Haloperidol versus low‐potency first‐generation antipsychotic drugs for schizophrenia
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To review the effects of the high‐potency antipsychotic drug haloperidol versus low‐potency antipsychotic drugs. Haloperidol is clinically perceived to be more efficacious than low‐potency drugs and in this review we tested the hypothesis that haloperidol is more effective than low potency antipsychotic drugs.
Background
Description of the condition
Schizophrenia is often a chronic and disabling psychiatric disorder. It afflicts approximately one per cent of the population world‐wide with little gender differences (Berger 2003). The typical manifestations of schizophrenia are 'positive' symptoms such as fixed, false beliefs (delusions) and perceptions without cause (hallucinations); 'negative' symptoms such as apathy and lack of drive, disorganisation of behaviour and thought; and catatonic symptoms such as mannerisms and bizarre posturing (Carpenter 1994). The degree of suffering and disability is considerable, with 80% to 90% not working (Marvaha 2004) and up to 10% dying by suicide (Tsuang 1978).
Description of the intervention
Antipsychotic drugs are the core treatment for schizophrenia. All antipsychotic drugs block, to a greater or lesser extent, D2‐receptors in the brain. They can be classified according to their biochemical structure (e.g. butyrophenones, phenothiazines, thioxanthenes etc.), their risk of producing movement disorders ('atypical' versus 'typical' antipsychotics) and the doses necessary for an antipsychotic effect (high‐potency versus low‐potency antipsychotics). The classification into high‐potency and low‐potency medication means that for low potency antipsychotic drugs, higher doses are necessary to obtain the same dopamine receptor occupancy and efficacy (Seeman 1975). In this context, haloperidol belongs to the high‐potency antipsychotic drug group (Figure 1). It is the most frequently used conventional antipsychotic drug in many countries including Germany (Kaye 2003; Lohse 2005; Paton 2003). Haloperidol is mostly indicated in schizophrenia, acute psychosis and delirium.
Haloperidol
Low‐potency antipsychotic drugs will be the comparator drugs in this review. Typical examples of low‐potency antipsychotic drugs are chlorpromazine, chlorprothixene, thioridazine or levomepromazine. It is an old psychiatric dogma that can be found in textbooks and guidelines that ‐ with the exception of clozapine ‐ there is no difference in efficacy between any antipsychotic compounds (Gaebel 2006; Lehman 2004). Nevertheless, low‐potency antipsychotic drugs are clinically often perceived as less efficacious than high‐potency compounds, and high‐ and low‐potency antipsychotics also seem to differ in adverse effects. Low‐potency drugs have a high incidence of sedation or hypotonia, whereas high‐potency drugs produce most extrapyramidal adverse effects.
How the intervention might work
The theory is that schizophrenia is a chronic disorder caused by hyper‐dopaminergic states in the limbic system (Berger 2003). All antipsychotic drugs block dopamine receptors. Haloperidol was discovered by Paul Janssen and developed 1957. Concerning dopamine receptor blockade, haloperidol is approximately 50 times more potent than chlorpromazine. It is a butyrophenone antipsychotic and is very effective against delusions and hallucinations. It is a strong dopamine (mainly D2) receptor antagonist with antipsychotic properties and antiemetic properties. Haloperidol effectively blocks receptors in the limbic system of the brain. It has a rapid onset of action lasting three to six hours and a bioavailability of 60%. The elimination half‐life period ranges from 12 to 36 hours. However, the dopaminergic action is blocked in the nigrostriatal pathways and this blockage can lead to extrapyramidal side effects.
Low‐potency medications have a lower affinity for dopamine receptors so that a higher dose is required to effectively treat symptoms of schizophrenia. They additionally also block other than dopamine receptors, such as cholinergic or histaminergic receptors. This also explains the occurrence of adverse effects which are less frequent with high‐potency drugs, such as sedation or hypotonia. The cutoff between high‐ and low‐potency drugs is not clear, but the attempt has been made to express their relationship in terms of dose equivalence. The most frequently applied concept is based on chlorpromazine equivalents according to Davis 1974 or Haase 1983 and provides data about comparable doses of various antipsychotic drugs to achieve a therapeutic effect similar to 100 mg chlorpromazine.
