Chlorpromazine versus atypical antipsychotic drugs for schizophrenia

  • Protocol
  • Intervention



This is the protocol for a review and there is no abstract. The objectives are as follows:

To compare the effects of chlorpromazine with atypical or second generation antipsychotic drugs, for treatment of people with schizophrenia.


Description of the condition

Schizophrenia is one of the severe forms of major mental health disorders. It has a high lifetime prevalence rate (four per 1000 people - Saha 2005) but low incident rate because of the chronic nature of the illness. The median incident rate of schizophrenia is 15.2 per 100,000 people (McGrath 2008).

The illness is classified in categories F20-F29 as ‘schizophrenia, schizotypal and delusional disorder’ in the International Classification of Diseases (ICD-10 1992), particularly ‘schizophrenia’ in F-20. In ICD-10, it is described: "the schizophrenic disorders are characterized in general by fundamental and characteristic distortions of thinking and perception, and affects that are inappropriate or blunted". The Diagnostic and Statistical Manual of the American Psychiatric Association (DSM-IV-TR 2000) has also used the term ‘schizophrenia’ (discussed in Chapter 5).

The prognosis of schizophrenia is quite variable, and in the past psychiatrists were not very optimistic about its treatment (Kraeplin 1919). However, recent studies show that the outcome of schizophrenia treatment is better than was previously thought and use of phenothiazines may have played a part along with other factors such as improving community services (Bland 1978).

Description of the intervention

Psychiatrists have been prescribing typical antipsychotic drugs since the 1950s, when the first antipsychotic medication, chlorpromazine, was synthesized. Chlorpromazine was first used as an antihistaminic agent to treat allergies. Later, surgeons started using it as a pre-surgical medication to sedate people before surgical procedures (Laborit 1951). In 1952, Paul Charpentier, from Laboratories Rhône-Poulenc in France, and Delay and Deniker’s team described the antipsychotic properties of chlorpromazine (Delay 1952). Chlorpromazine is considered as a pivotal discovery in the field of psychosis treatment, with other antipsychotics often measured in 'chlorpromazine equivalents' (Turner 2007; Yorston 2000).

There are now many antipsychotic drugs available. They are broadly divided into two groups ‘typical antipsychotic drugs’ and ‘atypical antipsychotic drugs’. Typical antipsychotic drugs are also known as ‘first generation’, ‘conventional’ or ‘classical’ antipsychotic drugs, e.g. chlorpromazine and haloperidol. Atypical antipsychotic drugs are also known as ‘second generation’ or ‘newer antipsychotic drugs’, e.g. clozapine, risperidone, quetiapine and olanzapine. Typical antipsychotic drugs have a good reputation regarding their efficacy in treating the 'positive' symptoms of schizophrenia (e.g. delusions and hallucinations) (Mathews 2007). They are also well known for their adverse effects such as movement disorders (extra-pyramidal symptoms or extra-pyramidal side effects - EPS or EPSE), sedation, metabolic syndromes; and sometimes potentially fatal conditions such as agranulocytosis and neuroleptic malignant syndrome (Arana 2000). The second generation antipsychotic drugs arrived on the market, with notable differences. They had a reputed low side-effect profile and, according to pharmaceutical companies, higher efficacy (Janssen 1988). However, research funded independently of pharmaceutical companies has suggested that there may be little difference between the older and newer drugs, subsequently fuelling debate as to whether new atypical antipsychotics are more effective than older established first-generation antipsychotics, and whether questioning the efficacy of the two classifications of drugs creates an improper generalisation of antipsychotics that do not form a homogenous class (Leucht 2009). Against this backdrop, chlorpromazine remains a benchmark drug in the treatment of schizophrenia, and although imperfect, it is relatively inexpensive and remains one of the most common drugs used for schizophrenia worldwide (Adams 2005).

