Sertindole versus other atypical antipsychotics for schizophrenia
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To review the effects of sertindole compared with other atypical antipsychotics for people with schizophrenia and schizophrenia‐like psychosis.
Background
Conventional antipsychotic drugs such as chlorpromazine and haloperidol have traditionally been used as first line antipsychotics for people with schizophrenia (Kane 1993). The reintroduction of clozapine in the United States of America and a finding that clozapine was more efficacious and associated with fewer movement disorders than chlorpromazine (Kane 1988) has boosted the development of so‐called "atypical" or new (second) generation antipsychotics (NGA). There is no good definition of what an "atypical" or new generation antipsychotic is, but they were initially said to differ from typical antipsychotics in that they do not cause movement disorders (catalepsy) in rats at clinically effective doses (Arnt 1998). The terms "new" or "second generation" antipsychotics are not much better, because clozapine is a very old drug. According to treatment guidelines (APA 2004, Gaebel 2006) new generation antipsychotics include drugs such as amisulpride, aripiprazole, clozapine, olanzapine, quetiapine, risperidone sertindole, ziprasidone and zotepine, although it is unclear whether some old and cheap compounds such as sulpiride or perazine have similar properties (Möller 2000). The new generation antipsychotics raised major hopes of superior effects in a number of areas such as compliance, cognitive functioning, negative symptoms, movement disorders, quality of life and the treatment of people with treatment resistant schizophrenia.
The debate as to how far the NGA improve these outcomes compared to conventional antipsychotics continues (Duggan 2005, El‐Sayeh 2006) and the results from recent studies were sobering (Liebermann 2005, Jones 2006). Nevertheless, in some parts of the world, especially in the highly industrialized countries, new generation antipsychotics have become the mainstay of treatment. The new generation antipsychotics also differ in terms of their costs: while amisulpride is already generic, risperidone will be generic in many countries in 2008. Therefore the question as to whether they differ from each other in their clinical effects becomes increasingly important. In this review we aim to summarise evidence from randomised controlled trials that compared sertindole with other new generation antipsychotics.
Technical background
Sertindole is a phenylindole derivative (1‐[2‐[4‐[5‐chloro‐1‐(4‐fluorophenyl)‐1H‐indol‐3‐yl]‐1‐piperidinyl] ethyl‐2‐imidazolidinone) which is manufactured by Lundbeck Ltd and is sold as Serdolect or Serlect (in several European countries) in 4 mg, 12 mg, 16 mg and 20 mg tablets. It is a long acting 5‐HT2 / alpha1 antagonist and a very mild D2 antagonist. (Lewis 2005). More than some other atypical antipsychotics sertindole may cause QT‐ prolongation and ventricular tachycardia. Due to this sertindole was taken from the market in 1998. Since 2002 it was again available for patient treatment in clinical studies, since December 2005 it became available again in some European countries: Germany, Estonia, Finland, Hungary, Denmark, Czech Republic, Spain, Slovakia and Greece, (Turkey planned 12/06) under special safety conditions; for example: no first choice treatment, not for emergency treatment, ECG observation (Lundbeck 2006).
Objectives
To review the effects of sertindole compared with other atypical antipsychotics for people with schizophrenia and schizophrenia‐like psychosis.
Methods
Criteria for considering studies for this review
Types of studies
We included randomised controlled trials which were at least single‐blind (blind raters). Where a trial was described as 'double‐blind', but it was only implied that the study was randomised, we included these trials in a sensitivity analysis. If there was no substantive difference within primary outcomes (see types of outcome measures) when these 'implied randomisation' studies were added, then we included these in the final analysis. If there was a substantive difference, we only used clearly randomised trials and described the results of the sensitivity analysis in the text. We excluded quasi‐randomised studies, such as those allocating by using alternate days of the week.
Types of participants
We included people with schizophrenia and other types of schizophrenia‐like psychosis (e.g. schizophreniform and schizoaffective disorders), irrespective of the diagnostic criteria used. There is no clear evidence that the schizophrenia‐like psychoses are caused by fundamentally different disease processes or require different treatment approaches (Carpenter 1994).
Types of interventions
1. Sertindole: any oral form of application, any dose
2. Other "atypical" antipsychotic drugs: amisulpride, aripiprazole, clozapine, olanzapine, quetiapine, risperidone, ziprasidone, zotepine: any oral form of application, any dose.
Types of outcome measures
We grouped outcomes into the short term (up to 12 weeks), medium term (13‐26 weeks) and long term (over 26 weeks).
Primary outcomes
We chose "no clinically important response as defined by the individual studies" as the primary outcome.
