Types of studies

All relevant randomised control trials will be considered. We will include quasi‐randomised trials such as those where allocation is undertaken based on time of admission to the hospital. We will also submit these trials to a sensitivity analysis. Where trials are described as 'double‐blind', but it is implied that the study is randomised and where the demographic details of each group's participants are similar, trials will be included and sensitivity analysis will be undertaken to the presence or absence of these data. Randomised cross‐over studies will be eligible but only data up to the point of first cross‐over will be analysed because of the instability of the problem behaviours and the likely carry‐over effects of all treatments (Elbourne 2002).

Types of participants

People with the diagnosis of schizophrenia and other types of schizophrenia‐like psychoses (schizophreniform disorder, schizoaffective disorder and acute psychotic disorder) however diagnosed, and irrespective of age, sex or severity of illness will be chosen for this study, as well as those with 'serious/chronic mental illness' or 'psychotic illness'. There is no clear evidence that the schizophrenia‐like psychoses are caused by fundamentally different disease processes or require different treatment approaches (Carpenter 1994). People with psychotic symptoms due to dementia, general medical conditions, depression and problems associated with substance misuse will be excluded.

Types of interventions

Comparisons will be made between sulpiride and individual comparator drugs. No comparison will be made between sulpiride and comparator drugs as a class, such as typical/atypical antipsychotics.

1. Sulpiride: any dose and mode or pattern of administration. If a high/low dichotomy is not provided within the trial, high dose will be defined as >800 mg/day and low dose as any dose less than that.
2. Other antipsychotic drugs: any dose and mode or pattern of administration.

Types of outcome measures

As schizophrenia is often a life‐long illness, and sulpiride is used as an ongoing treatment, outcomes will be grouped according to time periods: short term (less than three months), medium term (three ‐ twelve months) and long term (more than one year).

Electronic searches

1. The Cochrane Schizophrenia Group Trials Register was searched using the phrase:
 [(ability * or championyl* or coolspan* or col‐sulpir* or digton* or dixibon* or dobren* or do?matil* or drominetas* or eglonyl* or equilid* or eusulpid* or guastil* or isnamid* or kapirid* or lavodina* or leboprid* or lusedan* or miradol* or mirbanil* or misulvan* or neuromyfar* or normum* or omperan* or psicocen* or quiridil* or sato * or sernevin* or sicofrenol* or sulp?ride* or sulpisedan* or suprium* or sursumid* or tepavil* or tonofit* or ulpir* or vipral*) in title, abstract and index fields in REFERENCE) OR (sulp?rid* in interventions field in STUDY)]

This register is compiled by systematic searches of major databases, hand searches and conference proceedings (see Group Module). The Cochrane Schizophrenia Group Trials Register is maintained on Meerkat 1.5. This version of Meerkat stores references as studies. When an individual reference is selected through a search, all references which have been identified as the same study are also selected.

2. Details of previous electronic search
See Appendix 1.

Searching other resources

1. Reference searching
In addition to the above searches we will also search reference lists of included studies for additional relevant trials.

2. Personal contact
We will contact the first author of each included study and known experts who had published reviews in the field for information regarding unpublished trials and extra data on the published trials.

3. Drug company
The manufacturers of sulpiride (Lorex Synthelabo Ltd, Bristol‐Myers Pharmaceuticals, Pharmacia and Upjohn) will be contacted to provide relevant published and unpublished data.

Selection of studies

Authors IMO and JW will independently inspect all study citations identified by the searchers and full reports of the studies of agreed relevance will be obtained. Where disputes arise we will acquire the full report for more detailed scrutiny. These articles will be then inspected, independently, by two reviewers (IMO and JW) to assess their relevance to this review. Again where disagreement occur attempts will be made to resolve this through discussion; if doubts still remain we will add these trials to the list of those awaiting assessment pending acquisition of further information.

Data extraction and management

1. Data Extraction
IMO, JW and BS will independently extract data from the included studies. Again, any disagreement will be discussed, decisions will be documented and, if necessary, authors of studies will be contacted for clarification. When this is not possible and further information is necessary to resolve the dilemma, we will not enter the data and add the trial to the list of those studies awaiting assessment.

