and side effects remains contradictory between studies. The impact of olanzapine on quality of life for people with schizophrenia was not important at low doses (2.5 mg/day to 10 mg/day) but important improvements were observed at medium doses (10 mg/day to 20 mg/day) and high doses (more than 20 mg/day) (Bobes 2007). Olanzapine at high doses of 30 mg/day and 40 mg/day displayed pharmacokinetic and tolerance profiles consistent with that of 20 mg/day, however, akathisia (inability to stay still or restlessness) may be more likely to occur at these higher doses (Mitchell 2006; Kinon 2008).

This review aims to create an evidence base using the highest quality evidence from randomised controlled trials (RCTs) in order to clarify and identify the beneficial and harmful effects of varying dose levels of olanzapine for people with schizophrenia. Decisions on care can then be evidence‐based, and direction of future research clarified.

Objectives

To evaluate the efficacy and safety of different doses of olanzapine for people with schizophrenia.

Methods

Criteria for considering studies for this review

Types of studies

We will consider all relevant randomised controlled trials (RCTs). We will include RCTs meeting our inclusion criteria and reporting useable data. We will consider trials that are described as 'double‐blind' ‐ in which randomisation is implied ‐ and include or exclude once we have carried out a sensitivity analysis (see Sensitivity analysis). We will exclude quasi‐randomised studies, such as those that allocate intervention by alternate days of the week. Where people are given additional treatments as well as olanzapine, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the olanzapine administration that is randomised.

Types of participants

Adults (aged 18 years and over), however defined, with schizophrenia or related disorders, including schizophreniform disorder, schizoaffective disorder and delusional disorder, by any means of diagnosis.

Olanzapine is also intended for use in adolescents (13 to 17 years of age) (Grothe 2000), but we will not include trials for adolescents as another future Cochrane Review will assesses the effects of pharmacological interventions for adolescents.

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

Types of interventions

1. Oral Olanzapine
1.1 Low dose: 2.50 mg/day to 10 mg/day
1.2 Standard dose: 10 mg/day to 20 mg/day
1.3 High dose: > 20 mg/day
2. Intramuscular (IM) Olanzapine
2.1 Low dose: 150 mg every 2 weeks or 300 mg every 4 weeks
2.2 Standard dose: 210 mg every 2 weeks or 405 mg every 4 weeks
2.3 High dose: 300 mg every 2 weeks or higher

Types of outcome measures

We aim to divide all outcomes into short term (less than 6 months), medium term (7 to 12 months) and long term (over 12 months).

We will endeavour to report binary outcomes recording clear and clinically meaningful degrees of change (e.g. global impression of much improved, or more than 50% improvement on a rating scale ‐ as defined within the trials) before any others. Thereafter, we will list other binary outcomes and then those that are continuous.

For types of scales we will use to extract data, please see Data extraction and management.

Primary outcomes
1. Global State

1.1 Clinically important changes in global state, as defined by each study 1.2 Clinically important change in compliance with treatment, as defined by each study 1.3 Relapse, as defined by each study

2. Mental state

2.1 Clinically important change in overall mental state, as defined by each study

3. Quality of life

3.1 Clinically important changes in quality of life, as defined by each study

4. Adverse effects/events

4.1 Clinically important specific adverse effects ‐ movement disorder, as defined by each of the studies

Secondary outcomes
1. Global state

1.1 Any change in global state, as defined by each study 1.2 Average endpoint/change score on global state scale

2. Mental state
2.1 General

2.1.1 Any change in overall mental state, as defined by each study 2.1.2 Average endpoint/change scores on general mental state scale

2.2 Specific

2.2.1 Clinically important change in positive symptoms (e.g. delusions, hallucinations), as defined by each study 2.2.2 Any change in positive symptoms, as defined by each study 2.2.3 Average endpoint/change scores on positive symptom scale 2.2.4 Clinically important change in negative symptoms (e.g. affective flattening, alogia, or avolition), as defined by each study 2.2.5 Average endpoint/change scores on negative symptom scale