Secondary outcomes
1. Leaving the studies early (any reason, adverse events, inefficacy of treatment)
2. Global state
2.1 No clinically important change in global state (as defined by individual studies)
2.2 Relapse (as defined by the individual studies)
3. Mental state (with particular reference to the positive and negative symptoms of schizophrenia)
3.1 No clinically important change in general mental state score
3.2 Average endpoint general mental state score
3.3 Average change in general mental state score
3.4 No clinically important change in specific symptoms (positive symptoms of schizophrenia, negative symptoms of schizophrenia)
3.5 Average endpoint specific symptom score
3.6 Average change in specific symptom score
4. General functioning
4.1 No clinically important change in general functioning
4.2 Average endpoint general functioning score
4.3 Average change in general functioning score
5. Quality of life/satisfaction with treatment
5.1 No clinically important change in general quality of life
5.2 Average endpoint general quality of life score
5.3 Average change in general quality of life score
6. Cognitive functioning
6.1 No clinically important change in overall cognitive functioning
6.2 Average endpoint of overall cognitive functioning score
6.3 Average change of overall cognitive functioning score
7. Service use
7.1 Number of patients hospitalised
8. Adverse effects
8.1 Number of participants with at least one adverse effect
8.2 Clinically important specific adverse effects (cardiac effects, death, movement disorders, prolactin increase and associated effects, sedation, seizures, weight gain, effects on white blood cell count)
8.3 Average endpoint in specific adverse effects
8.4 Average change in specific adverse effects
Search methods for identification of studies
Electronic searches
We searched the Cochrane Schizophrenia Groups Register (April 2007) using the phrase:
[((sertindol* AND (amisulprid* OR aripiprazol* OR clozapin* OR olanzapin* OR risperidon* OR quetiapin* OR ziprasidon* OR zotepin*)) in title, abstract or index terms of REFERENCE) or ((sertindol* AND (amisulprid* OR aripiprazol* OR clozapin* OR olanzapin* OR risperidon* OR quetiapin* OR ziprasidon* OR zotepin*)) in interventions of STUDY)]
This register is compiled by systematic searches of major database, hand searches and conference proceedings (see Group Module).
Searching other resources
1. Reference searching
We inspected the reference of all identified studies for more trials.
2. Personal contact
We contacted the first author of each included study for missing information.
3. Drug companies
We contacted the manufacturers of all atypical antipsychotics included for additional data.
Data collection and analysis
[For definitions of terms used in this, and other sections, please refer to the Glossary]
1. Selection of trials
We independently inspected all reports. We resolved any disagreement by discussion, and where there was still doubt, we acquired the full article for further inspection. Once the full articles were obtained, we independently decided whether the studies met the review criteria. If disagreement could not be resolved by discussion, we sought further information and these trials were added to the list of those awaiting assessment.
2. Assessment of methodological quality
We assessed the methodological quality of included trials in this review using the criteria described in the Cochrane Handbook (Higgins 2005). The former is based on the evidence of a strong relationship between allocation concealment and direction of effect (Schulz 1995). The categories are defined below:
A. Low risk of bias (adequate allocation concealment)
B. Moderate risk of bias (some doubt about the results)
C. High risk of bias (inadequate allocation concealment). For the purpose of the analysis in this review, trials were included if they met the Cochrane Handbook criteria A or B.
3. Data collection
We independently extracted data from selected trials. When disputes arose we attempted to resolve these by discussion. 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.
4. Data synthesis
4.1 Data types
We assessed outcomes using continuous (for example 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 (for example, either "no important changes or "important change" in a person's behaviour) measures. Currently RevMan does not support categorical data so we were unable to analyse this.
4.2 Incomplete data
Although high rates of premature discontinuation are a major problem in this field, we felt that it is unclear which degree of attrition leads to a high degree of bias. We, therefore, did not exclude trials on the basis of the percentage of participants completing them. However we addressed the drop‐out problem in all parts of the review, including the abstract. For this purpose we calculated, presented and commented on frequency statistics (overall rates of leaving the studies early in all studies and comparators pooled and their ranges).
4.3 Dichotomous‐ yes/no‐ data
We carried out an intention to treat analysis. Everyone allocated to the intervention were counted, whether they completed the follow up or not. It was assumed that those who dropped out had no change in their outcome. This rule is conservative concerning response to treatment, because it assumes that those discontinuing the studies would not have responded. It is not conservative concerning adverse effects, but we felt that assuming that all those leaving early would have developed side effects would overestimate risk. Where possible, efforts were 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 was generally assumed that if there had been 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 were not available, we used the primary cut‐off presented by the original authors.
