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. 2019 Apr 15;2019(4):CD013310. doi: 10.1002/14651858.CD013310

Olanzapine versus placebo for people with schizophrenia

Yan Li 1,✉, Changjun Du 2, Ni Jiaxiang 3, Yang Liqiang 1, Fang Qi 4
PMCID: PMC6462848

Abstract

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

To systematically assess the clinical effects and safety of olanzapine compared with placebo for people with schizophrenia.

Background

Description of the condition

Schizophrenia is a chronic serious mental disorder with a lifetime prevalence of approximately 0.3% to 0.7% that usually occurs in young adulthood (APA 2013; Hafner 1994; Kumra 2001). Schizophrenia is diagnosed more frequently in males than in females (Castle 1991; Picchioni 2007). The symptoms of schizophrenia are usually divided into 'positive symptoms' (such as hallucinations and delusions) and 'negative symptoms' (such as emotional apathy, lack of drive, poverty of speech, social withdrawal, and self neglect) (NICE 2014). However, emotional symptoms such as depression are also common during the entire course of the illness, ranging from 7% to 65%, with a modal rate of 25% (Tollefson 1998a). In general, schizophrenia progresses through several stages, namely the premorbid stage, the prodrome stage, the rapid progress stage, and the deterioration or residual stage (Tasman 2015). In different studies, due to different definitions of recovering, the incidence of improvement or complete remission ranges from 45% to 67% (Tasman 2015). An estimated 40% to 60% of people with schizophrenia are likely to experience lifelong social and occupational impairment (Tasman 2015). Approximately 80% of people with schizophrenia will relapse within five years (NICE 2014). Life expectancy is reduced by 20% in individuals with schizophrenia, with 60% of the excess mortality due to physical illness (such as weight gain, diabetes, metabolic syndrome, cardiovascular and pulmonary disease) (APA 2013; Ifteni 2014; Mazi‐Kotwal 2011). Of note, schizophrenia itself is considered to be one of the risk factors for the development of metabolic syndrome. Furthermore, the use of antipsychotic drugs, especially atypical antipsychotics, has also been shown to increase the risk of metabolic syndrome (Casey 2004; O'Donoghue 2013; Scheepers‐Hoeks 2008; Yogaratnam 2013). The mortality rate associated with schizophrenia is approximately twice that of the general population (standardised all‐cause mortality ratio 2.6), with no difference between males and females (Tasman 2015). The current research suggests that antipsychotic treatment can effectively improve the prognosis and reduce the mortality of people with schizophrenia (Cullen 2013). However, adherence to antipsychotics is poor, which can be due to multiple risk factors such as unpleasant side effects or safety problems associated with antipsychotics, alcohol or drug abuse, a person's poor subjective judgment of the effect of the drug, or the person's belief that the condition has improved (Kulkarni 2015; Moritz 2014; Olivares 2013). This discontinuation of treatment is one of the main factors associated with relapse and deterioration (García 2016). In addition, antipsychotics, although effective for positive symptoms, often do not significantly improve primary negative symptoms of schizophrenia (Gaebel 2014; Kopelowicz 2000).

Description of the intervention

Antipsychotics have become one of the main treatments for schizophrenia. They are divided into typical, or first‐generation antipsychotics (such as haloperidol, perphenazine, chlorpromazine), and atypical, or second‐generation antipsychotics (such as clozapine, olanzapine, risperidone, quetiapine, amisulpiride, aripiprazole, zotepine, ziprasidone, paliperidone, asenapine, Iloperidone, and lurasidone).

Current research suggests that both typical and atypical antipsychotics have positive effects on positive symptoms (Gaebel 2014; Kahn 2008; Kryzhanovskaya 2009; Marques 2011; Zhu 2017). Some findings suggest that, when compared with typical antipsychotics, atypical antipsychotics may have additional advantages such as improving negative and depressive symptoms, improving quality of life, and causing less frequent extrapyramidal side effects (Duggan 2005; Gründer 2016; Leucht 2009; Tollefson 1998b; Zhu 2017).

Olanzapine is an atypical antipsychotic that has three formulations: the oral tablet, the acute intramuscular injection, and the long‐acting intramuscular depot. Intramuscular olanzapine was mainly used to treat acute agitation, while oral tablet and olanzapine long‐acting injection (OLAI) are mainly used for acute and maintenance treatment. Published research evaluating adolescents and adults with schizophrenia has demonstrated that the three formulations of olanzapine have significant efficacy in treating positive symptoms and acute agitated behaviour (Beasley 1996a; Chan 2014; Dellva 1997; Duggan 2005; Jones 2001; Kishi 2015; Kryzhanovskaya 2009; Krzystanek 2011; Woods 2003), and are moderately better than haloperidol or risperidone for treating negative, Beasley 1996b; Hamilton 1998, and emotional symptoms (Tollefson 1998b).

