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. 2017 Jul 20;2017(7):CD012728. doi: 10.1002/14651858.CD012728

Haloperidol versus risperidone for schizophrenia

Sujoy Ray 1,✉, Amita Ray 2, Arun Gopi 3, Robert Hunter 4
PMCID: PMC6483197

Abstract

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

To review the clinical effectiveness and safety of haloperidol compared with risperidone for people with schizophrenia.

Background

Description of the condition

Schizophrenia is a psychiatric condition characterised by certain typical manifestations. These manifestations are classified as positive and negative symptoms. Among the positive symptoms are delusions (fixed, false beliefs and perceptions without a stimulus). Among negative symptoms are apathy, paucity of speech, catatonic symptoms such as mannerisms or bizarre posturing and blunting or incongruity of emotional responses. These usually result in social withdrawal and lowering of social performance; which are generally not due to depression or antipsychotic medication.

There are specific diagnostic guidelines for schizophrenia in the International Classification of Diseases (ICD‐10) classification of Mental and Behavioural Disorders. It is also specified that the symptoms should have been clearly present for most of the time during a period of one month or more. Conditions meeting such symptomatic requirements, but of a duration less than one month (whether treated or not), should be diagnosed in the first instance as acute schizophrenia‐like psychotic disorder and are classified as schizophrenia if these symptoms persist for longer periods (ICD‐10 1992). As per the Diagnostic and Statistical Manual of Mental Disorders (DSM‐5) criteria, schizophrenia is diagnosed when two or more of delusions, hallucinations, disorganised speech, catatonic behaviour, or negative symptoms are present for at least one month, and a sx‐month duration of signs of disturbance in functioning such as self‐care, work or interpersonal relations (DSM‐5). There are other disorders such as persistent delusion disorder, which is characterised by the development either of a single delusion or of a set of related delusions, but which are usually persistent and sometimes lifelong. Other psychopathology pertaining to schizophrenia is characteristically absent. Another disorder group is that of schizoaffective disorders wherein both definite schizophrenic and definite affective symptoms are prominent simultaneously, or within a few days of each other, within the same episode of illness, and when, as a consequence of this, the episode of illness does not meet criteria for either schizophrenia or a depressive or manic episode (ICD‐10 1992).

In the age group of 15 to 44 years, schizophrenia is among the top leading causes of disease‐related disability (WHO 2001). The suffering and disability is considerable with 80% to 90% of people affected unable to work (Marwaha 2004) and 10% dying (Tsuang 1978). People with schizophrenia are more likely to die (by about three times) than the general population.(Olfson 2015). The causes are from various medical conditions such as cancer, cardiovascular disease and disturbance of metabolic parameters like glucose and lipids(Laursen 2012). One per cent of the American population is believed to have been affected with schizophrenia with 60% of adults with schizophrenia using healthcare services and 64.3% using all care services including health care (Regier 1993). Globally, the median prevalence of schizophrenia has been found to be 4.6/1,000 for point prevalence, 3.3/1,000 for period prevalence and 4.0 for lifetime prevalence with higher rates among migrants and homeless people,though no significant differences exist in terms of gender, nor between urban, rural, and mixed areas (Bhugra 2005).

Description of the intervention

There is a multitude of treatments available for schizophrenia (Dold 2014; Hasan 2012). Antipsychotics are the mainstay of treatment and are classified as typical or atypical depending upon the actions on various receptors (Davis 1977; Tandon 2011).

The first typical antipsychotics were discovered when there was found to be a calming effect on using a phenothiazine as an antihistaminic medication prior to surgery.(López‐Muñoz 2005) Typical antipsychotics tend to be effective for positive symptoms of schizophrenia, but have significant adverse effects.

An acute side‐effect is dystonia, which can be life‐threatening especially in critical regions such as the larynx (Christodoulou 2005). Antipsychotic‐induced parkinsonism is another side‐effect which has been linked to genes such as ZFPM2 SNP and rs12678719(Greenbaum 2012). Both of these side‐effects are reversible. A particularly distressing and often irreversible side‐effect is tardive dyskinesia (Ramachandraiah 2009). Haloperidol, a butyrophenone derivative, is the most used of the typical antipsychotics.

The atypical antipsychotics, developed later on, are also effective for the symptoms of schizophrenia (Swanson 2004), but have a lesser propensity to cause the serious adverse effects when compared to typical antipsychotics (Shen 1999). Risperidone, an atypical antipsychotic, is a benzisoxazole derivative first made available for the care of those with schizophrenia in 1986. Since then, clinical trials have been conducted to evaluate its efficacy and safety (Chouinard 1993; He 1995).

Risperidone has a beneficial effect on both the positive and negative symptoms of schizophrenia (Edwards 1994; Livingston 1994). The effects of risperidone on negative symptoms compared to haloperidol is under further study (Mirabzadeh 2014). It is also claimed that risperidone may reduce the decline in memory, attention and concentration associated with schizophrenia (Meltzer 1994, Stip 1996). Individuals with schizophrenia previously resistant to treatment may be helped by treatment with risperidone (Edwards 1994; Meltzer 1994).

