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. 2019 Oct 30;2019(10):CD013425. doi: 10.1002/14651858.CD013425

Haloperidol versus olanzapine for people with schizophrenia

Khasan Ibragimov 1,2, Gregory Keane 3,✉, Cristina Carreño Glaría 4, Jie Cheng 5, Augusto Llosa 2
PMCID: PMC6820922

Abstract

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

To assess the clinical effects and safety of haloperidol compared to olanzapine for people with schizophrenia and schizophrenia‐like illnesses.

Background

Description of the condition

Schizophrenia is often a severe and disabling psychiatric disorder, with about 1% of global lifetime prevalence (Zare 2017). The manifestations of schizophrenia are typically grouped into positive, negative, and cognitive sets of symptoms. Positive symptoms include delusions (false beliefs) and hallucinations, while negative symptoms are characterized by lack of normal emotional response, motivation, and interest, poverty of speech, social withdrawal, and an inability to feel pleasure in normally pleasurable activities (Carpenter 1994; Elis 2013). Cognitive impairment is a central component of the disease. This includes deficits of attention, vigilance, visual and verbal memory, learning, reasoning and problem solving, and speed of processing (Green 2004).

The median incidence of schizophrenia is 15.2 per 100,000 population. People with schizophrenia have two to three fold increased risk of death compared to the general population. Migrant status, and living in urban settings are associated with a higher risk of developing the disease (McGrath 2004; McGrath 2008). Male sex is associated with earlier onset and severe cognitive and negative symptoms (Abel 2010). People with schizophrenia generally have a poor prognosis, with one individual out of seven achieving complete remission (Jaaskelainen 2013). According to the findings from the global burden of disease study 2016, schizophrenia contributed 13.4 million years lost due to disability (YLDs), equivalent to 1.7% of the total global YLDs. Lower‐ and upper middle‐income countries (LMIC) experience four times the burden of schizophrenia in high income countries (Charlson 2018).

Antipsychotics remain the mainstay in the treatment of schizophrenia (WHO 2016). Despite the broad range of oral and long acting injectable antipsychotics available, there are cost, availability, and adverse effects to consider in selecting the most appropriate ones. From a humanitarian perspective, along with limited resources in LMICs, it is key to have several options of effective, low cost treatments, which require minimal monitoring.

Description of the intervention

Haloperidol is a first generation antipsychotic, developed by Doctor Paul Janssen in 1958 (Figure 1). There is much evidence supporting the effectiveness of haloperidol in the alleviation of positive symptoms, such as delusions and hallucinations (Lopez‐Munoz 2009). However, haloperidol also has significant adverse effects; the most frequently reported are extrapyramidal, which include movement disorders (dystonia, parkinsonism, tardive dyskinesia) and anticholinergic side effects (constipation, dry mouth, blurred vision (Settle 1983). The usual adult dosage of oral haloperidol is 0.5 mg to 2 mg for moderate, and 3 mg to 5 mg for severe psychosis, taken two to three times per day (Drugs 2018). Haloperidol is one of the four essential drugs recommended by the World Health Organization (WHO) for the treatment of mental and behavioural disorders (WHO 2017).

Figure 1.

Figure 1

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Haloperidol structure

Olanzapine is a second‐generation antipsychotic agent, introduced in the 1990s (Figure 2). Some evidence suggests high efficacy against both positive and negative symptoms (anergia, apathy), as well as fewer extrapyramidal adverse effects (Leucht 1999). However, adverse metabolic effects have been noted, including weight gain (Drugs 2018; Shirzadi 2006). The usual adult doses of oral olanzapine for schizophrenia are 5 mg to 10 mg per day for the initial dose, 10 mg per day for the first several days, with further dose adjustment to reach the target dose; the maximum dose should not exceed 20 mg per day (Drugs 2018).

Figure 2.

Figure 2

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Olanzapine structure

How the intervention might work

The exact mechanism of action of antipsychotics is not entirely understood. Due to its high potency to block dopamine (D2) and adrenergic (alpha 1) receptors, comparatively lower doses of haloperidol are needed to alleviate the positive symptoms of schizophrenia, such as delusions and hallucinations, compared to most other antipsychotics (Schotte 1993). The noted extrapyramidal adverse effects of typical antipsychotics, including haloperidol, may be related to a higher antidopaminergic activity, which implicates the dorsolateral striatum of the brain (Xiberas 2001). Haloperidol achieves peak serum concentration between two and six hours after dosing; the mean half time elimination ranges from 15 to 37 hours (Kudo 1999).