4. Quality of life

4.1 Any change in quality of life, as defined by each of the studies 4.2 Any change in employment status, as defined by each study/events 4.3 Average endpoint/change score on quality of life scale

5. Adverse effects/event

5.1 At least one adverse effect/event 5.2 Clinically important specific adverse effects, as defined by each of the studies (e.g. anticholinergic, antihistamine, endocrinological, cardiovascular, genitourinary, gastrointestinal, neurological, respiratory, abnormal laboratory tests and any other specific adverse effects) 5.3 Average endpoint/change score on general adverse effect scale 5.4 Death ‐ suicide or other causes

6. Service use

6.1 Hospital admissions 6.2 Duration of stay in hospital 6.3 Change in hospital status

7. Cognitive functioning

7.1 Clinically important change in cognitive functioning, as defined by each study 7.2 Any change in cognitive functioning, as defined by each study 7.3 Average endpoint/change score on cognitive functioning scale

8. Behaviour

8.1 Clinically important change in general behaviour, as defined by each study 8.2 Any change in general behaviour, as defined by each study 8.3 Average endpoint/change scores on general behaviour scale 8.4 Incidence aggression/violence

9. Satisfaction with care for either recipients of care or caregivers

9.1 Clinically important change in satisfaction, as defined by each study 9.2 Any change in satisfaction, as defined by each study 9.3 Average endpoint/change scores on satisfaction scale

10. Social functioning

10.1 Clinically important change in social functioning, as defined by each study 10.2 Any change in social functioning, as defined by each study 10.3 Average endpoint/change scores on social functioning scale

11. Leaving the study early

11.1 For any reason 11.2 Due to relapse 11.3 Due to adverse effects

12. Economic costs

12.1 Costs due to treatment, as defined by each study 12.2 Savings due to treatment, as defined by each study

'Summary of findings' table

We will use the GRADE approach to interpret findings (Schünemann 2011); and will use GRADEpro GDT to export data from our review to create a 'Summary of findings' table (GRADEpro GDT 2015). This table will provide outcome‐specific information concerning the overall certainty of evidence from each included study in the comparison, the magnitude of effect of the interventions examined, and the sum of available data on all outcomes we rate as important to patient care and decision making. We aim to select the following main outcomes for inclusion in the 'Summary of findings' table.

  1. Global state: clinically important change in global state, as defined by each study (long term).

  2. Global state: clinically important change in compliance with treatment, as defined by each study (long term).

  3. Quality of life: clinically important change in quality of life/satisfaction, as defined by each study (long term).

  4. Adverse effects/events: clinically important specific adverse effects ‐ movement disorder, as defined by each study (medium term).

  5. Mental state: clinically important change in general mental state, as defined by each study (long term).

  6. Cognitive functioning: clinically important change, as defined by each study (long term).

  7. Social functioning: clinically important change in social functioning, as defined by each study (long‐term).

If data are not available for these prespecified outcomes but are available for ones that are similar, we will present the closest outcome to the prespecified one in the table but take this into account when grading the finding.

Search methods for identification of studies

Electronic searches

Cochrane Schizophrenia's study‐based register of trials

The Information Specialist will search the register using the following search strategy.

(*Olanzapine* AND *Dosage*) in Intervention Field of STUDY

In such study‐based registers, searching the major concept retrieves all the synonyms and relevant studies because all the studies have already been organised based on their interventions and linked to the relevant topics (Shokraneh 2017).

This register is compiled by systematic searches of major resources (AMED, BIOSIS, CENTRAL, CINAHL, ClinicalTrials.Gov, EMBASE, MEDLINE, PsycINFO, PubMed, WHO ICTRP) and their monthly updates, ProQuest Dissertations and Theses A&I and its quarterly update, Chinese databases (CBM, CNKI, and Wanfang) and their annual updates, handsearches, grey literature, and conference proceedings (see Group's website). There is no language, date, document type, or publication status limitations for inclusion of records into the register.

