1. Fluphenazine: any dose of only oral administration

2. Placebo: (active or inactive) or no treatment

Primary outcomes

Secondary outcomes

Cochrane Schizophrenia Group’s Study‐Based Register of Trials

On 23 December 2014 and 9 November 2016, the information specialist searched the register using the following search strategy:

(*Fluphenazine* AND *Placebo*) in Intervention Field of STUDY

In such study‐based register, searching the major concept retrieves all the synonyms and relevant studies because all the studies have already been organised based on their interventions and linked to the relevant topics.

This register is compiled by systematic searches of major resources (including AMED, BIOSIS, CINAHL, EMBASE, MEDLINE, PsycINFO, PubMed, and registries of clinical trials) and their monthly updates, hand‐searches, grey literature, and conference proceedings (see Group’s Module). There is no language, date, document type, or publication status limitations for inclusion of records into the register.

For previous searches, please see Appendix 1.

1. Reference searching

We inspected references of all identified studies for further relevant studies.

2. Personal contact

We contacted the first author of each included study for information regarding unpublished trials.

1. Extraction

Review authors (HEM, MQA) extracted data from all included studies. In addition, to ensure reliability, SJS independently extracted data from a random sample of these studies, comprising 10% of the total. We attempted to extract data presented only in graphs and figures whenever possible, but included only if two reviewers independently obtain the same result. If studies were multi‐centre, then where possible we extracted data relevant to each. We discussed any disagreement and documented our decisions. If necessary, we attempted to contact authors through an open‐ended request in order to obtain missing information or for clarification. HEM helped clarify issues regarding any remaining problems and we documented these final decisions.

2. Management

1. Binary data

For binary outcomes we calculated a standard estimation of the risk ratio (RR) and its 95% confidence interval (CI), as it has been shown that RR is more intuitive than odds ratios (Boissel 1999); and that odds ratios tend to be interpreted as RR by clinicians (Deeks 2000). Although the number needed to treat for an additional beneficial outcome (NNTB) and the number needed to treat for an additional harmful outcome (NNTH), with their CIs, are intuitively attractive to clinicians, they are problematic to calculate and interpret in meta‐analyses (Hutton 2009). For binary data presented in the 'Summary of findings' table/s we, where possible, calculated illustrative comparative risks.

2. Continuous data

For continuous outcomes we estimated MD between groups. We preferred not to calculate effect size measures (SMD). However if scales of very considerable similarity are used, we presumed there is a small difference in measurement, and we calculated effect size and transform the effect back to the units of one or more of the specific instruments.

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 whereby P values are spuriously low, CIs unduly narrow and statistical significance overestimated (Divine 1992). This causes type I errors (Bland 1997; Gulliford 1999).

Where clustering has been incorporated into the analysis of primary studies, we presented these data as if from a non‐cluster randomised study, but adjusted for the clustering effect.

Where clustering is not accounted for in primary studies, we presented data in a table, with a (*) symbol to indicate the presence of a probable unit of analysis error. We contacted first authors of studies to obtain intra‐class correlation coefficients for their clustered data and adjusted for this by using accepted methods (Gulliford 1999).

We sought statistical advice and have been advised that the binary data from cluster trials 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 intra‐class correlation coefficient (ICC): thus design effect = 1 + (m − 1) * ICC (Donner 2002). If the ICC is not reported we assumed it to be 0.1 (Ukoumunne 1999).

If cluster studies have been appropriately analysed and taken intra‐class correlation coefficients and relevant data documented in the report into account, synthesis with other studies was possible using the generic inverse variance technique.

2. Cross‐over trials

A major concern of cross‐over trials is the carry‐over effect. This 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, participants can differ significantly from their initial state at entry to the second phase, 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 carry‐over and unstable conditions are very likely in severe mental illness, we only used data from the first phase of cross‐over studies.

3. Studies with multiple treatment groups

Where a study involves more than two treatment arms, if relevant, we presented the additional treatment arms in comparisons. If data are binary we simply added these and combined within the two‐by‐two table. If data are continuous we combined data following the formula for combining data in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Where additional treatment arms are not relevant, we did not reproduce these data.

1. Overall loss of credibility

At some degree of loss of follow‐up, data must lose credibility (Xia 2009). We chose that, for any particular outcome, should more than 50% of data be unaccounted for we would 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 addressed this within the 'Summary of findings' table/s by down‐rating quality. Finally, we also downgraded quality within the 'Summary of findings' table/s should the 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, we presented data on a 'once‐randomised‐always‐analyse' basis (an intention‐to‐treat analysis (ITT)). Those leaving the study early were 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 stay in the study ‐ in that particular arm of the trial ‐ was used for those who did not. We undertook a sensitivity analysis testing how prone the primary outcomes are to change when data only from people who complete the study to that point are compared to the intention‐to‐treat analysis using the above assumptions.

3. Continuous

1. Clinical heterogeneity

We considered all included studies initially, without seeing comparison data, to judge clinical heterogeneity. We simply inspected all studies for participants who are clearly outliers or situations that we had not predicted would arise and, where found, discussed such situations or participant groups.

2. Methodological heterogeneity

We considered all included studies initially, without seeing comparison data, to judge methodological heterogeneity. We simply inspected all studies for clearly outlying methods which we had not predicted would arise and discussed any such methodological outliers.

3. Statistical heterogeneity

Economic Summary

Data was summarised according to the Cochrane Campbell Economic Methods Group (Higgins 2011) and a narrative abstract provided for each included study. A table summarising the data was also provided for any studies had they been identified.