Olanzapine is a comparatively newer antipsychotic, with a strong affinity for dopaminergic (D1 to D5), serotonergic (5‐HT2A, 5‐HT2B, 5‐HT2C), adrenergic (alpha 1), and histamine (H1) receptors. Olanzapine has a relatively weaker antagonism to dopaminergic and muscarinic receptors, compared with other groups of receptors (Bymaster 1999). Studies suggest that high binding affinity of olanzapine to the central and peripheral muscarinic M3, 5‐HT2C, and dopamine‐D2 receptors dysregulates lipid, glucose, and insulin metabolism, causing antipsychotic‐induced weight gain and diabetes (Reynolds 2010; Weston‐Green 2013). After oral administration, olanzapine reaches peak plasma concentrations within five to eight hours. The mean half life elimination ranges from 21 to 54 hours, depending on smoking status, gender, and age (Drugs 2018).

Why it is important to do this review

According to the WHO Mental Health Gap Action Programme (mhGAP), haloperidol is a first line treatment for non‐affective psychosis, such as schizophrenia (WHO 2016). However, some patients do not tolerate it well, due to the extrapyramidal side effects (Fleischhacker 1994). Some evidence suggests that olanzapine is also an effective antipsychotic, which has a different adverse effect profile (i.e. fewer extrapyramidal effects, but can cause weight gain (Duggan 2005). The price of olanzapine has dropped since becoming available in generic form. Currently, olanzapine is not included in the WHO Essential Medicines List (WHO 2017).

From a humanitarian perspective, access to medications, especially for individuals with chronic mental health disorders, is often challenging (Jones 2009). Daily stressors in these contexts can prompt or exacerbate mental disorder (Miller 2010). First generation antipsychotics have strong advantages because of a combination of high efficacy, relatively easy access, and low cost. But some side effects can present problems of tolerability. An available, affordable, and well‐tolerated option is important. Given its efficacy, safety, and cost profile, olanzapine may prove to be a good alternative to haloperidol, but a thorough, up to date, neutral review of the evidence from randomised trials is needed. In some communities where Médecins Sans Frontières (MSF) works, olanzapine is used rather than first generation antipsychotics. However, olanzapine's adverse metabolic effects present their own challenges.

This review aims to present and analyse available high‐quality evidence on the effects of haloperidol and olanzapine for people with schizophrenia. We will update the evidence on haloperidol versus olanzapine from the 2005 Cochrane Review on olanzapine, focusing on their relative efficacy, safety, and tolerability (Duggan 2005). The results from this review can help doctors who are working in humanitarian situations and LMIC, such as those with MSF, to prescribe the most appropriate antipsychotic, or to offer information on a viable alternative in cases of poor tolerability. Depending on the findings, this updated analysis of the literature might also inform MSF's advocacy for an update or expansion to the set of essential medicines.

This review will make an important addition to the family of related Cochrane Reviews (Table 1).

Table 1.

Family of haloperidol and olanzapine reviews

Category Link Title Status
Original parent review Duggan 2005 Olanzapine for schizophrenia Review
Absolute effects Adams 2013 Haloperidol versus placebo for schizophrenia Review
Li 2019 Olanzapine versus placebo for people with schizophrenia Protocol
Comparative effects Bhattacharjee 2016 Aripiprazole versus haloperidol for people with schizophrenia and schizophrenia‐like psychoses Protocol
Asenjo‐Lobos 2018 Clozapine versus olanzapine for people with schizophrenia Protocol
Leucht 2018 Haloperidol versus chlorpromazine for schizophrenia Review
Dold 2015 Haloperidol versus first‐generation antipsychotics for the treatment of schizophrenia and other psychotic disorders Review
Tardy 2014 Haloperidol versus low‐potency first‐generation antipsychotic drugs for schizophrenia Review
Ray 2017 Haloperidol versus risperidone for schizophrenia Protocol
Komossa 2010 Olanzapine versus other atypical antipsychotics for schizophrenia Review
Jayaram 2006 Risperidone versus olanzapine for schizophrenia Review
Discontinuation Essali 2019 Haloperidol discontinuation for people with schizophrenia Review
Alahdab 2012 Olanzapine discontinuation for schizophrenia Protocol
Dose comparison Donnelly 2013 Haloperidol dose for the acute phase of schizophrenia Review
Latifeh 2019 Olanzapine dose for people with schizophrenia Protocol
Techniques of administration Quraishi 1999 Depot haloperidol decanoate for schizophrenia Review
Hanafi 2017 Haloperidol (route of administration) for people with schizophrenia Protocol
Herath Mudiyanselage 2009 Olanzapine depot for schizophrenia Protocol
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Objectives