Due to the compound's long half‐life, olanzapine can be dosed once daily, although it is frequently administered twice a day. The average dose ranges from 15 to 20 mg once daily. Common adverse events include weight gain, hyperglycaemia, hyperlipidaemia, sedation, dry mouth, nausea, lightheadedness, orthostatic hypotension, dizziness, constipation, headache, akathisia, and transient elevation of hepatic transaminases (Komossa 2010; Tasman 2015).

The half‐life of OLAI is 30 days. The peak concentration of OLAI mostly occurs two to four days after injection, and steady state is reached approximately at 12 weeks (Heres 2014). Olanzapine long‐acting injection is usually intramuscularly injected with a two‐ or four‐week injection interval, with a dosage range of 45 to 450 mg. The safety profile of OLAI is similar to the safety profile of oral olanzapine, except for the risk of postinjection delirium/sedation syndrome (PDSS) (such as sedation, confusion, dysarthria, somnolence, dizziness, and disorientation) (Bushe 2015). Postinjection delirium/sedation syndrome often occurs within one to three hours after intramuscular injection, and recovers within an average of 72 hours (Meyers 2017), therefore patients should be observed for at least three hours after every injection.

How the intervention might work

Olanzapine, a thienobenzodiazepine compound approved in 1996, has antagonistic effects at several receptors including dopamine D1 through D4, serotonin 5‐HT2A, 5‐HT2C, and 5‐HT6, α1, H1, and m1 receptors as well as DA and 5‐HT transporters. Furthermore, the antiserotonergic effect is more potent than the antidopaminergic activity (Miyamoto 2005). Olanzapine binds weakly to GABAA, benzodiazepine, and beta‐adrenergic receptors (Tasman 2015). Its unique mechanism of action may explain its efficacy in ameliorating positive, negative, cognitive, and emotional symptoms associated with schizophrenia in addition to improving sleep difficulties (Miyamoto 2005). However, olanzapine's D2 antagonist properties may increase the risk of extrapyramidal side effects, negative symptoms, and cognitive impairment, while simultaneously improving positive symptoms (Miyamoto 2005; Stahl 2013).

Olanzapine's 5HT2C antagonist properties may contribute to its efficacy in improving mood and cognitive symptoms (Stahl 2013), while its 5HT2A antagonist properties may ameliorate negative symptoms (Miyamoto 2005). In addition, olanzapine's 5HT2A and M1 antagonist properties may reduce the occurrence of extrapyramidal side effects (Miyamoto 2005). However, olanzapine can be somewhat sedating in some patients, as it does have antagonist properties at M1, H1, and α1 receptors. Furthermore, olanzapine is consistently associated with weight gain, which may be due to its antihistaminic and 5HT2C antagonist properties. Of significance, olanzapine ranks among the antipsychotics with the greatest known cardiometabolic risks, as it robustly increases fasting triglyceride levels and increases insulin resistance in at least some patients (Stahl 2013).

Why it is important to do this review

Olanzapine has become one of the more commonly used antipsychotic drugs administered to children, adolescents, adults, and elderly people with schizophrenia (Halfdanarson 2017). Although several previous placebo‐controlled studies or reviews have reported that olanzapine improves the positive symptoms associated with schizophrenia, amelioration of primary negative symptoms is controversial (Harvey 2016; Kopelowicz 2000; Tollefson 1997). In addition, the placebo effect has been shown to be a major concern in clinical psychiatric research (Weimer 2015). In a review of a comparative studies of antipsychotics, the placebo efficacy was as high as 21.3% (Oliveira 2009). Another review showed that the degree of placebo response had increased over decades in people with acute exacerbations of schizophrenia (Leucht 2017). It is therefore necessary to systematically evaluate the detailed effects of olanzapine versus placebo in the treatment of schizophrenia to determine both its associated benefits and harm in an effort to guide clinical practice. This comparison of olanzapine versus placebo will be a part of a family of olanzapine reviews that update and expand the previous review 'Olanzapine for schizophrenia' (Duggan 2005).

Objectives

To systematically assess the clinical effects and safety of olanzapine compared with placebo 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 participants have been given treatments additional to olanzapine, we will only include data if the adjunct treatment is evenly distributed between groups, and only olanzapine has been randomised.