Why it is important to do this review
Systematic reviews on the comparative efficacy of high‐potency versus low‐potency antipsychotic drugs are not available. Cochrane reviews on the effects of specific conventional antipsychotic drugs have been published, but they compared the effects of one antipsychotic drug versus any other antipsychotic drugs (e.g. pimozide versus any other antipsychotic drug, Fenton 2007) and thus did not consider the important classification in high‐potency and low‐potency antipsychotics. Due to this lack of evidence, treatment guidelines make statements such as “all conventional antipsychotics if adequately dosed have comparable efficacy” (German national schizophrenia guideline (Gaebel 2006,); or guideline of the World Federations of Societies of Biological Psychiatry (Falkai 2005)).
These guidelines contrast with the clinical impression that low‐potency conventional antipsychotic drugs are less efficacious than high‐potency conventional antipsychotic drugs. The clinical consequences to follow these guidelines are considerable, because high‐potency and low‐potency antipsychotics differ clearly in side effects. High‐potency antipsychotics often lead to strong extrapyramidal symptoms; low‐potency antipsychotics on the other hand have strong sedating properties and often also lead to hypotension.
Conventional antipsychotic drugs are still the mainstay of treatment in countries that can not afford newer, expensive 'atypical' or 'second generation' antipsychotic drugs and even in some industrialised countries such as Germany, conventional antipsychotic medications still account for 50% of the market share (Lohse 2005). Recent studies about these more expensive second generation antipsychotics have also called into question their superiority (Jones 2006; Leucht 2009a; Lieberman 2005). Therefore, research on older conventional agents is very essential and has been requested (Leucht 2009b).
For list of similar reviews please see Table 1.
| Title |
| Haloperidol versus low‐potency antipsychotic drugs |
| Flupenthixol versus low‐potency antipsychotic drugs (protocol to be published 2011) |
| Fluphenazine versus low‐potency antipsychotic drugs (protocol to be published 2011) |
| Perphenazine versus low‐potency antipsychotic drugs |
| Trifluoperazine versus low‐potency antipsychotic drugs (protocol to be published 2011) |
Objectives
To review the effects of the high‐potency antipsychotic drug haloperidol versus low‐potency antipsychotic drugs. Haloperidol is clinically perceived to be more efficacious than low‐potency drugs and in this review we tested the hypothesis that haloperidol is more effective than low potency antipsychotic drugs.
Methods
Criteria for considering studies for this review
Types of studies
We included randomised controlled (parallel group or cross‐over) trials that had a minimum follow‐up duration of three weeks. We included trials that were described as randomised or where randomisation was implied. We excluded quasi‐randomised trials, such as those that used alternation, an open list of random numbers, or any other method of recruitment where allocation to interventions was predictable.
Types of participants
People with schizophrenia and schizophrenia‐like psychoses (schizophreniform and schizoaffective disorders). There is no clear evidence that the schizophrenia‐like psychoses are caused by fundamentally different disease processes or require different treatment approaches (Carpenter 1994). We included studies irrespective of the diagnostic criteria used. Diagnostic criteria, such as ICD 10 or DSM‐IV, are not routinely used in clinical practice and restricting inclusion to trials that used operationally defined diagnostic criteria would have reduced generalisation and representativeness.
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. Intervention: haloperidol
Any dose of oral mode of administration (no depots, no short‐acting parenteral forms of administration).
We have made an a priori decision that haloperidol will be the examination drug because it is clinically perceived to be more efficacious than low‐potency drugs. Therefore, our hypothesis is that haloperidol is more efficacious and we have thus chosen it as the examination drug.
2. Low‐potency antipsychotic drugs
The control interventions will be low‐potency conventional antipsychotic drugs with any oral form of administration and any dose. We will use the dose equivalence tables by Davis 1974 and/or Haase 1983 to define drugs as low‐potency with a chlorpromazine equivalence roughly equal or higher than chlorpromazine.