Risperidone does not bind to the sites in the brain (cholinergic/muscarinic receptors) that cause dry mouth, blurred vision, constipation and urinary retention, often associated with haloperidol (Edwards 1994; Gupta 1994; He 1995; Keltner 1995). However, risperidone is associated with side‐effects such as sedation, giddiness, movement difficulties, headache and weight gain (Remington 1993). Concern has been raised that the emphasis on primarily controlling the positive symptoms of schizophrenia may deflect attention from the tendency of antipsychotics to cause what are considered minor side‐effects, and that this is often illustrated by the paucity of information regarding such side‐effects in antipsychotic drug trials (Kane 1990).

How the intervention might work

Typical antipsychotics are predominantly D2 receptor antagonists and reduce dopaminergic transmission in the mesolimbic, meso cortical, nigrostriatal and tuberoinfundibular pathways.The action on the mesolimbic pathway is primarily responsible for the antipsychotic effects which are of use in the treatment of Schizophrenia (Crow 1980; Sadock 2009).

Atypical antipsychotics occupy D2 receptors transiently and then rapidly dissociate. They also block 5‐HT2A receptors at the same time and this serotonin‐dopamine balance confers atypicality. While 5‐HT2A receptors are readily blocked at low dosages of most atypical antipsychotic drugs, the dosages at which this happens are below those needed to alleviate psychosis. The antipsychotic threshold occupancy of D2 for antipsychotic action remains at about 65% for both typical and atypical antipsychotic drugs, regardless of whether 5‐HT2A receptors are blocked or not. At the same time, the antipsychotic threshold occupancy of D2 for eliciting extrapyramidal symptoms (EPS) remains at about 80% for both typical and atypical antipsychotics, regardless of the occupancy of 5‐HT2A receptors.(Seeman 2002)

The other effects of both classes also vary considerably.

Typical antipsychotics such as haloperidol cause neuron apoptosis by a free radical‐induced mechanism, involving Bcl‐XS, P53, cytochrome C translocation and Caspase 3 activation. They also reduce levels of neurotrophin such as brain‐derived neurotrophic factor, nerve growth factor and neurotrophin‐3. Atypicals like risperidone have effects opposite to these by increasing neurotrophin, improving cell survival and enhancing neurogenesis. They also prevent the effects of typical induced toxicity. The mechanism is linked to the inverse agonist action on 5HT receptors, particularly the 2A subset (Nandra 2012).

Why it is important to do this review

This review is important because it aims to directly compare efficacy and safety of two popular and well‐used antipsychotics and provide information that could help clinicians and patients in treatment decisions. It is often a dilemma to the treating psychiatrist to determine which drug to choose in a given condition (Andreasen 1985; Christison 1991). Recent research suggests decision making would be helped if direct comparisons between individual drugs are available rather than comparing one group (typical antipsychotics ) with another (atypical antipsychotics) (Leucht 2013).

As well as efficacy and safety, cost needs to be considered. According to MIMS and the Scottish Drug Tarrif, the total number of prescription items dispensed for psychoses and related disorders increased between 2012/13 and 2013/14 (from 836,756 to 864,241 items; an increase of 3.3%) (MIMS 2016; Scottish Drug Tariff 2015). This follows a gradual increase over the last 10 years; the total number of dispensed items has increased by 38.7% between 2004/05 and 2013/14 (from 622,979 items in 2004/05) (Scottish Drug Tariff 2015). Under these circumstances it would be necessary to select the more cost‐effective treatment. However calculating cost‐effectiveness in mental health is complex and it can be argued for example, that improved treatment efficacy may reduce costs incurred as a result of hospitalisation (Addington 1993; Guest 1996). Risperidone is relatively more expensive than haloperidol, however, when depot preparations of both are compared, some studies have found depot risperidone more cost‐effective than depot haloperidol (Curtis 1995; Liorca 2005)

A Cochrane review (Hunter 2003), which compared risperidone with typical antipsychotics as a group found that risperidone caused fewer side‐effects (movement disorders and sedation) as compared to typical antipsychotics. Risperidone was also found to be more expensive. The review stated that since most of the advantages of risperidone have been observed in comparison to haloperidol, it would we worthy to directly compare trials related to only those two particular drugs.

This review title is the resulting of splitting the Cochrane reviewRisperidone versus typical antipsychotic medication for schizophrenia (Hunter 2003), and will become part of a set of haloperidol direct comparison reviews (see Table 1).

Table 1.

Haloperidol direct comparison reviews currently registered with Cochrane Schizophrenia

Review Title Stage Reference DOI
Aripiprazole versus haloperidol for people with schizophrenia and schizophrenia‐like psychoses Protocol Bhattacharjee 2016 10.1002/14651858.CD012073
Haloperidol versus chlorpromazine for schizophrenia Full review Leucht 2008 10.1002/14651858.CD004278.pub2
Haloperidol versus placebo for schizophrenia Full review Adams 2013 10.1002/14651858.CD003082.pub3
Haloperidol versus risperidone for schizophrenia ‐ Current review
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Objectives

To review the clinical effectiveness and safety of haloperidol compared with risperidone for people with schizophrenia.

