Benperidol for schizophrenia

Types of studies

We included all relevant randomised controlled trials. We excluded studies with inappropriate randomisation methods such as alternate allocation or randomisation by day of the week, date of birth etc (Higgins 2008). Randomised cross‐over studies were eligible but only 
 data up to the point of first cross‐over because of the instability of the problem behaviours and the likely carryover 
 effects of all treatments (Elbourne 2002, see below).

Types of participants

We included people with schizophrenia, diagnosed by any criteria. We also included those with 'serious/chronic mental illness' or 'psychotic illness'. If possible we excluded those with dementia, depression and problems primarily associated with substance misuse.

Types of interventions

1. Benperidol: any dose, route and pattern of administration against one or more of the following: 
 2. Placebo or no treatment 
 3. Other antipsychotic drugs: any dose or pattern of administration.

Types of outcome measures

All outcomes were reported for the short term (up to 12 weeks), medium term (13‐26 weeks), and long term (more than 26 weeks).

Electronic searches

We searched the Cochrane Schizophrenia Group Register (March 23rd 2009) with the phrase :

[(*benperido* or *benzperidol* or *benzoperidol* or *frenactyl* or *glianimon* or *phenactil* or *frenactil* or *anquil* or *Psichoben* or *CB‐8089* or *cb 8089* or *8089 CB* or *McN‐JR‐4584* or *mcn jr 4584* or *R‐4584* or *r 4584 in title, abstract, index terms of REFERENCE) and  (benperido* or benzperidol* or benzoperidol* or frenactyl* or glianimon* or phenactil* or frenactil* or anquil* or Psichoben* or CB‐8089* or cb 8089* or 8089 CB* or McN‐JR‐4584* or mcn jr 4584* or R‐4584* or r 4584* in interventions of STUDY)].

This register is compiled by systematic searches of major databases, hand searches and conference proceedings (see group module).

The search strategies of the previous versions of this review are described in Appendix 1.

Searching other resources

1. Reference searching 
 We inspected references of all identified studies for more studies.

2. Personal contact 
 We contacted the first author of each included study for further information regarding unpublished trials.

3. Drug companies 
 We contacted the manufacturers of proprietary benperidol (Bayer AG, Germany) for additional data (relates only to the first version of this review).

Selection of studies

Two review authors independently inspected all citations of studies identified by the search. We resolved any disagreement by discussion, but if there was still doubt, we acquired the full article for further inspection. Once the full articles were obtained author CS decided whether they met review criteria and this was checked by author SL. Once again, we resolved any disagreement by discussion and if doubt remained, the study was put on the list of those awaiting assessment.

Data extraction and management

1. Data Extraction 
 CS and SL independently extracted data from included studies. Any disagreement was discussed, decisions documented and, if necessary, authors of studies were contacted for clarification. When this was not possible and further information was necessary to resolve the dilemma, we did not enter data and added the trial to the list of those awaiting assessment. 
 2. Management 
 We extracted the data onto standard, simple forms. Where possible, data were entered into RevMan in such a way that the area to the left of the 'line of no effect' indicates a 'favourable' outcome for benperidol. Where this was not possible, for example for scales that calculate higher scores = improvement, graphs in RevMan analyses were labelled accordingly so that the direction of effects were clear.

Assessment of risk of bias in included studies

Again working independently, two authors assessed risk of bias using the tool described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2008). This tool encourages consideration of how the sequence was generated, how allocation was concealed, the integrity of blinding at outcome, the completeness of outcome data, selective reporting and other biases. We would not have included studies where sequence generation was at high risk of bias and where allocation was clearly not concealed.

If disputes arise as to which category a trial has to be allocated, again, resolution was made by discussion.

Measures of treatment effect

1. Data types 
 Outcomes are assessed using continuous (for example, average changes on a behaviour scale), categorical (for example, one of three categories on a behaviour scale, such as 'little change', 'moderate change' or 'much change') or dichotomous measures (for example, either 'no important changes' or 'important changes' in a person's behaviour). Currently RevMan software does not support categorical data so we only presented these in the text of the review.

2. Dichotomous/binary data 
 2.1 Defining cut‐offs 
 Where the original authors of the studies gave outcomes such as 'clinically improved' or 'not clinically improved', based on their clinical judgement, predetermined criteria, or any scale, we recorded this in RevMan. If data were from a rater not clearly stated to be independent, then we included it provided it did not change the results, otherwise it was presented separately with a label 'prone to bias'. Where possible, we converted relevant categorical or continuous outcome measures to dichotomous data by identifying cut off points on rating scales and dividing subjects into groups accordingly. This was with the cut‐off points 'moderate or severe impairment' for end of study data or 'no better or worse' for change data.