Types of participants

We will include people with no age or gender limitations, and with a diagnosis of schizophrenia or related disorders, including schizophreniform disorder, schizoaffective disorder, and delusional disorder, by any one of several diagnostic criteria (such as international standards (International Statistical Classification of Diseases and Related Health Problems 10th Revision (ICD‐10), Diagnostic and Statistical Manual of Mental Disorders (DSM: DSM‐III, DSM‐III‐R, DSM‐IV, DSM‐IV‐TR, DSM‐V), Chinese Classification of Mental Disorders (CCMD: CCMD‐1, CCMD‐2, CCMD‐3). We will not include people with a diagnosis of schizophrenia and who are aggressive or agitated; olanzapine for this situation is assessed in another Cochrane Review (Belgamwar 2005)

We are interested in ensuring that information is as relevant as possible to the current care of people with schizophrenia, therefore we aim to highlight the current clinical state clearly (acute, early postacute, 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 (e.g. negative symptoms, treatment‐resistant illnesses).

Types of interventions

1. Olanzapine

Any dose administered as oral tablets or intramuscular injection (short‐ or long‐acting injectable).

2. Placebo

Active or inactive.

Types of outcome measures

We aim to divide all outcomes into short term (up to 12 weeks), medium term (13 to 26 weeks), and long term (over 26 weeks).

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.

Primary outcomes

For outcomes such as 'clinically important change', 'any change', and 'relapse', we will use the definition used by each of the trials.

1. Global state

1.1 Clinically important change in global state (e.g. global impression less than much improved, or less than 50% reduction on a specified rating scale)

2. Mental state

2.1 Clinically important change in general mental state

3. Adverse effect/events

3.1 Death (suicide and natural causes)

Secondary outcomes
1. Global state

1.1 Relapse 1.2 Any change in global state 1.3 Average endpoint or change score on a global state scale

2. Mental state
2.1 General

2.1.1 Any change in general mental state 2.1.2 Average endpoint or change score on a general mental state scale

2.2 Specific

2.1 Clinically important change in specific symptoms (e.g. positive, negative, affective, cognitive symptoms of schizophrenia) 2.2 Any change in specific symptoms 2.2 Average endpoint or change score on a specific symptom scale

3. Service use

3.1 Number of hospitalisations 3.2 Number of days in hospital

4. Functioning
4.1 General

4.1.1 Clinically important change in general functioning, including working ability 4.1.2 Any change in general functioning ‐ as defined by individual studies 4.1.3 Average endpoint or change score on a general functioning scale

4.2 Specific

4.2.1 Clinically important change in specific aspects of functioning, such as life skills 4.2.2 Any change in specific aspects of functioning, such as life skills 4.2.3 Average endpoint or change score on a specific aspects of functioning scale

5. Adverse events

5.1 At least one adverse effect/event 5.2 Clinically important adverse effect 5.3 General and specific adverse effects (except death) 5.4 Average endpoint or change score on an general/specific adverse effect scale

6. Leaving the study early

6.1 For any reason 6.2 For specific reason

7. Quality of life

7.1 Clinically important change in general/specific aspects of quality of life 7.2 Any change in general/specific aspects of quality of life 7.2 Average endpoint or change score on a general/specific aspects of quality of life scale

'Summary of findings' table

We will use the GRADE approach to interpret findings and employ GRADEpro GDT to export data from our review to create a 'Summary of findings' table (Schünemann 2011). These tables 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

  2. Mental state ‐ general: clinically important change in general mental state

  3. Adverse event: death: suicide and natural causes

  4. Functioning ‐ general: clinically important change in general functioning

  5. Adverse effects: clinically important metabolic effect

  6. Leaving the study early: for any reason

  7. Quality of life: clinically important change in general quality of life

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 Group's Study‐Based Register of Trials

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

(Olanzapine AND Placebo) in Intervention Field of STUDY

In such a study‐based register, 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 (the Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE, Embase, CINAHL (Cumulative Index to Nursing and Allied Health Literature), PsycINFO, PubMed, US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov, World Health Organization International Clinical Trials Registry Platform (WHO ICTRP)) and their monthly updates, ProQuest Dissertations and Theses A&I and its quarterly update, Chinese databases (CBM (Chinese Biomedical Literature Database), CNKI (China National Knowledge Infrastructure), and Wanfang) and their annual updates, handsearches, grey literature, and conference proceedings (see Group's website). There will be 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 'Characteristics of included studies' or 'Characteristics of studies awaiting classification' tables.