Methods

Criteria for considering studies for this review

Types of studies

All randomised controlled trials where the assessor at least is blinded. If a trial is described as 'double‐blind' but implies randomisation only, we will complete a sensitivity analysis (see Sensitivity analysis). We will exclude quasi‐randomised studies. Where people are given additional treatments, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the aspects related to haloperidol and risperidone 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. We will exclude trials where the primary diagnosis is of a mood disorder with psychotic symptoms. Also, we will exclude trials with schizophrenia showing a clear causal correlation with substance use. We will also account for other treatments such as mood stabilisers that have been used concomitantly so that their influence/confounding factor is matched.

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

Types of interventions

1. Haloperidol: any dose and administration
2. Risperidone: any dose and administration

Types of outcome measures

We aim to divide outcomes into short term (less than six months), medium term (seven to 12 months) and long term (over one year).

Primary outcomes
1. Global state

1.1 Relapse (as defined in individual studies)

2. Mental state

2.1 Clinically important change in general mental state (as defined in individual studies)

3. Adverse effects

3.1 Movement disorders 3.1.1 Clinically important extrapyramidal symptoms (EPS)

4. Leaving the study early

4.1 For any reason

Secondary outcomes
1. Global state

1.1 Time to relapse 1.2 Clinically important change in global state ‐ as defined by individual studies 1.3 Any change in global state ‐ as defined by individual studies 1.4 Average endpoint/change score on global state scale

2. Mental state

2.1 Any change in general mental state ‐ as defined by individual studies 2.2 Average endpoint/change score on general mental state scale 2.3 Clinically important change in specific symptoms ‐ as defined by individual studies 2.4 Any change in specific symptoms ‐ as defined by individual studies 2.5 Average endpoint/change score on specific symptom scale

3. Adverse events/effects

3.1 Clinically important general adverse event/effects 3.2 At least one general adverse event/effects 3.3 Death ‐ suicide or other cause 3.4 Average endpoint/change score on general adverse event/effect scale 3.5 Specific adverse effects: 3.5.1 Anticholinergic 3.5.2 Cardiovascular 3.5.3 Central nervous system 3.5.4 Gastrointestinal 3.5.5 Endocrine 3.5.6 Haematology 3.5.7 Hepatitic 3.5.8 Metabolic 3.5.9 Movement disorders 3.5.10 Various other specific events/effects 3.5.11 Average endpoint/change score adverse effect scale

4. Leaving the study early

4.1 due to adverse event/effect 4.2 due to inefficacy of treatment

5. General functioning

5.1 Clinically important change in general functioning ‐ as defined by individual studies 5.2 Average endpoint/change score on general functioning scale 5.3 Clinically important change in specific aspects of functioning, such as social or life skills ‐ as defined by individual studies 5.4 Any change in specific aspects of functioning, such as social or life skills ‐ as defined by individual studies 5.5 Average endpoint/change score on specific aspects of functioning scale

6. Service outcomes

6.1 Hospitalisation 6.2 Time to hospitalisation 6.3 Clinically important engagement with services ‐ as defined by individual studies 6.4 Any engagement with services ‐ as defined by individual studies 6.5 Average endpoint/change score on engagement scale

7. Behaviour

7.1 Clinically important change in general behaviour ‐ as defined by individual studies 7.2 Any change in general behaviour ‐ as defined by individual studies 7.3 Average endpoint/change score on general behaviour scale 7.4 Clinically important change in specific aspects of behaviour ‐ as defined by individual studies 7.5 Any change in specific aspects of behaviour ‐ as defined by individual studies 7.6 Average endpoint/change score on specific aspects of behaviour scale

8. Satisfaction with treatment

8.1 Recipient of care satisfied with treatment 8.2 Recipient of care average/change score satisfaction scale 8.3 Carer satisfied with treatment 8.4 Carer average/change score satisfaction scale

9. Quality of life

9.1 Clinically important change in quality of life 9.2 Any change in quality of life 9.3 Average endpoint/change score quality of life scale 9.4 Cinically important change in specific aspects of quality of life 9.5 Any change in specific aspects of quality of life 9.6 Average endpoint/change score specific aspects of quality of life scale

10. Economic outcomes

10.1 Direct costs 10.2 Indirect costs

'Summary of findings' table

We will use the GRADE approach to interpret findings (Schünemann 2011) and will use GRADE profiler (GRADEPRO) to import data from RevMan 5 (Review Manager) to create 'Summary of findings' tables. These tables provide outcome‐specific information concerning the overall quality of evidence from each included study in the comparison, the magnitude of effect of the interventions examined, and the sum of available data on all outcomes we rated as important to patient‐care and decision making. We aim to select the following main outcomes for inclusion in the 'Summary of findings' tables.