2. Management
We will extract the data onto standard, simple forms. Where possible, data will be entered into RevMan in such a way that the area to the left of the 'line of no effect' will indicate a 'favourable' outcome for sulpiride. Where this is not possible, for example for scales that calculate higher scores = improvement, graphs in RevMan analyses will be labelled accordingly so that the direction of effects is clear.

3. Scale‐derived data
3.1 Valid scales
A wide range of instruments are available to measure outcomes in mental health studies. These instruments vary in quality and many are not validated, or are even ad hoc. It is accepted generally that measuring instruments should have the properties of reliability (the extent to which a test effectively measures anything at all) and validity (the extent to which a test measures that which it is supposed to measure) (Rust 1989). Unpublished scales are known to be subject to bias in trials of treatments for schizophrenia (Marshall 2000). Therefore continuous data from rating scales will be included only if the measuring instrument was described in a peer‐reviewed journal.

3.2 Binary outcomes from scale data
Where possible, efforts will be made to convert outcome measures to binary 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 will be 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 2005, Leucht 2005a). If data based on these thresholds are not available, we will use the primary cut‐off presented by the original authors.

Regarding categorical measures (e.g. one of seven categories on a global state, such as 'very much improved', 'much improved', 'minimally improved', 'no change', 'minimally worse', 'much worse', 'very much worse' in an overall improvement), we will set the cut‐off points between 'much improved' and 'minimally improved', dividing participants into 'clinically improved' or 'not clinically improved'.

Assessment of risk of bias in included studies

IMO, JW and BS will work independently to assess risk of bias by using criteria described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2008). This set of criteria is based on evidence of associations between overestimation of effect and high risk of bias of the article such as sequence generation, allocation concealment, blinding, incomplete outcome data, and selective reporting.

The categories are defined below:
YES ‐ low risk of bias
NO ‐ high risk of bias
UNCLEAR ‐ uncertain risk of bias

If sequence generation process within the trial is by quasi‐random means, such as by hospital record number, this will be noted and the study will be given a 'NO (high risk of bias)' rating. If disputes will arise as to which category a trial have to be allocated, again resolution will be made by discussion.

Measures of treatment effect

1. Binary data
The review will use relative risk (RR) and its 95% confidence interval (CI) based on the fixed‐effect model as this takes into account the true effect of intervention is the same value in every study. RR is more intuitive (Boissel 1999) than odds ratios and 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. For statistically significant results we will calculate the number needed to treat to provide benefit (NNTB) and the number needed to treat to induce harm (NNTH) as the inverse of the risk difference.

2. Continuous data
2.1 Summary statistic
For continuous outcomes we will estimate a fixed‐effect weighted mean difference (WMD) between groups. We will not calculate effect size measures. If SDs are not reported, authors will be asked to supply the data. When standard errors, CIs, t values or P values are reported, SDs will be calculated according to Higgins 2008. In the absence of these data, the mean standard deviation from other studies will be used (Furukawa 2006).

2.2 Endpoint versus change data
We prefer to use scale endpoint data, which typically cannot have negative values and is easier to interpret from a clinical point of view. Change data is more problematic and the rule described above does not hold for it. Where both endpoint and change are available for the same outcome the reviewers prefer to present the former.

2.3 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 will be applied to all data before inclusion: (i) means and SDs are reported in the paper or are obtained from the authors, or SDs are estimated by the method described before; (ii) if the data are finite number zero, for example 0‐100, when the standard deviation is 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 to them. 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 will be 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 they will be entered into syntheses.

Unit of analysis issues

1. Cluster trials
Studies increasingly employ 'cluster randomisation' (such as randomisation by clinician or by practice) but analysis and pooling of clustered data poses problems. First, 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 is not accounted for in primary studies, we will present data in a table, with a (*) symbol to indicate the presence of a probable unit of analysis error. In subsequent versions of this review we will seek to contact first authors of studies to obtain intraclass correlation coefficients of their clustered data and to adjust for this by using accepted methods (Gulliford 1999). Where clustering had been incorporated into the analysis of primary studies, we will present these data as if from a non‐cluster randomised study, but adjust for the clustering effect.