We anticipated that most studies would be Grade C level of economic evidence and that we would use data from such studies to calculate a GBP value associated with the outcomes. These approximate values were calculated by (a) using the PSSRU calculation of £338 (weighted average of all adult mental health inpatient bed days) per hospital bed day based in a UK NHS setting (PSSRU 2012) , and (b) assuming that one relapse equals one hospital admission, a median length of stay as 16 days, as per Hospital Episode Statistics 2012 (HES 2012; main speciality ‘adult mental illness’) we utilised results of the effects of the intervention that presented service use data for an adult ward as well as for relapse rates (HES is a data warehouse containing details of all admissions, outpatient appointments and A&E attendances at NHS hospitals in England).

We have not factored any associated costs (including cost and resource use of treatment) prior to the relevant measured outcomes of relapse and hospital discharge. We are using UK NHS PSSRU reference costs of 2012, and therefore present the outcomes in terms of a GBP value found in the comparison data as a proxy measure for relative risk, which is achieved through the assumption of average (median) length of hospital stay (16 days) and average cost per day (£338). The average cost of relapse ‐ based on our assumption that one relapse equals one hospital admission lasting 16 days (338 x 16) ‐ has been calculated at £5,408 per person. From this number, the average cost of relapse has been calculated for both (a) the number of participants alone who experienced relapse in both the intervention or control group (n=relapsed x 5,408) and (b) the entire population at risk of relapse between groups (£ of n=relapsed per group ÷ total N receiving intervention across studies).

The authors wish to emphasise the numerous assumptions that have been made for the purposes of presenting this economic data, specifically at Grade C quality level:

1. The current included studies contributing to the Grade C‐level of quality were undertaken between the years of 1963 to 1999; and, taking this into account ‐

2. The average length of stay and costs have been calculated from current available data, that is, according to 2012 HES costs, from most primarily a UK NHS perspective; and

3. The GBP value data that are presented reflect a proxy measure only; that is, the GBP value of the intervention effect on the measured outcome, and not taking into account any costs or resource use that may likely have been incurred prior to the actual outcome (which includes, but is not limited to, costs and resource use prior to intervention, the intervention itself and post‐intervention up to outcome).

1. Subgroup analyses

2. Investigation of heterogeneity

We reported if inconsistency was high. Firstly, we investigated whether data have been entered correctly. Secondly, if data are correct, we inspected the graph visually and remove outlying studies successively 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 10% of the total weighting, we presented data. If not, we did not pool these data and discussed 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 simply stated hypotheses regarding these for future reviews or versions of this review. We do not anticipate undertaking analyses relating to these.

1. Implication of randomisation

We included trials in a sensitivity analysis if they were described in some way that implies randomisation. For primary outcomes, if the inclusion of these trials did not result in a substantive difference, they remained in the analyses. If their inclusion did result in statistically significant differences, we did not add the data from these lower‐quality studies to the results of the higher‐quality trials, but presented these data within a subcategory.

2. Assumptions for lost binary data

Where assumptions have to be made regarding people lost to follow‐up (see Dealing with missing data), we compared the findings of the primary outcomes when we use our assumption compared with completer data only. If there is a substantial difference, we reported results and discussed them, but continued to employ our assumption.

Where assumptions have to be made regarding missing SD data (see Dealing with missing data), we compared the findings of primary outcomes when we used our assumption compared with complete data only. We undertook a sensitivity analysis to test how prone results are to change when completer data only were compared to the imputed data using the above assumption. If there was a substantial difference, we reported results and discussed them, but continued to employ our assumption.

3. Risk of bias

We analysed the effects of excluding trials that are judged to be at high risk of bias across one or more of the 'Risk of bias' domains (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 did not alter the direction of effect or the precision of the effect estimates substantially, then we included relevant data from these trials.

4. Imputed values

We undertook a sensitivity analysis to assess the effects of including data from trials where we use imputed values for ICC in calculating the design effect in cluster‐randomised trials.

If substantial differences were noted in the direction or precision of effect estimates in any of the sensitivity analyses listed above, we did not pool data from the excluded trials with the other trials contributing to the outcome, but presented them separately.

5. Fixed‐ and random‐effects

We synthesised data using radnom‐effects model; however, we also synthesised data for the primary outcome using a fixed effect model to evaluate whether this alters the significance of the results.

It was expected that several sensitivity analyses could be undertaken within this review. The following hypotheses were be tested:

When compared with placebo, for the primary outcomes of interest (see: Criteria for considering studies for this review), fluphenazine is differentially effective for:

1. Men and women.

2. People who are under 18 years of age, between 18 and 64, or over 65 years of age.

3. People who became ill recently (i.e. acute episode approximately less than one month's duration) as opposed to people who have been ill for a longer duration.

4. People who are given low doses (1‐ 5 mg/day), and those given high doses (over 5 mg/day).

5. People who have schizophrenia diagnosed according to any operational criterion 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.

6. People treated earlier (pre‐1990) and people treated in recent years (1990 to 2006).

We additionally applied all sensitivity analyses to the primary outcomes of this review.

Economic summary

We undertook a sensitivity analysis taking into account both the mean length of hospital stay; the median length of hospital stay (HES 2012); and the associated upper (£376) and lower quartile (£299) ranges of the weighted average cost of all adult mental health inpatient bed days (PSSRU 2012), to investigate how far this affects the direction of the estimated value.