  1. Global state: relapse ‐ as defined by individual studies

  2. Global state: clinically important change ‐ as defined by individual studies

  3. Adverse effects: Movement disorders ‐ clinically important extrapyramidal symptoms ‐ as defined by individual studies

  4. Adverse effects: Metabolic ‐ clinically important metabolic symptoms ‐ as defined by individual studies

  5. Leaving the study early: for any reason

  6. Service use: hospitalisation ‐ ‐ as defined by individual studies

  7. Economic costs: direct costs

We aim to use binary data, which are more clinically‐meaningful, in the 'Summary of findings' tables. If such data are not available we will use relevant continuous data but downgrade quality of evidence.

Search methods for identification of studies

Electronic searches

Cochrane Schizophrenia Group’s Study‐Based Register of Trials

The Information Specialist of the Cochrane Schizophrenia Group will search the register using the following search strategy:

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

In such a study‐based register, searching the major concept retrieves all the synonym and relevant studies because all the studies have already been organised based on their interventions and linked to the relevant topics.

This register is compiled by systematic searches of major resources (including AMED, BIOSIS, CINAHL, Embase, MEDLINE, PsycINFO, PubMed, and registries of clinical trials) and their monthly updates, handsearches, grey literature, and conference proceedings (see Group’s Module). 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 or awaiting assessment studies tables.

Data collection and analysis

Selection of studies

Review authors SR and RH will independently inspect citations from the searches and identify relevant abstracts. A random 20% sample will be independently re‐inspected by AR and AG to ensure reliability. Where disputes arise, the full report will be acquired for more detailed scrutiny. Full reports of the abstracts meeting the review criteria will be obtained and inspected by SR and RH. Again, a random 20% of reports will be re‐inspected by AR and AG. in order to ensure reliable selection. Where it is not possible to resolve disagreement by discussion, we will attempt to contact the authors of the study for clarification.

Data extraction and management

1. Extraction

Review authors SR and RH will extract data from all included studies. In addition, to ensure reliability, AR and AG will independently extract data from a random sample of these studies, comprising 10% of the total. Again, any disagreement will be discussed, decisions documented and, if necessary, authors of studies will be contacted for clarification. With remaining problems SR and RH will help clarify issues and these final decisions will be documented. We will attemp to extract data presented only in graphs and figures whenever possible, but will only include in analyses if two review authors independently have the same result. We will attempt to contact authors through an open‐ended request in order to obtain missing information or for clarification whenever necessary. If studies are multi‐centre, where possible, we will extract data relevant to each component centre separately.

2. Management
2.1 Forms

We will extract data onto standard, simple forms.

2.2 Scale‐derived data

We will include continuous data from rating scales only if: a) the psychometric properties of the measuring instrument have been described in a peer‐reviewed journal (Marshall 2000); and b) the measuring instrument has not been written or modified by one of the trialists for that particular trial. Ideally, the measuring instrument should either be i. a self‐report or ii. completed by an independent rater or relative (not the therapist). We realise that this is not often reported clearly, in Description of studies we will note if this is the case or not.

2.3 Endpoint versus change data

There are advantages of both endpoint and change data. Change data can remove a component of between‐person variability from the analysis. On the other hand, calculation of change needs two assessments (baseline and endpoint), which can be difficult in unstable and difficult to measure conditions such as schizophrenia. We have decided primarily to use endpoint data, and only use change data if the former are not available. Endpoint and change data will be combined in the analysis as we prefer to use mean differences (MD) rather than standardised mean differences (SMD) 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 aim to apply the following standards to relevant data before inclusion:

We will enter data from studies of at least 200 participants, for example, in the analysis irrespective of the following rules, because skewed data pose less of a problem in large studies. We will also enter change data as when continuous data are presented on a scale that includes a possibility of negative values (such as change data), it is difficult to tell whether data are skewed or not. We will present and enter change data into statistical analyses

For endpoint data:

(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 a skew and the study will be excluded. If this ratio is higher than one but below two, there is suggestion of skew. We will enter the study and test whether its inclusion or exclusion would change the results substantially. Finally, if the ratio is larger than two the study will be included, because skew is less likely (Altman 1996; Higgins 2011).

b) if a scale starts from a positive value (such as the Positive and Negative Syndrome Scale (PANSS), (Kay 1986)), which can have values from 30 to 210), the calculation described above will be modified to take the scale starting point into account. In these cases skew is present if 2 SD > (S‐S min), where S is the mean score and 'S min' is the minimum score.

2.5 Common measure

To facilitate comparison between trials, we intend to convert variables that can be reported in different metrics, such as days in hospital (mean days per year, per week or per month) to a common metric (e.g. mean days per month).

2.6 Conversion of continuous to binary

Where possible, efforts will be made to convert outcome measures to dichotomous data. This can be done by identifying cut‐off points on rating scales and dividing participants accordingly into 'clinically improved' or 'not clinically improved'. It is generally assumed that if there is a 50% reduction in a scale‐derived score such as the Brief Psychiatric Rating Scale (BPRS, Overall 1962) or the Positive and Negative Syndrome Scale (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 haloperidol. 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. This will be noted in the relevant graphs.