Types of outcome measures
We will analyse the outcomes for different lengths of follow‐up: up to three months, six months or more than six months.
Primary outcomes
1. Clinical response
Clinically significant response in global state as defined by the original studies.
Secondary outcomes
1. Mental state: symptoms of schizophrenia
1.1 Overall symptoms ‐ average score/change in mental state
1.2 Positive symptoms ‐ average score/change in positive symptoms
1.3 Negative symptoms ‐ average score/change in negative symptoms
2. Global state: average score/change in global state
3. Relapse ‐ as defined by each of the studies
4. Leaving the study early
4.1 Leaving the study due to any reason
4.2 Leaving the study early due to inefficacy of treatment
4.3 Leaving the study early due to side effects
5. Service use
5.1 Rehospitalisation
6. Mortality
6.1 Death (all causes)
6.2 Suicide
7. Adverse effects
7.1 At least one adverse effect
7.2 Extrapyramidal/movement disorders
7.3 Cardiac effects
7.4 Hypotension
7.5 Sedation
7.6 Weight gain
8. Quality of life
9. Participant's/carer`s satisfaction with care
10. Economic outcomes
Search methods for identification of studies
We will apply no language restrictions within the limitations of the search tools.
Electronic searches
We will search the ‘Cochrane Schizophrenia Group Trials Register’ for relevant studies (July 2010) using the phrase:
[(*haloperidol* in intervention of STUDY) OR (*haloperidol* in title, abstract and index terms of REFERENCE entered >=01/05/10)]
This register is compiled by systematic searches of major databases, hand searches and conference proceedings (see Group Module).
Searching other resources
1. Reference searching
We will inspect the references of all identified studies for more trials.
2. Previous reviews
We will search previous conventional reviews (Davis 1989; Klein 1969).
3. Personal contact
We will contact the first author of each included study for missing information and for the existence of further studies.
4. Drug companies
We will contact the original manufacturer of haloperidol and ask them for further relevant studies and for missing information on identified studies.
Data collection and analysis
Selection of studies
Two review authors will independently inspect all abstracts identified in the searches. We will resolve disagreement by discussion and, where doubt still remains, we will acquire the full article for further inspection. Once we obtain the full articles, at least two authors will independently whether the studies meet the review criteria. If we cannot resolve disagreement by discussion, we will request input from the third author, or seek further information from the study authors.
Data extraction and management
1. Extraction
One review author (MT) will extract data from all included studies. In addition, to ensure reliability, another author (MH) will independently extract data from a random sample of these studies, comprising 10% of the total. Again, we will discuss any disagreement, document decisions and, if necessary, contact authors of studies for clarification. With any remaining problems SL will help clarify issues and we will document those final decisions. We will extract data presented only in graphs and figures whenever possible, but we will include them only if two reviewers independently reach 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. Where possible, we will extract data relevant to each component centre of multi‐centre studies separately.
2. Management
2.1 Forms
We will extract data onto simple standard 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 was not written or modified by one of the trialists for that particular trial.
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 to primarily use endpoint data and only use change data if the former are not available. We will combine endpoint and change data in the analysis as we used mean differences (MD) rather than standardised mean differences throughout (Higgins 2009, Chapter 9.4.5.2).
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 all data before inclusion: a) standard deviations and means are reported in the paper or obtainable from the authors; b) when a scale starts from the finite number zero, the standard deviation, when multiplied by two, is less than the mean (as otherwise the mean is unlikely to be an appropriate measure of the centre of the distribution, (Altman 1996); c) if a scale started from a positive value (such as PANSS which can have values from 30 to 210) we will modify the calculation described above 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 that includes a possibility of negative values (such as change data), it is difficult to tell whether data are skewed or not. We will enter skewed data from studies of fewer than 200 participants 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.
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, we will attempt 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'. We will generally assume 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 can be considered as a clinically significant response (Leucht 2005b, Leucht 2005a). 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 improved') we will report data where the left of the line indicates an unfavourable outcome. We will note this in the relevant graphs.