Searching other resources

1. Reference searching

We will inspect references of all included studies for further relevant studies.

2. Personal contact

We will contact the first author of each included study for information regarding unpublished trials. We will note the outcome of this contact in the 'Included studies' or 'Studies awaiting classification' tables.

Data collection and analysis

Selection of studies

Review authors MM, SM and TN will independently inspect citations from the searches and identify relevant abstracts; YL will independently reinspect a random 20% sample of these abstracts to ensure reliability of selection. Where disputes arise, we will acquire the full report for more detailed scrutiny. Review authors MM, SM and TN will then obtain and inspect full reports of the abstracts or reports meeting the review criteria. YL will reinspect a random 20% of these full reports in order to ensure reliability of selection. Where it is not possible to resolve disagreement by discussion, we will attempt to contact the authors of the study concerned for clarification.

Data extraction and management

1. Extraction

Review authors YL and TN will extract data from all included studies. In addition, to ensure reliability, review authors MM and SM will independently extract data from a random sample of these studies, comprising 10% of the total. We will attempt to extract data presented only in graphs and figures whenever possible, but will include them only if two review authors independently obtain the same result. If studies are multicentred, then where possible we will extract data relevant to each. We will discuss any disagreement and document our decisions. If necessary, we will attempt to contact authors through an open‐ended request in order to obtain missing information or for clarification. Review authors YL and TN will help clarify issues regarding any remaining problems and we will document these final decisions.

2. Management
2.1 Forms

We will extract data onto standard, predesigned, 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); b) the measuring instrument has not been written or modified by one of the trialists for that particular trial; and c) the instrument should be a global assessment of an area of functioning and not subscores which are not, in themselves, validated or shown to be reliable. However there are exceptions; we will include subscores from mental state scales measuring positive and negative symptoms of schizophrenia. 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; however, calculation of change needs two assessments (baseline and endpoint) that can be difficult to obtain 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. If necessary, we will combine endpoint and change data in the analysis, as we prefer to use mean differences (MDs) rather than standardised mean differences (SMDs) throughout (Deeks 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 will apply the following standards to relevant continuous data before inclusion.

For endpoint data from studies including fewer than 200 participants:

a) when a scale starts from the finite number zero, we will subtract the lowest possible value from the mean, and divide this by the standard deviation (SD). If this value is lower than one, it strongly suggests that the data are skewed and we will exclude these data. If this ratio is higher than one but less than two, there is suggestion that the data are skewed: we will enter these data and test whether their inclusion or exclusion would change the results substantially. If such data change results, we will enter as 'other data'. Finally, if the ratio is larger than two, we will include these data, because it is less likely that they are skewed (Altman 1996; Higgins 2011a).

b) 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)), we will modify the calculation described above to take the scale starting point into account. In these cases skewed data are present if 2 SD > (S − S min), where S is the mean score and 'S min' is the minimum score.

Please note: we will enter all relevant data from studies of more than 200 participants in the analysis irrespective of the above rules, because skewed data pose less of a problem in large studies. We will also enter all relevant 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 or not data are skewed.

2.5 Common measurement

To facilitate comparison between trials, we aim, where relevant, 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 Olanzapine. Where keeping to this makes it impossible to avoid outcome titles with clumsy double‐negatives (e.g. 'not unimproved') 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

Review authors YL, MM, SM and TN will work independently to assess risk of bias by using criteria described in the Cochrane Handbook for Systematic Reviews of Interventions to assess trial quality (Higgins 2011b). This set of criteria is based on evidence of associations between potential overestimation of effect and the level of risk of bias of the article that may be due to aspects of sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting, or the way in which these 'domains' are reported.