Assessment of risk of bias in included studies

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

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

The level of risk of bias will be noted in both the text of the review and in the 'Summary of findings' tables.

Measures of treatment effect

1. Binary data

For binary outcomes, we will calculate a standard estimation of the risk ratio (RR) and its 95% confidence interval (CI). It has been shown that RR is more intuitive (Boissel 1999) than odds ratios and that odds ratios tend to be interpreted as RR by clinicians (Deeks 2000). The number needed to treat for an additional beneficial outcome/harmful outcome (NNTB/NNTH) statistic with its confidence intervals is intuitively attractive to clinicians, but is problematic both in its accurate calculation in meta‐analyses and interpretation (Hutton 2009). For binary data presented in the 'Summary of findings' table/s, where possible, we will calculate illustrative comparative risks.

2. Continuous data

For continuous outcomes we will estimate mean difference (MD) between groups. If the scales are dissimilar, we will use standardised mean difference (SMD). However, if scales of very considerable similarity are used, we will presume there is a small difference in measurement, and we will calculate effect size and transform the effect back to the units of one or more of the specific instruments.

Unit of analysis issues

1. Cluster trials

Studies increasingly employ 'cluster randomisation' (such as randomisation by clinician or practice) but analysis and pooling of clustered data poses problems. Firstly, authors often fail to account for intra‐class correlation in clustered studies, leading to a 'unit of analysis' error (Divine 1992) whereby P values are spuriously low, confidence intervals unduly narrow and statistical significance overestimated. This causes type I errors (Bland 1997; Gulliford 1999).

Where clustering is not accounted for in primary studies, we will present data in a table, with a (*) symbol to indicate the presence of a probable unit of analysis error. In subsequent versions of this review, we will seek to contact first authors of studies to obtain intra‐class correlation coefficients (ICCs) for their clustered data and to adjust for this by using accepted methods (Gulliford 1999). Where clustering has been incorporated into the analysis of primary studies, we will present these data as if from a non‐cluster randomised study, but adjust for the clustering effect.

We have sought statistical advice and have been advised that the binary data as presented in a report should be divided by a 'design effect'. This is calculated using the mean number of participants per cluster (m) and the ICC [Design effect = 1+(m‐1)*ICC] (Donner 2002). If the ICC is not reported it will be assumed to be 0.1 (Ukoumunne 1999).

If cluster studies have been appropriately analysed taking into account ICCs and relevant data documented in the report, synthesis with other studies will be possible using the generic inverse variance technique.

2. Cross‐over trials

A major concern of cross‐over trials is the carry‐over effect. It occurs if an effect (e.g. pharmacological, physiological or psychological) of the treatment in the first phase is carried over to the second phase. As a consequence, on entry to the second phase the participants can differ systematically from their initial state despite a wash‐out phase. For the same reason cross‐over trials are not appropriate if the condition of interest is unstable (Elbourne 2002). As both effects are very likely in severe mental illness, we will only use data of the first phase of cross‐over studies.

3. Studies with multiple treatment groups

Where a study involves more than two treatment arms, if relevant, the additional treatment arms will be presented in comparisons. If data are binary, these will be simply added and combined within the two‐by‐two table. If data are continuous we will combine data following the formula in section 7.7.3.8  (Combining groups) of the Cochrane Handbook for Systematic reviews of Interventions (Higgins 2011 ). Where the additional treatment arms are not relevant, we will not use these data.

Dealing with missing data

1. Overall loss of credibility

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 down‐rating quality. Finally, we will also downgrade quality within the 'Summary of findings' tables should 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, with the exception of the outcome of death and adverse effects. For these outcomes, the rate of those who stay in the study ‐ in that particular arm of the trial ‐ will be used for those who did not. We will undertake a sensitivity analysis to test 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

In the case where attrition for a continuous outcome is between 0% and 50%, and data only from people who complete the study to that point are reported, we will reproduce these.

3.2 Standard deviations

If standard deviations (SDs) are not reported, we will first try to obtain the missing values from the authors. If not available, where there are missing measures of variance for continuous data, but an exact standard error (SE) and confidence intervals available for group means, and either P value or t value available for differences in mean, we can calculate them according to the rules described in the Cochrane Handbook for Systematic reviews of Interventions (Higgins 2011): When only the standard error (SE) is reported, SDs are calculated by the formula SD = SE * square root (n). Chapters 7.7.3 and 16.1.3 of the Cochrane Handbook for Systematic reviews of Interventions (Higgins 2011) present detailed formulae for estimating SDs from P values, t or F values, confidence intervals, ranges or other statistics. 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. We nevertheless will examine the validity of the imputations in a sensitivity analysis excluding imputed values.