Data collection and analysis

Selection of studies

Review authors (YL and CD) will independently inspect citations from the searches and identify relevant abstracts; review author FQ will independently re‐inspect 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. YL and CD will then obtain and inspect the full reports of the abstracts or reports meeting the review criteria. FQ will re‐inspect a random 20% of these full reports 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 CD) will extract data from all included studies. In addition, to ensure reliability, FQ 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 this information only if two review authors independently obtain the same result. If studies are multicentre, then where possible we will extract data relevant to each centre. Any disagreements will be discussed and decisions documented. If necessary, we will attempt to contact authors through an open‐ended request in order to obtain missing information or for clarification. FQ 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 be either 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 if this is the case or not in 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; however, calculation of change needs two assessments (baseline and endpoint), which can be difficult to obtain 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. 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, it is suggested 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 the results, then 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 un‐improved'), we will report data where the left of the line indicates an unfavourable outcome and note this in the relevant graphs.

Assessment of risk of bias in included studies

Review authors (YL and CD) will independently assess risk of bias using the 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 YL and CD disagree, we will make the final rating by review team consensus. Where inadequate details of randomisation and other characteristics of trials are provided, we will attempt to contact the authors of the studies 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 review team discussion.

We will note the level of risk of bias in both the text of the review, 'Risk of bias' summary, 'Risk of bias' graph, 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 (Boissel 1999); and that odds ratios 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/s, 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 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 ICCs and relevant data documented in the report been taken 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 wash‐out 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, we will present the additional treatment arms in comparisons if they are relevant. 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. However, if more than 50% of data 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 downrating quality. Finally, we will also downgrade quality within the 'Summary of findings' table/s 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 will all be assumed to have the same rates of negative outcome as those who completed, with the exception of the outcome of death and adverse effects. For these outcomes we will use the rate of those who stayed 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 from only 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 the point of follow up are reported.

3.2 Standard deviations

If standard deviations (SDs) are not reported, we will attempt to obtain the missing values from the study authors. If these are 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 value or t value is 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 to thus 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 who were lost to follow‐up

Various methods are available to account for participants who left the trials early or who were lost to follow‐up. Some trials only 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 reasons for leaving the studies 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, that is 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' 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 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 that 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 per Chapter 9 of the Cochrane Handbook for Systematic Reviews of Interventions (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 Section 10.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Sterne 2011).

1. Protocol versus full study

We will attempt to locate protocols of the included trials. If the protocol is available, we will compare outcomes in the protocol with those in the published report. If the protocol is not available, we will compare outcomes listed in the methods section of the trial report with the 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, in that it puts added weight onto small studies, which are often 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 aim, if possible, to conduct subgroup analyses on the following factors:

  1. age of participants (< 18 years versus ≧ 18 years);

  2. different types of olanzapine administration (oral tablets versus intramuscular injection)

2. Investigation of heterogeneity

We will report if inconsistency is high. We will investigate whether data have been entered correctly or that we have made no unit of analysis errors. If the high levels of heterogeneity remain, we plan not to undertake a meta‐analysis at this point, because if there is considerable variation in results, and particularly if there is inconsistency in the direction of effect, it may be misleading to quote an average value for the intervention effect.

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 must 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 the results and discuss them but continue to employ our assumption.

3. Assumptions for lost continuous data

Where assumptions must 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 the 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 'Risk of bias' 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‐effect and random‐effects

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

Acknowledgements

The Cochrane Schizophrenia Group Editorial Base at the University of Nottingham, Nottingham, UK, produces and maintains standard text for use in the Methods section of their reviews.

We would like to thank the Cochrane Schizophrenia Group and its editorial team for their help and editorial advice throughout the completion of this protocol.

We thank peer reviewers Shuhua Wang, Ángel Luis Asenjo‐Esteve, and Marie Purcell for their helpful comments.

We would like to thank Systematic Review Solutions Ltd for their effort on providing methodological guidance. We also thank Margueritte Mabry White (MD, Global Community Writer) for her help on proofreading of this protocol.

Contributions of authors

Yan Li: contributed to writing the protocol.

Changjun Du: contributed to writing the protocol.

Ni Jiaxiang: contributed to review of the protocol.

Yang Liqiang: contributed to review of the protocol.

Fang Qi: contributed to writing the protocol.

Sources of support

Internal sources

  • Xuanwu Hospital, Capital Medical University, Beijing, China.

    Employs review authors Yan Li, Ni Jiaxiang, and Yang Liqiang

  • Tianjin Hospital, Tianjin, China.

    Employs review author Changjun Du.

  • Systematic Review Solutions Ltd, UK.

    Employs review author Fang Qi.

  • The Affiliated Wuxi People's Hospital of Nanjing Medical University, Wuxi, China.

    Employs review author Jiaying Wang.

External sources

  • Beijing Postdoctoral Research Foundation [2018‐ZZ‐108, 2018], China.

Declarations of interest

Yan Li: none known

Changjun Du: none known

Ni Jiaxiang: none known

Yang Liqiang: none known

Fang Qi: none known

New

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