To assess the clinical effects and safety of haloperidol compared to olanzapine for people with schizophrenia and schizophrenia‐like illnesses.

Methods

Criteria for considering studies for this review

Types of studies

We will consider all relevant randomised controlled trials (RCTs). For analyses, we will include RCTs meeting our inclusion criteria and reporting useable data. If a trial is described as 'double blind' but implies randomisation, we will carry out a sensitivity analysis to analyse the effects of including such trials (see Sensitivity analysis). We will exclude quasi‐randomised studies, such as those that allocate intervention by alternate days of the week.

We will exclude quasi‐randomised studies, such as those that allocate intervention by alternate days of the week. Where people are given treatments in additional to haloperidol versus olanzapine, we will only include data if the adjunct treatment is evenly distributed between groups, and it is only the haloperidol versus olanzapine that is randomised.

Types of participants

Adults, however defined, with schizophrenia or related disorders, including schizophreniform disorder, schizoaffective disorder, and delusional disorder, by any means of diagnosis. Where there are a range of diagnoses, we will include only trials where the majority of participants (over 50%) are diagnosed with schizophrenia or schizophrenia‐like illnesses (nonaffective psychoses).

We are interested in making sure that information is as relevant as possible to the current care of people with schizophrenia, so aim to highlight the current clinical state (acute, early post‐acute, partial remission, remission), and 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). See Subgroup analysis and investigation of heterogeneity.

Types of interventions

1. Haloperidol (oral)

Any dose.

2. Olanzapine (oral)

Any dose.

Types of outcome measures

We plan to divide all outcomes into short‐term (less than six months), medium‐term (seven to 12 months) and long‐term (over 12 months). We will endeavour to report binary outcomes that record 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 in the trials) before any others. Thereafter, we will list binary outcomes, and then continuous outcomes.

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

For valid scales please see Data extraction and management.

Primary outcomes
1. Global state

1.1 Clinically important change in global state 1.2 Relapse

2. Adverse effects or events

2.1 Specific – incidence of clinically important extrapyramidal effects 2.2 Specific – incidence of clinically important metabolic effects

Secondary outcomes
1. Global state

1.1 Any change in global state 1.2 Use of additional medication (other than anticholinergics) for psychiatric symptoms 1.3 Average endpoint or change score on global state scale

2. Mental state
2.1 Overall

2.1.1 Clinically important change in overall mental state 2.1.2 Any change in overall mental state 2.1.3 Average endpoint or change score on overall mental state scale

2.2 Specific – e.g. positive symptoms, negative symptoms

2.2.1 Clinically important change in specific mental state symptoms 2.2.2 Any change in specific mental state symptoms 2.2.3 Average endpoint or change score on specific mental state symptoms scale.

3. Functioning
3.1 General

3.1.1 Clinically important change in general functioning 3.1.2 Any change in general functioning 3.1.3 Average endpoint or change score on general functioning scale

3.2 Specific – e.g. social, cognitive, life skills, working ability

3.2.1 Clinically important change in specific aspects of functioning 3.2.2 Any change in specific aspects of functioning 3.2.3 Average endpoint or change score on specific aspects of functioning scale