3.3 Assumptions about participants who left the trials early or were lost to follow‐up

Various methods are available to account for participants who left the trials early or were lost to follow‐up. Some trials just present the results of study completers, others use the method of last observation carried forward (LOCF), while more recently, methods such as multiple imputation or mixed‐effects models for repeated measurements (MMRM) have become more of a standard. While the latter methods seem to somewhat better than LOCF (Leon 2006), we feel that the high percentage of participants leaving the studies early and differences in the reasons for leaving the studies early between groups is often the core problem in randomised schizophrenia trials. We will therefore not exclude studies based on the statistical approach used. However, we will preferably use the more sophisticated approaches e.g. MMRM or multiple‐imputation will be preferred to LOCF and completer analyses will only be presented if some kind of ITT data are not available at all. Moreover, we will address this issue in the item 'incomplete outcome data' of the 'Risk of bias' tool.

Assessment of heterogeneity

1. Clinical heterogeneity

We will consider all included studies initially, without seeing comparison data, to judge clinical heterogeneity. We will simply inspect all studies for clearly outlying people or situations which we had not predicted would arise. When such situations or participant groups arise, these will be fully discussed.

2. Methodological heterogeneity

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

3. Statistical heterogeneity
3.1 Visual inspection

We will visually inspect graphs to investigate the possibility of statistical heterogeneity.

3.2 Employing the I2 statistic

Heterogeneity between studies will be investigated by considering the I2 method alongside the Chi2 P value. The I2 provides an estimate of the percentage of inconsistency thought to be due to chance (Higgins 2003). The importance of the observed value of I2 depends on i. magnitude and direction of effects and ii. strength of evidence for heterogeneity (e.g. P value from Chi2  test, or a confidence interval for I2). An I2 estimate greater than or equal to around 50% accompanied by a statistically significant Chi2 statistic, will be interpreted as evidence of substantial levels of heterogeneity (Section 9.5.2 ‐ 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

1. Protocol versus full study

Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results. These are described in section 10.1 of the Cochrane Handbook for Systematic reviews of Interventions (Sterne 2011). We will try to locate protocols of included randomised trials. If the protocol is available, outcomes in the protocol and in the published report will be compared. If the protocol is not available, outcomes listed in the methods section of the trial report will be compared with actually reported results.

2. Funnel plot

Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997). These are again described in Section 10 of the Cochrane Handbook for Systematic reviews of Interventions (Sterne 2011). We are aware that funnel plots may be useful in investigating reporting biases but are of limited power to detect small‐study effects. We will not use funnel plots for outcomes where there are 10 or fewer studies, or where all studies are of similar sizes. In other cases, where funnel plots are possible, we will seek statistical advice in their interpretation.

Data synthesis

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

Subgroup analysis and investigation of heterogeneity

1. Subgroup analyses
1.1 Primary outcomes

For primary outcomes we aim to conduct subgroup analyses for:

1. people whose illnesses are described as 'treatment resistant' compared with those whose illnesses are not designated as such; 2. first episode of schizophrenia compared with people who had longer duration of the illness.

2. Investigation of heterogeneity

If inconsistency is high, this will be reported. First, we will investigate whether data have been entered correctly. Second, if data are correct, we will visually inspect the graph and remove outlying studies to see if homogeneity is restored. For this review, we decided that should this occur with data contributing to the summary finding of no more than around 10% of the total weighting, data will be presented. If not, data will not be pooled and issues will be discussed. We know of no supporting research for this 10% cut‐off but are investigating use of prediction intervals as an alternative to this unsatisfactory state.

When unanticipated clinical or methodological heterogeneity are obvious, we will simply state hypotheses regarding these for future reviews or versions of this review. We do not anticipate undertaking analyses relating to these.

Sensitivity analysis

1. Implication of randomisation

We aim to include trials in a sensitivity analysis if they are described in some way as to imply randomisation. For the primary outcomes if their inclusion does not result in a substantive difference, they will remain in the analyses. If their inclusion does result in important clinically significant, but not necessarily statistically significant differences, we will not add the data from these lower quality studies to the results of the better trials, but will present such data within a subcategory.

2. Assumptions for lost binary data

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

Where assumptions have to be made regarding missing SDs data (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumption/s and when we use data only from people who complete the study to that point. We will undertake a sensitivity analysis to test how prone results are to change when completer‐only data only are compared to the imputed data using the above assumption. If there is a substantial difference, we will report results and discuss them but will continue to employ our assumption.

3. Risk of bias

We will analyse the effects of excluding trials that are judged to be at high risk of bias across one or more of the domains of randomisation (implied as randomised with no further details available) allocation concealment, blinding and outcome reporting for the meta‐analysis of the primary outcome. If the exclusion of trials at high risk of bias does not substantially alter the direction of effect or the precision of the effect estimates, then data from these trials will be included in the analysis.

4. Imputed values

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

If substantial differences are noted in the direction or precision of effect estimates in any of the sensitivity analyses listed above, we will not pool data from the excluded trials with the other trials contributing to the outcome, but will present them separately.

5. Fixed and random effects

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

Acknowledgements

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

The search terms were developed by the Information Specialist of the Cochrane Schizophrenia Group and the contact author of this protocol.