How the intervention might work

Chlorpromazine is an aliphatic phenothiazine, which is one of the widely-used typical antipsychotic drugs. Chlorpromazine is reliable for its efficacy and one of the most tested first generation antipsychotic drugs. It has been used as a ‘gold standard’ to compare the efficacy of older and newer antipsychotic drugs. It blocks alpha 1, 5HT2A, D2 and D1 receptors in the brain, and thus it works as an antipsychotic. It also has effect on muscarinic, serotonin & H1 receptors. By blocking D2 receptor it can also cause extrapyramidal side-effects. Other adverse effects include dry mouth, blurred vision, restlessness, sedation, neuroleptic malignant syndrome (DSM-IV 1994) etc. On the other hand, atypical antipsychotic drugs by definition may cause decreased or no extrapyramidal side-effects (Kinon 1996). Different atypical antipsychotic drugs act in different ways; for example, Clozapine blocks D2 & 5HT2 receptors (Meltzer 1989). Both clozapine and quetiapine blocks more 5HT2 receptors than D2 receptors. Olanzapine blocks 5HT2A, 5HT6, D1, D2, D3 and muscarinic receptors (Zhang 1999).

Why it is important to do this review

This is one of a family of related reviews on this important compound.

Chlorpromazine versus placebo Adams 2007
Chlorpromazine versus haloperidol Leucht 2008
Chlorpromazine doses Liu 2009
Chlorpromazine cessation Almerie 2007
Chlorpromazine for acute aggression Ahmed 2010

Chlorpromazine is one of two oral antipsychotic drugs on the World Health Organization's Essential Drug list (WHO 2011). It is globally accessible and has been known for its effectiveness in the treatment of schizophrenia since the 1950s (Adams 2007); it is also the most commonly used and inexpensive treatment for schizophrenia (Odejide 1982). Expensive new generation drugs are heavily marketed worldwide as a better treatment for schizophrenia - this may not be the case and an unnecessary drain on very limited resource (Adams 2006). Also, comparisons with new generation drugs, which are coming off-patent and therefore more accessible, are important to assist informed and independent choice.


To compare the effects of chlorpromazine with atypical or second generation antipsychotic drugs, for treatment of people with schizophrenia.


Criteria for considering studies for this review

Types of studies

All relevant randomised controlled trials will be included in the study. If a trial is described as 'double blind' but implies randomisation, we will include such trials in a sensitivity analysis (see Sensitivity analysis). If their inclusion does not result in a substantive difference, they will remain in the analyses. If their inclusion does result in 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. We will exclude quasi-randomised studies, such as those allocating by alternate days of the week. Where people are given additional treatments within the chlorpromazine and atypical antipsychotic groups, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the chlorpromazine and atypical antipsychotic groups that is randomised.

Types of participants

Adults however defined in each study, with schizophrenia including schizophreniform, schizoaffective and delusional disorders, by any means of diagnosis - including operational criteria (ICD-10 1992; DSM-IV 1994) or clinical opinion.

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. Chlorpromazine

Any dose and any route of administration.

2. Any atypical antipsychotic

Atypical antipsychotic drugs including: amisulpride, aripiprazole, asenapine (Smith 2010), clozapine, clothiapine or clotiapine (Toren 1995), iloperidone (Caccia 2010), lurasidone (Risbood 2012), mosapramine (Takahashi 1999), olanzapine, paliperidone, perospirone (Bian 2008), quetiapine, remoxipride (Nadal 2001), risperidone, sertindole (Cincotta 2010), sulpiride (Rzewuska 1988), ziprasidone and zotepine (list non-exhaustive).

Any dose and any route of administration.

Types of outcome measures

All outcomes will be divided into short term (nought to six months), medium term (seven to 12 months) and long term (over one year).

Primary outcomes
1. Clinical response

Clinically significant improvement - as defined by each study.

2. Relapse

As defined by each study.

Secondary outcomes
1. Death: natural death or suicide
2. Global state

2.1  Any change in global state.
2.2  Deterioration.
2.3  Need of additional antipsychotic drugs.
2.4  Need of additional benzodiazepines.
2.5  Poor compliance.

3. Mental state
3.1  General symptoms

3.1.1 Any change in general symptoms.
3.1.2 Average endpoint general symptom score.
3.1.3 Average change in general symptom score.

3.2 Specific symptoms (positive and negative symptoms of schizophrenia, depression & mania/hypomania)

3.2.1 Any change of specific symptoms.
3.2.2 Average endpoint specific symptom score.
3.2.3 Average change specific symptom score.

4. Service involvement

4.1 Duration of hospital stay.
4.2 Re-hospitalisation.
4.3 Engagement with community services.
4.4 Engagement with inpatient/outpatient services.