4. Adverse effects or events
4.1.General

4.1.1 At least one event or effect 4.1.2 Average endpoint or change score on adverse effect scale

4.2 Specific

4.2.1 Extrapyramidal – incidence of extrapyramidal adverse effects 4.2.2 Extrapyramidal – incidence of use of antiparkinson drugs 4.2.3 Metabolic – incidence of metabolic effects 4.2.4 Metabolic – clinically important change in weight 4.2.5 Metabolic – clinically important metabolic changes (other than weight) 4.2.6 Various other effects – incidence of other clinically important effects 4.2.7 Average endpoint or change score on specific adverse effect scale

5. Quality of life

5.1 Clinically important change in quality of life 5.2 Any change in quality of life 5.3 Average endpoint or change score on quality of life scale

6. Leaving the study early

6.1 For any reason 6.2 For specific reason (e.g. treatment discontinuation, adverse effect)

7. Service use

7.1 Hospital admission 7.2 Days in hospital

8. Economic

8.1 Direct costs 8.2 Indirect costs

'Summary of findings' table(s)

We will use the GRADE approach to interpret findings, and GRADEpro GDT to export data from our review in Review Manager 5 to create a 'Summary of findings' table (GRADEpro GDT; Review Manager 2014; Schünemann 2011). 'Summary of findings' tables provide outcome‐specific information about the overall certainty of the evidence from the included studies in the comparison, the magnitude of effect of the interventions examined, and the sum of available data on all outcomes rated as important to patient care and decision making. We plan to include the following outcomes in the 'Summary of findings' table:

  1. Global state: clinically important change in global state

  2. Global state: relapse

  3. Adverse effects or events: specific – incidence of clinically important extrapyramidal effects

  4. Adverse effects/events: specific – incidence of clinically important metabolic effects

  5. Mental state: clinically important change in overall mental state

  6. Quality of life: clinically important change in quality of life

  7. Leaving the study early, for specific reason – treatment discontinuation

If data are not available for these pre‐specified outcomes but are available for ones that are similar, we will present the closest outcome to the pre‐specified 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:

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

In a study‐based register, searching with the major concept retrieves all the synonyms and relevant studies, because all the studies have already been organised according to their interventions, and linked to the relevant topics (Shokraneh 2017). This allows rapid and accurate searches that reduce waste in the next steps of systematic reviewing (Shokraneh 2019).

This register is compiled by systematic searches of major resources: CENTRAL (Cochrane Central Register of Controlled Trials), MEDLINE, Embase, PubMed, CINAHL (Cumulative Index to Nursing and Allied Health Literature), PsycINFO, AMED (Allied and Complementary Medicine), BIOSIS, ClinicalTrials.gov (US National Institutes of Health Ongoing Trials Register), ISRCTN, WHO ICTRP (International Clinical Trials Registry Platform), and their monthly updates; ProQuest Dissertations and Theses A&I and its quarterly update; Chinese databases (CNKI, SinoMed, VIP, 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 on the records included in 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.

3. Previous Cochrane review

The large Cochrane Review covering this area is now considerably out of date both in content and form (Duggan 2005). Nevertheless, it does contain useful information, including the clustering of the great number of reports into relevant studies. We will continue to use this work as a source document for this update of the haloperidol versus olanzapine comparison.

Data collection and analysis

Selection of studies

Review authors KI and AL will independently inspect citations from the searches, and identify relevant abstracts; CC and GK 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. KI and AL will obtain and inspect full reports of the abstracts or reports that meet the review criteria. CC and GK will re‐inspect 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.

The original review already contains collated clusters of reports relating to trials that are relevant to this new review. KI will inspect Duggan 2005, and all the included trials relevant to the olanzapine versus haloperidol comparison and their references. JC (who is a native Mandirin speaker and writer) will inspect studies in the Chinese language. Jun Xia (see Acknowledgements) will supervise JC.

Data extraction and management

1. Extraction

Review authors KI and AL will independently extract data from all new included studies. In addition, to ensure reliability, CC and GK will independently extract data from a random 10% sample of the total number of included studies. 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 multi‐centre, where possible, we will extract data relevant to each centre. 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. GK and CC will help to clarify issues regarding any remaining problems, and we will document these final decisions.

KI will use the extracted data from relevant studies in Duggan 2005. CC and GK will independently extract data from a random 10% of the relevant trials in Duggan 2005 to ensure reliability of previous data extraction. If the previous data extraction is not reliable, KI and CG will independently extract the data from the previously included studies.