We have sought statistical advice and have been advised that 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 is not reported it will be 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, we will only use data from the first phase of the cross‐over studies.

Dealing with missing data

1. Overall loss of credibility
At some degree of loss to follow‐up data must lose credibility (Xia 2007). We are forced to make a judgment where this is for the trials likely to be included in this review. Where more than 40% of data is unaccounted for by the end of the trial we will not reproduce these data or use them within analyses.

2. Binary
Where attrition for a binary outcome is between 0 and 40%, and outcomes of these people are described, we will include these data as reported. Where the outcomes of such people are not clearly described, data will be presented on a 'once‐randomised‐always‐analyse' basis, assuming an intention to treat analysis. Those lost to follow‐up are all assumed to have a negative outcome, with the exception of the outcome of death. For example, for the outcome of 'not clinically improved', those who are lost to follow‐up are all 'not clinically improved'. A final sensitivity analysis will be undertaken testing how prone the primary outcomes are to change when 'completed' data only are compared to the intention to treat analysis using the negative assumption.

3. Continuous
In the case where attrition for a continuous outcome is between 0 and 40% and completer‐only data will be reported, we will use them within analysis. 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. Therefore, where LOCF data are used in the analysis, it will be indicated in the review.

Assessment of heterogeneity

1. Clinical heterogeneity
We will consider all included studies individually, without any comparison to judge clinical heterogeneity.

2. Statistical
2.1 Visual inspection
We will visually inspect graphs to investigate the possibility of statistical heterogeneity.

2.2 Employing the I‐squared statistic
This provided an estimate of the percentage of inconsistency thought to be due to chance. An I‐squared estimate greater than or equal to 50% is interpreted as evidence of substantial heterogeneity (Higgins 2008), and reasons for heterogeneity will be explored. If the inconsistency is high and the clear reasons are found, data will be presented 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). 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 ten 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

Where possible we will employ a fixed‐effect model for analyses. 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, although, random‐effects does put extra weight onto the smaller studies, i.e. those trials that are most vulnerable to bias. For this reason we favour using the fixed‐effect model employing random‐effects only when investigating heterogeneity.

Subgroup analysis and investigation of heterogeneity

1. Investigation of heterogeneity
If high levels of heterogeneity are found, we will check that data are correctly extracted and entered and that we have made no unit of analysis errors.Then we will re‐analyse the data using a random‐effects model to see if this will make a substantial difference. If the high levels of heterogeneity remain we will not undertake a meta‐analysis at this point for if there is considerable variation in results, and particularly if there is inconsistency in the direction of effect, it may be misleading to quote an average value for the intervention effect. We would want to explore heterogeneity. Pre‐specified subgroup analyses will be undertaken as a means of investigating heterogeneous results.

2. Subgroup analysis
It is expected that several subgroup analyses can be undertaken within this review. The following hypotheses will be tested: when compared with other antipsychotics, for the primary outcomes of interest (Criteria for considering studies for this review), sulpiride is differentially effective for:

2.1 Men and women
2.2 People who are under 18 years of age (adolescent patients), between 18 and 64 (adult patients), or over 65 years of age (elderly patients).
2.3 People who became ill recently (i.e. acute episode approximately less than one month's duration, including first onset of disease or recurrence) as opposed to people who have been ill for longer.
2.4 People who are given low doses (1‐800 mg/day) and those given high doses (over 801 mg/day) of sulpiride.
2.5 People who have schizophrenia diagnosed according to any operational criteria (i.e. a pre‐stated checklist of symptoms/ problems/ time periods/ exclusions) as opposed to those who have entered the trial with loosely defined illness.
2.6 People treated earlier (pre‐1990) and people treated in recent years (1990 to present).
2.7 Duration of study: short term (less than three months), medium term (three to twelve months) and long term (more than one year).

Sensitivity analysis

We plan sensitivity analyses of the primary outcome a priori for examining the change in the robustness of the sensitivity to including studies with quasi‐randomisation, with implied randomisation and with high attrition rates (more than 40%). In addition, we will conduct a sensitivity analysis to investigate whether the findings of Chinese trials differ substantially from other trials, as there is concern regarding the quality of trials from China (Wu 2006).