2.8 Summary of findings table
We anticipate including the following short‐ or medium‐term outcomes in a summary of findings table.
1. Clinical response
-
Clinically significant response in global state ‐ as defined by each of the studies
-
Healthy days
2. Acceptability of treatment
-
Leaving the study early
3. Service utilisation outcomes
-
Hospital admission
-
Days in hospital
4. Adverse effect ‐ any important adverse event ‐ e.g. EPS, sedation, death
5. Quality of life ‐ improved to an important extent
Assessment of risk of bias in included studies
Again working independently, two authors will assess 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 will assess the risk of bias in each domain and overall and categorise these as follows
A. Low risk of bias: plausible bias unlikely to seriously alter the results (categorised as 'Yes' in Risk of Bias table)
B. High risk of bias: plausible bias that seriously weakens confidence in the results (categorised as 'No' in Risk of Bias table)
C. Unclear risk of bias: plausible bias that raises some doubt about the results (categorised as 'Unclear' in Risk of Bias table)
If the raters disagree, we will make the final rating by consensus with the involvement of another member of the review group. Where inadequate details of randomisation and other characteristics of trials are provided, we will contact authors of the studies in order to obtain further information. We will report non‐concurrence in quality assessment.
Measures of treatment effect
1. Dichotomous data
For binary outcomes we will calculate a standard estimation of the random‐effects 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). This misinterpretation then leads to an overestimate of the impression of the effect. Where possible, we will attempt to convert outcome measures to dichotomous data. This could be done by identifying cut‐off points on rating scales and dividing participants accordingly into 'clinically improved' or 'not clinically improved'. We will generally assume 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 can 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. Continuous data
For continuous outcomes we will estimate a mean difference (MD) between groups using the random‐effects model, as this takes into account any differences between studies even if there is no statistically significant heterogeneity. We will not calculate standardised mean differences (SMD) measures, except in cases where scales are of such similarity to allow pooling, when we will calculate the SMD and, whenever possible, 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 pose problems. 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 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. 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 adjusted for the clustering effect. If a cluster study has been appropriately analysed taking into account intra‐class correlation co‐efficient and relevant data documented in the report, synthesis with other studies would 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 schizophrenia, we will consider randomised cross‐over studies eligible, but use only data up to the point of first cross‐over.
3. Studies with multiple treatment groups
Where a study involves more than two treatment arms, if relevant, we will present the additional treatment arms in comparisons. If data are binary we will simply add these and combine within the two‐by‐two table. If data are continuous we will combine following the formula in section 7.7.3.8 (Combining groups) of the Handbook. Where the additional treatment arms are not relevant, we will not reproduce these data.
Dealing with missing data
1. Overall loss of credibility
At some degree of loss of follow‐up data must lose credibility (Xia 2007). The loss to follow‐up in randomised schizophrenia trials is often considerable calling the validity of the results into question. Nevertheless, it is unclear which degree of attrition leads to a high degree of bias. We will not exclude trials from outcomes on the basis of the percentage of participants completing them. We, however, will use the risk of bias tool described above to indicate potential bias when more than 25% of the participants from the haloperidol group and low‐potency drug group have left the studies prematurely, when the reasons for attrition differ between the intervention and the control group, and when no appropriate imputation strategies have been applied.
2. Dichotomous data
We will present data on a 'once‐randomised‐always‐analyse' basis, assuming an intention‐to‐treat analysis. If the original authors have applied such a strategy, we will use their results. If the authors have presented only the results of the per‐protocol or completer population, we will assume that those participants lost to follow‐up would have had the same percentage of events as those who remained in the study.
3. Continuous data
3.1 Attrition
We will use intention‐to‐treat (ITT) when available. We anticipate that in some studies, in order to do an ITT analysis, the method of last observation carried forward (LOCF) would be employed within the study report. As with all methods of imputation to deal with missing data, LOCF introduces uncertainty about the reliability of the results (Leon 2006). Therefore, where LOCF data have been used in the analysis, we will indicate this in the review.