KI will use previous risk of bias tables from Duggan 2005, and update where necessary. Again, CC and GK will cross check a 10% random sample of the previous 'Risk of bias' tables for reliability. If the previous tables are not reliable, all review authors will complete new 'Risk of bias' tables for all previously included studies.

JS will extract data and complete new 'Risk of bias' table for the studies in the Chinese language, and Jun Xia will supervise.

2. Management
2.1 Forms

We will extract data onto standard, pre‐designed, simple 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);

  • the measuring instrument has not been written or modified by one of the trialists for that particular trial; and

  • the instrument is a global assessment of an area of functioning, and not a subscore that has not been validated or shown to be reliable as a stand alone instrument. However there are exceptions; we will include subscores from mental state scales that measure positive and negative symptoms of schizophrenia.

Ideally, the measurment instrument should either be a self‐report, or be 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), which can be difficult to obtain in unstable and difficult‐to‐measure conditions, such as schizophrenia. We have decided to use endpoint data first, 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 including them.

For endpoint data from studies including fewer than 200 participants:

  1. When a scale starts from zero, we will subtract the lowest possible value from the mean, and divide this by the standard deviation (SD). If this value is less 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 suggests that the data are skewed: we will enter these data and test whether their inclusion would change the results substantially. If such data change results, we will enter them 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).

  2. 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, regardless 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 plan, 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 cutoff 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 a clinically significant response (Leucht 2005a; Leucht 2005b). If data based on these thresholds are not available, we will use the primary cutoff 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 haloperidol versus 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 KI and AL will work independently to assess risk of bias by using the criteria described in the revised guidance for rating risk of bias (RoB2 2016). 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, which 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 any lack of concurrence in quality assessment, but if disputes arise regarding the category to which a trial is to be allocated, we hope to be able to resolve this by discussion.

At the time of writing (2019) the 'Risk of bias' assessment questions 1 and 2 relate to the methods of the study, and therefore, will be completed for all included trials. Questions 3 to 5 are outcome‐specific, so KI and AL will only complete them for outcomes that are to be included in the 'Summary of findings' table. We are unsure how to display these data in figures as we are currently using RevMan (version 5.3.5) with no facility for integration of Risk of Bias (version 2) tables into the forest plots. Use of the older RevMan 5.3.5 was necessary to ensure full compatibility with the older version of this review and sharing of files by authors working independently. We hope to use this review to experiment with Risk of Bias (v2) ‐ MS Excel tool to see if this produces figures that are of value to the readers of the review.

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 intuitive, rounded risks for the haloperidol group and, using the RR, apply this to the olanzapine group for easy comparison.

2. Continuous data

For continuous outcomes, we will estimate mean difference (MD) between groups. We prefer not to calculate effect size measures (SMD). However, if similar scales 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 intra‐class 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 intra‐class correlation coefficients 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 intra‐class correlation coefficient (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 intra‐class correlation coefficients 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 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, 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 2011). Where additional treatment arms are not relevant, we will not use data from these arms.

Dealing with missing data

1. Overall loss of credibility

At some degree of loss of follow‐up, data must lose credibility (Xia 2009). If more than 50% of data is missing for any outcome, we will not use them in the meta‐analyses. If more than 50% is lost to follow‐up in one treatment arm, but the total loss is less than 50%, we will address this by downgrading the quality of the evidence for the outcome involved (by two points). We will also downgrade the quality of the evidence (by one point) if the total loss is between 25% to 50%.

2. Binary

If attrition for a binary outcome is between 0% and 50%, and these data are not clearly described, we will present data on an intention‐to‐treat analysis (ITT) basis. We will assume that those who left the study early had the same rates of negative outcome as those who completed. We will use the rate of those who stayed in the study ‐ in that particular arm of the trial ‐ and apply it to those who did not. We will undertake a sensitivity analysis to test how prone the primary outcomes are to change, when we compare data from people who completed the study to that point to the intention‐to‐treat analysis using the above assumptions.

3. Continuous
3.1 Attrition

We will use data when attrition for a continuous outcome is between 0% and 50%, and only data from people who completed the study to that point are reported.