5. Functioning
5.1  General functioning

5.1.1 Any change in general functioning.
5.1.2 Average endpoint score in general functioning.
5.1.3 Average change score in general functioning.

5.2  Social functioning

5.1.1 Any change in social functioning.
5.1.2 Average endpoint score in social functioning.
5.1.3 Average change score in social functioning.

5.3  Employment status

5.1.1 Any change in employment status.
5.1.2 Average endpoint score in employment functioning.
5.1.3 Average change score in employment functioning.

6. Behaviour

6.1 General behaviour
6.2 Any improvement in behaviour - as defined in each study.
6.3 Specific behaviour (e.g. agitation, aggression, violent incidents).
6.4 Average endpoint in behaviour scores.
6.5 Average change in behaviour scores.

7. Satisfaction

7.1 Patient satisfaction.
7.2 Carer satisfaction.
7.3 Professional satisfaction (managers/doctors/nurses).

8. Economic outcomes

8.1  Direct costs - as defined in each study.
8.2  Indirect costs - as defined in each study.
8.3  Cost-effectiveness - as defined in each study.

9. Quality of life

9.1 Average endpoint score in quality of life.
9.2 Average change score in quality of life.
9.3 Any improvement in quality of life.

10. Adverse effects
10.1 Extrapyramidal symptoms

10.1.1 Specific effects (e.g. akathisia, muscle stiffness or rigidity, tremor).
10.1.2 Parkinsonism.
10.1.3 Average endpoint score.
10.1.4 Average change score.
10.1.5 Need for medication to reduce extrapyramidal symptoms.

10.2 Specific averse effects

10.2.1 Weight gain/ loss.
10.2.2 Headache.
10.2.3 Sedation.

10.3 Allergic/anaphylactic reaction
10.4 Endocrinological & metabolic adverse effects (amenorrhoea, galactorrhoea, hyperlipidaemia, hyperglycaemia)
10.5 Gastrointestinal adverse effects

10.5.1 Nausea/vomiting.
10.5.2 Constipation.

10.6 Cardiovascular adverse effect (ECG changes, QTc prolongation, arrhythmia)
10.7 Anticholinergic adverse effect

10.7.1 Dry mouth.
10.7.2 Blurred vision.

10.9 Sexual adverse effect

10.9.1 Loss of libido.
10.9.2 Erectile dysfunction.
10.9.3 Delayed ejaculation
10.9.4 Anorgasmia

10.10 Agranulocytosis/neutropenia
11. Effects on physiology

11.1 Pulse.
11.2 Blood pressure (hypertension/ hypotension).
11.3 Laboratory findings (e.g. blood count, cholesterol, glucose, liver function).

12. 'Summary of findings' table

We will use the GRADE approach to interpret findings (Schünemann 2008) and 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 will rate as important to patient-care and decision making. We aim to select the following main outcomes for inclusion in the 'Summary of findings' table:

  • Clinical response - clinically significant improvement (as defined by each of the studies) - by medium term.

  • Relapse (as defined by each of the studies) - by medium term.

  • Mental state - average endpoint score (Brief Psychopathology Rating Scale (BPRS)) - by medium term.

  • Extrapyramidal side effects - reported by the number participants - by medium term.

  • Participants leaving the study early - by medium term.

  • Quality of life - improvement - as defined by each of the study - by medium term.

  • Economic outcomes - cost effectiveness (as defined in each study) - by long term.

Search methods for identification of studies

Electronic searches

1. Cochrane Schizophrenia Group Trials Register

The Trials Search Co-ordinator will search the Cochrane Schizophrenia Group’s Trials Register using the phrase:

[((*chlorpromazine* AND (*amisulprid* or *aripiprazol* or *clozapin* or *olanzapin* or *quetiapin* or *risperidon* or *sertindol* or *ziprasidon* or *zotepin*or *sulpiride* or *remoxipride* or *paliperidone* or *perospirone*)) in title, abstract or index terms of REFERENCE or interventions of STUDY)]

The Cochrane Schizophrenia Group’s Trials Register is compiled by systematic searches of major databases, handsearches and conference proceedings (see Group Module). Incoming trials are assigned to existing or new review titles.

Searching other resources

1. Reference searching

We will inspect references of all included studies for further relevant studies published in any language.