We calculated the relative risk (RR) and its 95% confidence interval (CI) based on the random effects model, as this takes into account any differences between studies even if there is no statistically significant heterogeneity. 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). This misinterpretation then leads to an overestimate of the impression of the effect. When the overall results were significant we calculated the number needed to treat (NNT) and the number‐ needed‐ to‐ harm (NNH) as the inverse of the risk difference.
4.4 Continuous data
4.4.1 Normal distribution of the data
The meta‐analytic formulas applied by RevMan Analyses (the statistical programme included in RevMan) require a normal distribution of data. The software is robust towards some skew, but to which degree of skewness meta‐analytic calculations can still be reliably carried out is unclear. On the other hand, excluding all studies on the basis of estimates of the normal distribution of the data also leads to a bias, because a considerable amount of data may be lost leading to a selection bias. Therefore, we included all studies in the primary analysis. In a sensitivity analysis we excluded potentially skewed data applying the following rules:
a) When a scale started from the finite number zero the standard deviation, when multiplied by two, was less than the mean (as otherwise the mean is unlikely to be an appropriate
measure of the centre of the distribution, Altman 1996).
b) If a scale started from a positive value (such as PANSS which can have values from 30 to 210) the calculation described above was modified to take the scale starting point into account. In these cases skew is present if 2SD>(S‐Smin), where S is the mean score and Smin is the minimum score.
c) In large studies (as a cut‐off we used 200 participants) skewed data pose less of a problem. In these cases we entered the data in a synthesis.
d) The rules explained in a) and b) do not apply to change data. The reasons is that when continuous data are presented on a scale which includes a possibility of negative values, it is difficult to tell whether data are non‐normally distributed (skewed) or not. This is also the case for change data (endpoint minus baseline). In the absence of individual patient data it is impossible to know if data are skewed, though this is likely. After consulting the ALLSTAT electronic statistics mailing list, we presented change data in RevMan Analyses in order to summarise available information. In doing this, it was assumed either that data were not skewed or that the analysis could cope with the unknown degree of skew. Without individual patient data it is impossible to test this assumption. Change data were therefore included and a sensitivity analysis was not applied.
4.4.2 Data synthesis
For continuous outcomes we estimated a weighted mean difference (WMD) between groups. WMDs were again based on the random effects model, as this takes into account any differences between studies even if there is no statistically significant heterogeneity. We combined both endpoint data and change data in the analysis, because there is no principal statistical reason why endpoint and change data should measure different effects (Higgins 2005). When standard errors instead of standard deviations (SD) were presented, we converted the former to standard deviations. If both were missing we estimated SDs from p‐values or used the average SD of the other studies (Furukawa 2006)
4.4.3 Rating scales: A wide range of instruments are available to measure mental health outcomes. These instruments vary in quality and many are not valid, or even ad hoc. For outcome instruments some minimum standards have to be set. It has been shown that the use of rating scales which have not been described in a peer‐reviewed journal (Marshall 2000) are associated with bias, therefore we excluded the results of such scales.
4.5 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 1 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 intra‐class correlation co‐efficients of their clustered data and to adjust for this 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 co‐efficient (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 intra‐class correlation coefficients and relevant data documented in the report, synthesis with other studies would have been possible using the generic inverse variance technique.
5. Investigation for heterogeneity
Firstly, we considered all the included studies within any comparison to judge for clinical heterogeneity. Then visually inspected graphs to investigate the possibility of statistical heterogeneity. This was supplemented using, primarily, the I‐squared statistic. This provides an estimate of the percentage of variability due to heterogeneity rather than chance alone. Where the I‐squared estimate was greater than or equal to 50% we interpreted this as indicating the presence of considerable levels of heterogeneity (Higgins 2003). If inconsistency was high and clear reasons explaining the heterogeneity were found, we presented the data separately. If not, we commented on the heterogeneity of the data.
6. Addressing publication bias
We entered data from all identified and selected trials into a funnel graph (trial effect versus trial size) in an attempt to investigate the likelihood of overt publication bias. A formal test for funnel‐plot asymmetry was not undertaken.
7. Sensitivity analyses
In sensitivity analyses we excluded studies with potentially skewed data. A recent report showed that some of the comparisons of atypical antipsychotics may have been biased by using inappropriate comparator doses (Heres 2006). We, therefore, also analysed whether the exclusion of studies with inappropriate comparator doses changed the results of the primary outcome and the general mental state.
8.General
Where possible, we entered data in such a way that the area to the left of the line of no effect indicated a favourable outcome for sertindole.