We would like to thank the staff at Cochrane Schizophrenia for their help and support in developing and editing this protocol and Qijing Bo for providing peer review feedback.

Appendices

Appendix 1. Previous search for risperidone versus typical antipsychotics

1. The Cochrane Schizophrenia Group's Register of Randomised Controlled Trials (July 2001) was searched using the phrase:

[risperidone or risperdal or 9‐OH‐risperidone or #42 = 142]

(#42 is the field in this Register that contains a code for each intervention.)

2. Searches of commercial databases Biological Abstracts (1980‐2001), The Cochrane Library (Issue 1, Feburary 2001), EMBASE (1980‐2001), PsycLIT (1974‐2001) and MEDLINE (1966‐2001) were searched using the Cochrane Schizophrenia Group's phrase for randomised controlled trials and schizophrenia (see Group search strategy) combined with the phrase:

[and (risperidone or risperdal or 9‐OH‐risperidone)]

Appendix 2. Methods used in previous review of risperidone versus typical

1. Study selection CJ inspected all reports of studies identified as above. Randomly selected samples of 10% of all reports were re‐inspected by RH in order to allow selection to be reliable. Where disagreement occurred this was resolved by discussion, and where there was still doubt the full article was acquired for further inspection. Once the full articles were obtained EK and FS independently decided whether the studies met the review criteria. EK was blinded to the names of the authors, institutions and journal of publication. Where disagreement occurred this was resolved by discussion and when this was not possible further information was sought. These trials were added to the list of those awaiting assessment pending acquisition of further information. For the 2001 update, the reviewer (CJ) inspected all reports identified in the new search. Randomly selected samples of 10% of all new reports were re‐inspected by RH. Again once full reports were obtained, CJ and RH resolved disputes over whether studies meet inclusion criteria by discussion.

2. Quality assessment Trials were allocated to three quality categories, as described in the Cochrane Collaboration Handbook (Joy 2001) by each reviewer. When disputes arose as to which category a trial was allocated to, resolution was attempted by discussion. When this was not possible and further information was necessary, data were not entered and the trial was allocated to the list of those awaiting assessment. Only trials in Category A or B were included in the review.

3. Assessing the presence of publication bias Data from all included trials were entered into a funnel graph (trial effect versus trial size or 'precision') in an attempt to investigate the likelihood of overt publication bias. Where only 3‐4 studies reported an outcome or there was little variety in sample size (or precision estimate) between studies ‐ funnel plot analysis was not appropriate. There is currently no consensus about the validity of formal statistical tests to investigate funnel plot asymmetry, one test, proposed by Egger 1997 has been subject to criticism (Irwig 1998). Further versions of this review will include such tests when their validity has been proven. 4. Data extraction Data from selected trials were independently extracted by EK, FS, RH and SG. When disputes arose resolution was attempted by discussion. When this was not possible and further information was necessary to resolve the dilemma, data were not entered and this trial was added to the list of those awaiting assessment. For the 2001 update, CJ extracted data, a random sample of extracted data were independently checked by SG.

5. Data synthesis Data types: Outcomes were assessed using continuous (for example changes on a behaviour scale), categorical (for example, one of three categories on a behaviour scale, such a 'little change', 'moderate change' or 'much change') or dichotomous measures (for example, either 'no important changes' or 'important changes' in a persons behaviour). Currently RevMan does not support categorical data so they were presented only in the text of the review.

5.1 Dichotomous data Where possible, efforts were made to convert outcome measures to dichotomous data; this may be done by identifying cut off points on rating scales and dividing subjects accordingly into 'clinically improved' or 'not clinically improved'. If the authors of a study had used a designated cut off point for determining clinical effectiveness this was used by the reviewers where appropriate. For dichotomous outcomes, a random effects Relative Risk (RR) with the 95% confidence interval (CI) around this was estimated. As a summary measure of effectiveness, the number needed to treat statistic (NNT) was also calculated.

5.2 Continuous data 5.2.1 Scale derived data A wide range of rating scales is available to measure outcomes in mental health trials. These scales vary in quality and many are questionably validated, or even ad hoc. It is generally accepted that measuring instruments should have the properties of reliability (the extent to which a test effectively measures anything at all) and validity (the extent to which a test measures that which it is supposed to measure). Before publication of an instrument, most scientific journals insist that reliability and validity be demonstrated to the satisfaction of referees. It was therefore decided, as a minimum standard, not to include any data from a rating scale in this review unless its properties had been published in a peer‐reviewed journal. In addition, the following minimum standards for rating scales were set: the rating scale should either be a self‐report, or completed by an independent rater or relative. More stringent standards for instruments may be set in future editions of this review.

Whenever possible we took the opportunity to make direct comparisons between trials that used the same measurement instrument to quantify specific outcomes. Where continuous data was presented from different scales rating the same effect, both sets of data were presented and the general direction of effect inspected.