For example the Brief Psychiatric Rating Scale (BPRS ‐ Overall 1962) and the Positive and Negative Syndrome Scale (Kay 1986) are frequently used as a measure of change of symptoms in studies. We defined a 50% change on these particular scales as clinically important, although we recognised that for many people, especially those with chronic or severe illnesses, a less rigorous definition of important improvement (for example 25% on the BPRS/PANSS) would be equally valid (Leucht 2005a, Leucht 2005b). Where individual patient data were available, we used the 50% cut‐off for the definition in the case of non‐chronically ill people, and 25% for those with chronic illness.

2.2 Intention‐to‐treat analysis 
 The review presents an intention‐to‐treat analysis. Provided that more than 50% of people in short and medium‐term studies and 40% in long‐term studies completed the trial, we counted everyone allocated to the intervention, whether or not they completed follow up. We assumed that those who left the study early had no change in their outcome.

2.3 Effect size 
 The review uses the relative risk (RR) and 95% confidence interval (CI). It has been shown that RR is more intuitive (Boissel 1999) and that odds ratios tend to be interpreted as RR by clinicians (Deeks 2000). This misinterpretation then leads to an overestimate of the impression of the effect. We did inspect data, however, to see if analysis using a Mantel‐Haenszel odds ratio made a substantive difference. Where possible, we estimated the number needed to treat (NNT) using an on‐line calculator (http://www.mango3d.cwc.net/vsx.htm).

3. Continuous data 
 3.1 Intention‐to‐treat versus completer analyses 
 In the case of continuous data we assumed that in many cases an intention‐to‐treat analysis would not be available and presented a completer analysis.

3.2 Rating scales 
 A wide range of instruments is available to measure mental health outcomes. These instruments vary in quality and many are not valid, or even ad hoc. For outcome instruments it is necessary to set minimum standards. We only included continuous data from rating scales if the measuring instrument had been described in a peer‐reviewed journal (Marshall 2000), the instrument was either a self report or completed by an independent rater or relative (not the therapist), and the instrument could be considered a global assessment of an area of functioning. However, as it was expected that therapists would frequently also be the rater, we commented on such data as 'prone to bias'.

3.3 Skewed data 
 Mental health continuous data is often not "normally" distributed. To avoid the pitfall of applying parametric tests to non‐parametric data the following standards were applied to all data before inclusion: (i) standard deviations and means were reported in the paper or were obtained from the authors; (ii) if the data were finite number zero, for example 0‐100, when the standard deviation was multiplied by two, the result should be less than the mean, otherwise the mean is unlikely to be an appropriate measure of the centre of the distribution (Altman 1996). (III) 
 if a scale starts from a positive value (such as PANSS 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 2SD>(S‐S min), where S is the mean score and S min is the minimum score. Endpoint scores on scales often have a finite start and end point and these rules can be applied. When continuous data are presented on a scale which includes a possibility of negative values (such as change data), it is difficult to tell whether data are skewed or not. Skewed data from studies of less than 200 participants were entered in additional tables rather than into an analysis. Skewed data pose less of a problem when looking at means if the sample size is large and were entered into syntheses.

3.4 Endpoint versus change data 
 Endpoint scale‐derived data are finite, ranging from one score to another. Change data are more problematic and for it the rule described above does not hold. Although most change scores are likely to be skewed, this cannot be proven so they were presented in MetaView. Where possible we presented endpoint data, and if both endpoint and change data were available for the same outcomes, then we reported only the former.

3.5 Summary statistic 
 For continuous outcomes, we estimated a weighted mean difference (MD) between groups.

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 intraclass 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 can cause type I errors (Bland 1997, Gulliford 1999).

Where clustering was not accounted for in primary studies, we presented the 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 intraclass correlation coefficients of their clustered data and to adjust for these using accepted methods (Gulliford 1999). Where clustering has been incorporated into the analysis of primary studies, we will also present these data as if from a non‐cluster randomised study, but adjusted 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 intraclass correlation coefficient (ICC) [Design effect = 1+ (m‐1)*ICC] (Donner 2002). If the ICC was not reported it was assumed to be 0.1 (Ukoumunne 1999).

If cluster studies had been appropriately analysed taking into account intraclass correlation coefficients and relevant data documented in the report, synthesis with other studies would have been 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 schizophrenia, randomised cross‐over studies were eligible but only data up to the point of first cross‐over.

3. Studies with multiple treatment groups 
 Where a study involved more than two treatment arms, if relevant, the additional treatment arms were presented in comparisons. Where the additional treatment arms were not relevant, these data were not reproduced.

Dealing with missing data

At some degree of loss to follow‐up data must lose credibility (Xia 2007). With the exception of the outcome of leaving the study early, we did not include trial outcomes of studies if more than 50% of people in short and medium‐term studies, or 60% of people in long‐term studies, were not reported in the final analysis. We felt that with such a great degree of attrition, assumptions would have to be made that would threaten the validity of any findings.