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 attempt to contact authors of the studies in order to obtain further information. We will report non‐concurrence in quality assessment, but if disputes arise regarding the category to which a trial is to be allocated, we will resolve this by discussion.

We will note the level of risk of bias in both the text of the review and 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), as it has been shown that RR is more intuitive than odds ratios (ORs) (Boissel 1999); and that ORs tend to be interpreted as RR by clinicians (Deeks 2000). Although the number needed to treat for an additional beneficial outcome (NNTB) and the number needed to treat for an additional harmful outcome (NNTH), with their CIs, are intuitively attractive to clinicians, they are problematic to calculate and interpret in meta‐analyses (Hutton 2009). For binary data presented in the 'Summary of findings' table we will, where possible, calculate illustrative comparative risks.

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. Authors often fail to account for intraclass correlation in clustered studies, leading to a unit of analysis error whereby P values are spuriously low, CIs unduly narrow and statistical significance overestimated (Divine 1992). This causes type I errors (Bland 1997; 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.

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 seek to contact first authors of studies to obtain intraclass correlation coefficients (ICCs) for their clustered data and to adjust for this by using accepted methods (Gulliford 1999).

We have sought statistical advice and have been advised that the binary data from cluster trials 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: thus 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 and taken ICCs and relevant data documented in the report into account, 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. This 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, participants can differ significantly from their initial state at entry to the second phase, despite a washout phase. For the same reason cross‐over trials are not appropriate if the condition of interest is unstable (Elbourne 2002). As both carry‐over and unstable conditions 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 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 the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). Where 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 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 by downgrading quality. Finally, we will also downgrade quality within the 'Summary of findings' table should the loss be 25% to 50% in total.

2. Binary

In the case where attrition for a binary outcome is between 0% and 50% and where these data are not clearly described, we will present data on a 'once‐randomised‐always‐analyse' basis (an intention‐to‐treat (ITT) analysis). Those leaving the study early are all assumed to have the same rates of negative outcome as those who completed. We will use the rate of those who stay in the study ‐ in that particular arm of the trial ‐ and apply this also to 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 ITT analysis using the above assumptions.

3. Continuous
3.1 Attrition

We will use data 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.

3.2 Standard deviations

If SDs are not reported, we will try to obtain the missing values from the authors. If these are not available, where there are missing measures of variance for continuous data, but an exact standard error (SE) and CIs available for group means, and either P value or t value available for differences in mean, we can calculate SDs according to the rules described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). When only the SE is reported, SDs are calculated by the formula SD = SE * √(n). The Cochrane Handbook for Systematic Reviews of Interventions presents detailed formulae for estimating SDs from P, t or F values, CIs, ranges or other statistics (Higgins 2011a). If these formulae do not apply, we will calculate the SDs according to a validated imputation method which is based on the SDs of the other included studies (Furukawa 2006). Although some of these imputation strategies can introduce error, the alternative would be to exclude a given study’s outcome and thus to lose information. Nevertheless, we will examine the validity of the imputations in a sensitivity analysis that excludes 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 between groups in their reasons for doing so is often the core problem in randomised schizophrenia trials. We will therefore not exclude studies based on the statistical approach used. However, by preference we will use the more sophisticated approaches, i.e. we will prefer to use MMRM or multiple imputation to LOCF, and we 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' table.

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 participants who are clearly outliers or situations that we had not predicted would arise and, where found, discuss such situations or participant groups.

2. Methodological heterogeneity

We will consider all included studies initially, without seeing comparison data, to judge methodological heterogeneity. We will simply inspect all studies for clearly outlying methods which we had not predicted would arise and discuss any such methodological outliers.

3. Statistical heterogeneity
3.1 Visual inspection

We will inspect graphs visually 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 Chi² P value. The I² statistic 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 the magnitude and direction of effects as well as the 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 50% and accompanied by a statistically significant Chi² statistic as evidence of substantial heterogeneity (Deeks 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

Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997). These are described in Chapter 10 of the Cochrane Handbook for Systemic reviews of Interventions (Sterne 2011).