3.2 Standard deviations
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 and confidence interval are available for group means, and either P value or T value are available for differences in mean, we will calculate them according to the rules described in the Handbook (Higgins 2009): when only the standard error (SE) is reported, standard deviations (SDs) are calculated by the formula SD = SE * square root (n). Chapters 7.7.3 and 16.1.3 of the Handbook (Higgins 2009) present detailed formula for estimating SDs from P values, T or F values, confidence intervals, ranges or other statistics. If these formula 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 will nevertheless examine the validity of the imputations in a sensitivity analysis excluding imputed values.
3.3 Last observation carried forward
We anticipate that in some studies the method of LOCF would be employed within the study report. As with all methods of imputation to deal with missing data, LOCF introduces uncertainty about the reliability of the results (Leucht 2007). Therefore, where LOCF data has been used in the trial, if less than 50% of the data have been assumed, we will reproduce these data and indicate that they are the product of LOCF assumptions.
Assessment of heterogeneity
1. Clinical heterogeneity
We will consider all included studies without any comparison group to judge clinical heterogeneity.
We will simply inspect all studies for clearly outlying situations or people which we had not predicted would arise. Should such situations or participant groups arise, we will fully discuss these.
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. Should such methodological outliers arise, we will fully discuss these.
3. Statistical
3.1 Visual inspection
We will visually inspect graphs to investigate the possibility of statistical heterogeneity.
3.2 Employing the I2statistic
We will investigate heterogeneity among studies 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 2008). 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 of 50% to 90%, accompanied by a statistically significant Chi2 statistic, may represent substantial heterogeneity (Section 9.5.2 ‐ Higgins 2008); and we will explore reasons for heterogeneity. If the inconsistency is high and the clear reasons are found, we will present data separately.
Assessment of reporting biases
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997). These are described in Section 10 of the Handbook (Higgins 2009). 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 will employ a random‐effects model for analyses (Der‐Simonian 1986). 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 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 will examine in a secondary analysis whether using a fixed‐effect model markedly changed the results of the primary outcome.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analysis
1.1 Different low‐potency drugs
We will perform sub‐grouping by comparing haloperidol versus each single low‐potency antipsychotic separately.
1.2 Clinical state, stage or problem
We propose to undertake this review and provide an overview of the effects of social skills training for people with schizophrenia in general. In addition, however, we will try to report data on subgroups of people in the same clinical state, stage and with similar problems.
2. Investigation of heterogeneity
If inconsistency is high, we will report this. First we will investigate whether data have been entered correctly. Second, if data are correct, we will visually inspect the graph and successively remove studies outside of the company of the rest to see if homogeneity is restored. For this review we have decided that should this occur with data contributing to the summary finding of no more than around 10% of the total weighting, we will present data. If not, we will not pool data and will discuss any issues. 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 is obvious, we plan to 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 outcome we will include these studies and if there is no substantive difference when the implied randomised studies are added to those with better descriptions of randomisation, then we will employ all data from these studies.
2. Implication of non double‐blind trials
We aim to include trials in a sensitivity analysis if participants and treating psychiatrists have not been blinded. For the primary outcome we will include these studies and, if there is no substantive difference when the non double‐blind studies are added to the double‐blind studies, then we will employ all data from these studies.
3. Assessment of dosage
We aim to include trials in a sensitivity analysis if doses between haloperidol and low‐potency antipsychotics are clearly discrepant by our judgement based on the chlorpromazine equivalence tables (Andreasen 2010; Davis 1974; Haase 1983). If there is no substantive difference when studies with discrepant doses are added, then we will employ all data from these studies.
| Title |
| Haloperidol versus low‐potency antipsychotic drugs |
| Flupenthixol versus low‐potency antipsychotic drugs (protocol to be published 2011) |
| Fluphenazine versus low‐potency antipsychotic drugs (protocol to be published 2011) |
| Perphenazine versus low‐potency antipsychotic drugs |
| Trifluoperazine versus low‐potency antipsychotic drugs (protocol to be published 2011) |