Assessment of heterogeneity

1. Clinical heterogeneity 
 Firstly, we would have considered all the included studies within any comparison to judge clinical heterogeneity.

2. Statistical 
 2.1 Visual inspection 
 We would have used visual inspection of graphs to investigate the possibility of statistical heterogeneity.

2.2 Employing the I‐squared statistic 
 The I‐squared statistic provides an estimate of the percentage of variability due to heterogeneity rather than chance alone. If the I‐squared estimate had been greater than or equal to 50%, we would have interpreted this as indicating the presence of high levels of heterogeneity (Higgins 2003).

Assessment of reporting biases

Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997). We are aware that funnel plots may be useful in investigating reporting biases but are of limited power to detect small‐study effects. We did not use funnel plots for outcomes where there were ten or fewer studies, or where all studies were of similar sizes.

Data synthesis

Where possible we employed a random‐effects model for analyses (Der‐Simonian 1986). We understand that there is no closed argument for preference for use of fixed or random‐effects models. The random‐effects method incorporates an assumption that the different studies are estimating different, yet related, intervention effects. This does seem true to us and the random‐effects model takes into account differences between studies even if there is no statistically significant heterogeneity. Therefore, the random‐effects model is usually more conservative in terms of statistical significance, although as a disadvantage it puts added weight onto smaller studies which can either inflate or deflate the effect size. We examined in a secondary analysis whether using a fixed‐model markedly changed the results.

Subgroup analysis and investigation of heterogeneity

1. Subgroup analyses: 
 Subgroup analyses were not planned.

2. Investigation of heterogeneity: 
 If data are clearly heterogeneous we checked that data are correctly extracted and entered and that we had made no unit of analysis errors. If the high levels of heterogeneity remained we looked whether differences in the methods of the studies explained the discrepancies. If such differences were found, the studies were not pooled, but rather presented separately. If such differences were not found, we pooled the studies using a random effects model.

Sensitivity analysis

For binary data, results for intention‐to‐treat analysis were compared with those using completer only data. If analyses using completer data did result in a substantive change in the estimate of effect we discussed this in the 'Discussion' section.

Results of the search

Our initial search in the version of this review yielded 35 citations, but only ten of these were publications about benperidol. We had to exclude nine of these.

The update search in November 2004 yielded 39 citations (in part overlapping with the initial search). Thirty‐seven citations were clearly not relevant to our review. The search identified only one study not found by the previous search (Digo 1967 ‐ excluded) and one further reference of the already excluded Seiler 1994 study.

The most recent update search in March 2009 yielded 241 references (from 201 studies, in part overlapping with the initial search). Inspection of the abstracts made it clear that none of them met the inclusion criteria close enough to be reported in this review.

Included studies

We identified only one unpublished manuscript (Eckmann 1984) concerning a small (n=40), 30‐day, randomised controlled, double‐blind study.

1. Participants 
 People in this study were acutely ill, with paranoid schizophrenia (ICD‐9). All participants were in a hospital setting, and most were men in their mid‐thirties.

2. Interventions 
 Oral benperidol (6 to 12 mg/day) was compared with oral perphenazine (12 to 24 mg/day). These doses are seen in routine clinical care.

3. Outcomes 
 At the end of the trial, raters were asked to judge the 'global effect of treatment' according to the criteria: very much improved, improved, moderately improved, unchanged and worsened. We have made these ratings binary (see below).

A variety of outcome scales were used to monitor mental state (BPRS, AMDP), behaviour (NOSIE) and movement disorders (SAS). As standard deviations were not presented, all data from these scales were impossible to include. We have therefore not shown further details of these scales. The only useable outcomes in this review were leaving the study early and global state which was not measured by a scale. Results on all other prespecified outcomes for the review were not available.

Excluded studies

There were ten excluded studies. Five excluded studies were not randomised, three did not include people with schizophrenia and two studies compared different doses of benperidol, but did not include a placebo group or a group receiving a comparator antipsychotic (Nedopil 1985, Seiler 1994).

Allocation

The only included study (Eckmann 1984) did not describe the method used to generate random allocation. Although no differences in baseline descriptions of the comparator groups were found, the readers were given little assurance that bias was minimised during the allocation procedure.

Blinding

Although Eckmann 1984 did state that the study was double‐blind, the report did not describe the precautions taken to minimise observation bias. Both medications were administered in liquid form, but whether colour, taste etc. of the liquids were the same is unclear.

Incomplete outcome data

No data on losses to follow up were given so we had to assume that no participant had left the study early.

Selective reporting

The study is to date only available as an unpublished manuscript. Continuous scale‐derived data were very poorly reported. Explicit statements regarding the denominator or standard deviation were not present. Often data were only presented as significance tests or within graphs which made them impossible to include in this review. We therefore do not describe the scales in detail in this review.

Other potential sources of bias

We did not find other clear sources of bias.