1. Protocol versus full study

We will try to locate protocols of included randomised trials. If the protocol is available, we will compare outcomes in the protocol and in the published report. If the protocol is not available, we will compare outcomes listed in the methods section of the trial report with actually reported results.

2. Funnel plot

We are aware that funnel plots may be useful in investigating reporting biases but are of limited power to detect small‐study effects. We will not use funnel plots for outcomes where there are 10 or fewer studies, or where all studies are of similar size. In other cases, where funnel plots are possible, we will seek statistical advice in their interpretation.

Data synthesis

We understand that there is no closed argument for preference for use of fixed‐effect or random‐effects models. The random‐effects method incorporates an assumption that the different studies are estimating different, yet related, intervention effects. This often seems to be true to us and the random‐effects model takes into account differences between studies, even if there is no statistically significant heterogeneity. There is, however, a disadvantage to the random‐effects model: it puts added weight onto small studies, which often are the most biased ones. Depending on the direction of effect, these studies can either inflate or deflate the effect size. We choose to use a random‐effects model for all analyses.

Subgroup analysis and investigation of heterogeneity

1. Subgroup analyses
1.1 Primary outcomes

We do not anticipate any subgroup analyses.

2. Investigation of heterogeneity

We will report if inconsistency is high. Firstly, we will investigate whether data have been entered correctly. Secondly, if data are correct, we will inspect the graph visually and remove outlying studies successively 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 10% of the total weighting, we will present data. If not, we will not pool these data and will discuss any 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 is 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

We will carry out sensitivity analyses for primary outcomes only. If there are substantial differences in the direction or precision of effect estimates in any of the sensitivity analyses listed below, we will not add data from the lower‐quality studies to the results of the higher‐quality trials, but will present these data within a subcategory. If their inclusion does not result in a substantive difference, they will remain in the analyses.

1. Implication of randomisation

If trials are described in some way as to imply randomisation, we will compare data from the implied trials with trials that are randomised.

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 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.

3. Assumptions for lost continuous data

Where assumptions have to be made regarding missing SDs (see Dealing with missing data), we will compare the findings when we use our assumption compared with data that are not imputed. If there is a substantial difference, we will report results and discuss them but continue to employ our assumption.

4. Risk of bias

We will analyse the effects of excluding trials that are at high risk of bias across one or more of the domains (see Assessment of risk of bias in included studies).

5. Imputed values

We will also undertake a sensitivity analysis to assess the effects of including data from trials where we use imputed values for ICC in calculating the design effect in cluster‐randomised trials.

6. Fixed‐ and random‐effects

We will synthesise data using a fixed‐effect model; however, we will also synthesise data for the primary outcome using a random‐effects model to evaluate whether this alters the significance of the results.

Acknowledgements

We would like to thank the editorial team of Cochrane Schizophrenia for its support throughout the whole process. The Cochrane Schizophrenia editorial base at the University of Nottingham, Nottingham, UK, 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 terms were developed by the Information Specialist of Cochrane Schizophrenia and the contact author of this protocol. We thank Huiting Xie and Jiaxiang Ni for peer reviewing this protocol.

Contributions of authors

Youssef Latifeh: initiated the protocol, revised the methodology, writing and content of the protocol before submission, guarantor of the review.

Mays Mohsen, Sara Mohamad, Tarek Nassif: developed the background, drafted and reviewed the methods of the protocol.

Sources of support

Internal sources

  • Faculty of Medicine, Damascus University, Syrian Arab Republic.

    Lead author, Youssef Latifeh, and review authors Tarek Nassif, Mays Mohsen and Sara Mohamad are residents at this university.

External sources

  • No sources of support supplied

Declarations of interest

Youssef Latifeh: none known

Mays Mohsen: none known

Sara Mohamad: none known

Tarek Nassif: none known

New

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