3.2 Standard deviations

If standard deviations (SDs) are not reported, we will try to obtain the missing values from the trial authors. If they are not available, but we have an exact standard error (SE) and CIs available for group means, and either a P value or t value for differences in mean, we can calculate SDs according to the rules described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). When only the SE is reported, SDs are calculated with 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 2011). 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 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, 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 (Leon 2006). Therefore, we will not exclude studies based on the statistical approach used. However, we will use the more sophisticated approaches first, i.e. we will use MMRM or multiple‐imputation rather than LOCF, and we will only present completer analyses if ITT data are not available. We will address this issue when we assess the incomplete outcome data domain.

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 or situations that are clearly different to the participants or situations in the other included studies and 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 results visually to investigate the possibility of statistical heterogeneity.

3.2 Using 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 of 50% or higher, and accompanied by a statistically significant Chi² statistic, as evidence of substantial heterogeneity (Deeks 2011). When substantial levels of heterogeneity are found for the primary outcomes, 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 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 the 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 ten or fewer studies, or where all studies are of similar size. In other cases, where funnel plots are possible, we will seek statistical advice for 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. However, there is a disadvantage to the random‐effects model: it puts added weight onto small studies, which often are the most biased ones. Depending on the direction of effect, these studies can either inflate or deflate the effect size. We will choose to use random‐effects model for our analyses.

Subgroup analysis and investigation of heterogeneity

1. Subgroup analyses
1.1 Primary outcomes only

Where data are available we will carry out sub‐group analyses for

  • First episode psychoses

  • Treatment resistant participants

2. Investigation of heterogeneity

We will report if heterogeneity is high. Firstly, we will investigate whether data have been entered correctly. Secondly, if data are correct, we will inspect the forest plots 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 the 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 plan to carry out sensitivity analyses, for primary outcomes only, to explore the influence of the factors listed below. If there are substantial differences in the direction or precision of effect estimates in any of the sensitivity analyses listed below, we will remove data from the lower‐quality trials from analyses and present these data separately and discuss issues. Where there are no substantial differences in the direction or precision of effect estimates we will keep data from the lower‐quality trials in the relevant analyses.

1. Implication of randomisation

We will analyse the effects of incuding data from lower‐quality trials where randomisation is implied rather than clearly described.

2. Assumptions for lost data

We will analyse the effects of including data where we have made assumptions regarding lost data (see Dealing with missing data).

3. Risk of bias

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

4. Imputed values

We will analyse the effects of including data from trials where we use imputed values for ICC to calculate the design effect in cluster‐randomised trials (see Unit of analysis issues).

5. Fixed‐ and random‐effects

We intend to synthesise data using random‐effects model; however, we will also synthesise data using fixed‐effect model to evaluate whether this alters the size or direction of effect estimates.

Acknowledgements

We would like to thank the editorial team of Cochrane Schizophrenia for support throughout the whole process. Cochrane Schizophrenia's 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.

Jun Xia is a review author with Cochrane Schizophrenia. She has decades of experience in undertaking these reviews and we are grateful for her supervision of JC.

We would like to thank Lorna Duggan for enabling us to use her previous data extraction (Duggan 2005)

What's new

Date Event Description
10 December 2019 Amended Error in numbering of Types of outcome measures corrected.
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Contributions of authors

Khasan Ibragimov: writing the first draft of the protocol, entering data into RevMan 5, extracting data from papers.

Gregory Keane: conceiving and co‐ordinating the review, editing the protocol for content, revising the methodology

Cristina Carreno: conceiving and co‐ordinating the review, editing the protocol for content, revising the methodology.

Jie Cheng: considering the text for the procedure by which Chinese trials are to be selected and data extracted.

Augusto Llosa: conceiving and co‐ordinating the review, editing the protocol for content, revising the methodology.

Sources of support

Internal sources

  • No sources of support supplied

External sources

  • Medicine sans Frontieres, France.

    This work is funded in full by the humanitarian non‐profit agency Medecins Sans Frontieres (MSF). AL, GK, CC are full time salaried employees of MSF; KI is a Masters Student at EHESP funded by the scholarship Campus France, and an intern at MSF.

Declarations of interest

Khasan Ibragimov: none known

Gregory Keane: none known

Cristina Carreno: none known

Jie Cheng: none known.

Augusto Llosa: none known

Edited (no change to conclusions)

References

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