2. Personal contact

We will contact the first author of each included study for information regarding unpublished trials.

Data collection and analysis

Selection of studies

Review authors KS and RZ will independently inspect citations from the searches and identify relevant abstracts. A random 20% sample will be independently re-inspected by SS 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 SS. Again, a random 20% of reports will be re-inspected by SS. 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 KS and RZ will extract data from all included studies. In addition, to ensure reliability, SS 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 SS will help clarify issues and these final decisions will be documented. Data presented only in graphs and figures will be extracted whenever possible, but included only 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:

  • the psychometric properties of the measuring instrument have been described in a peer-reviewed journal (Marshall 2000); and

  • 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 will use mean differences (MD) rather than standardised mean differences (SMD) throughout (Higgins 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 all data before inclusion:
a) standard deviations (SDs) and means are reported in the paper or obtainable from the authors;
b) when a scale starts from the finite number zero, the SD, 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 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.

Endpoint scores on scales often have a finite start and end point and these rules can be applied. Skewed data pose less of a problem when looking at means if the sample size is large (> 200) and we will enter these into the syntheses. We will present skewed endpoint data from studies of less than 200 participants as 'other data' within the data and analyses section rather than enter such data in analyses.
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 skewed change data into statistical analyses.

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 BPRS (Overall 1962) or the PANSS (Kay 1986), this could be considered as a clinically significant response (Leucht 2005; 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 chlorpromazine. 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. This will be noted in the relevant graphs.

Assessment of risk of bias in included studies

Again review authors KS and RZ will work independently to assess risk of bias by using criteria described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) 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 another member of the review group. 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 by discussion.

The level of risk of bias will be noted in both the text of the review and in the Summary of findings table 1.

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/Harm (NNT/H) 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. We prefer not to calculate effect size measures (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 the review we will seek to contact first authors of such 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 received statistical advice that the binary data 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  (Combining groups) of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Where the additional treatment arms are not relevant, these data will not be reproduced.

Dealing with missing data

1. Overall loss of credibility

At some degree of loss of follow-up, data must lose credibility (Xia 2009). We choose that, 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/s by down-rating quality. Finally, we will also downgrade quality within the 'Summary of findings' table/s 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, data will be presented on a 'once-randomised-always-analyse' basis (an intention-to-treat 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 stayed in the study - in that particular arm of the trial - will be used for those who did not. A sensitivity analysis will be undertaken to test how prone the primary outcomes are to change when 'completer' data only are compared to the intention-to-treat 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 completer-only data 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 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 nevertheless will 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 last observation carried forward (LOCF) will 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 have 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 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 - Higgins 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 (Higgins 2011). We will try to locate protocols of included randomised trials. If the protocol is available, we will compare outcomes in the protocol and in the published report. If the protocol is not available, we will compare outcomes listed in the methods section of the trial report with actually reported results.

2. Funnel plot

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 (Higgins 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 random-effects model for all analyses. The reader is, however, able to choose to inspect the data using the fixed-effect model.

Subgroup analysis and investigation of heterogeneity

1. Subgroup analyses
1.1 Primary outcomes

No subgroup analyses are anticipated.

1.2 Clinical state, stage or problem

We propose to undertake this review and provide an overview of the effects of chlorpromazine versus atypical antipsychotic drugs 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, 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 outlying studies will be successively removed 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, 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, we will include these studies and if there is no substantive difference when the implied randomised studies are added to those with better description of randomisation, then all data will be employed from these studies.

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 compared with completer data only. If there is a substantial difference, we will report results and discuss them but 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 on primary outcomes when we use our assumption compared with complete data only. A sensitivity analysis will be undertaken testing how prone results are to change when 'completer' 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 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

All data will be synthesised 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.


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.

We would like to thank Khaled Turkmani for peer reviewing this protocol.

Contributions of authors

Kumar Saha - developed the protocol.

Rashid Zaman - developed the protocol.

Stephanie Sampson - helped to develop the protocol.

Declarations of interest

No conflicts of interest known.

Sources of support

Internal sources

  • Nottinghamshire Healthcare NHS Trust, UK.

External sources

  • National Institute for Health Research (NIHR), UK.

    Cochrane Collaboration Programme Grant 2011; Reference number: 10/4001/15