5.2.2 Normal data Data on outcomes in neuroleptic trials are often not normally distributed. To avoid the pitfall of applying parametric tests to non‐parametric data the following standards were applied to data derived from continuous measures of end point 'state'. The criteria were used before inclusion: i. Standard deviations and means were reported in the paper or were obtainable from the authors; ii. The standard deviation (SD), when multiplied by 2 was less than the mean (as otherwise the mean was unlikely to be an appropriate measure of the centre of the distribution) (Altman 1996). Data that did not meet the first or second standard were not entered into RevMan software for analysis, but were reported in the text of the 'Results' section.

For continuous mean change data (endpoint minus baseline) the situation is even more problematic. In the absence of individual patient data it is impossible to know if change data is skewed. The RevMan meta‐analyses of continuous data are based on the assumption that the data are, at least to a reasonable degree, normally distributed. It is quite feasible that change data is skewed but, after consulting the ALLSTAT 1988 electronic statistics mailing list (http://www.stats.gla.ac.uk/allstat/index.html), it was entered into RevMan in order to summarise the available information. In doing this it is assumed that either data were not skewed or that the analyses within RevMan could cope with the unknown degree of skew. Without individual trial data it is not possible to formally check this assumption.

5.2.3 Summary statistic We estimated a weighted mean difference, random effects model (WMD) for continuous outcomes.

5.3 Intention to treat analysis We hoped we would produce a review of risperidone that was pragmatic and answered the question as to whether, on average, those who take this new drug do better or worse than if they had taken none, an old drug or a similar new medication. The purpose of this review was not to ask the question "does risperidone work with people who are very compliant with medication and complete the course?" as this greatly limits the generalisability (external validity) of the findings. The reviewers therefore undertook an intention to treat analysis assuming that those who dropped out ‐ from whatever group ‐ had an unfavourable outcome. The reviewers investigated the sensitivity of the principle dichotomous outcomes to this assumption. For continuous, summary data it is not possible to include such an assumption so non‐intention to treat data were presented. Such data, however, were excluded if studies had more than 50% of the people lost to follow‐up.

5.4 Cluster trials Studies increasingly employ 'cluster randomisation' (such as randomisation by clinician or practice) but analysis and pooling of clustered data poses problems: Firstly, authors often fail to account for intra class correlation in clustered studies, leading to a 'unit of analysis' error (Divine 1992) ‐ whereby p values are spuriously low, confidence intervals unduly narrow and statistical significance overestimated ‐ causing type I errors (Bland 1997, Gulliford 1999). Secondly, RevMan does not currently support meta‐analytic pooling of clustered dichotomous data, even when these are correctly analysed by the authors of primary studies, since the 'design effect' (a statistical correction for clustering) cannot be incorporated.

Where clustering was not accounted for in primary studies, we presented the data in a table, with an (*) symbol ‐ to indicate the presence of a probable unit of analysis error. In subsequent versions of this review we will seek to contact first authors of studies to seek intra‐class correlation co‐efficients of their clustered data and to adjust for this using accepted methods (Gulliford 1999). If clustering had been incorporated into the analysis of primary studies, we also presented these data in a table. No further secondary analysis (including meta‐analytic pooling) will be attempted until there is consensus on the best methods of doing so, and until RevMan, or any other software, allows this. A Cochrane Statistical Methods Workgroup is currently addressing this issue. In the interim, individual studies were very crudely classified as positive or negative, according to whether a statistically significant result (p<0.05) was obtained for the outcome in question, using an analytic method which allowed for clustering.

5.5 Test for heterogeneity A Chi‐square test was used, as well as visual inspection of graphs, to investigate the possibility of heterogeneity. A significance level less than 0.10 was interpreted as evidence of heterogeneity. If heterogeneity was found, the studies responsible for heterogeneity were not added to the main body of homogeneous trials, but summated and presented separately and reasons for heterogeneity investigated.

6. Addressing publication bias Data from all included studies were entered into a funnel graph (trial effect against trial size) in an attempt to investigate the likelihood of overt publication bias (Egger 1997).

7. Sensitivity analyses The effect of including studies with high attrition rates was analysed in a sensitivity analysis.

8. General Where possible, reviewers entered data in such a way that the area to the left of the line of no effect indicated a favourable outcome for risperidone.

Contributions of authors

Sujoy Ray‐ development and writing of protocol

Amita Ray ‐ help with preparation of protocol.

Arun Gopi ‐ help with preparation of protocol.

Robert Hunter ‐ advice, help with preparation of protocol.

Sources of support

Internal sources

  • St. John's Medical College and Hospital, Bangalore, India.

    Employs lead author Sujoy Ray.

  • Greater Glasgow Health Board, Glasgow, UK.

    Employs review author Robert Hunter.

  • DM Wayanad Institute of Medical Sciences, Wayanad, India.

    Employs review authors Amita Ray and Arun Gopi.

External sources

  • No sources of support supplied

Declarations of interest

Sujoy Ray: none known.

Amita Ray: none known.

Arun Gopi: none known.

Robert Hunter: none known.

New

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