1. Cochrane Schizophrenia Group's trials register (September 2006)

We searched the Cochrane Schizophrenia Group's trials register (September 2006) using the phrase:
[((fluphen* or flufen* or modec* or moditen* or eutimax* or prolixin* or siqualon* or anaten* or dapotum* or decazate* or decafen* or decentan* or fludecate* or lyogen* or lyoridin* or mirenil*) in title, abstract and index fields in REFERENCE) OR (fluphenazin* in interventions field in STUDY)]

The Cochrane Schizophrenia Group’s Trials Register is compiled by systematic searches of major databases, handsearches and conference proceedings (see group module).

1. Cochrane Schizophrenia Group's trials register (May 2012)

The Trial Search Co‐ordinator searched the Cochrane Schizophrenia Group’s Trials Register 15th May 2012 using the same search criteria as our initial 2006 review.

For details of previous search please see Appendix 1.

[((fluphen* or flufen* or modec* or moditen* or eutimax* or prolixin* or siqualon* or anaten* or dapotum* or decazate* or decafen* or decentan* or fludecate* or lyogen* or lyoridin* or mirenil*) in title, abstract and index fields in REFERENCE) OR (fluphenazin* in interventions field in STUDY)]

The Cochrane Schizophrenia Group’s Trials Register is compiled by systematic searches of major databases, handsearches and conference proceedings (see group module).

2. Economic study search of Cochrane Schizophrenia Group Health Economic Database (2013)

For the economic search, we replicated the above strategy in the Cochrane Schizophrenia Group Health Economic Database (CSzGHED) on 23 July 2013. The database of studies relates to cost‐effectiveness of schizophrenia treatments. This database was constructed from systematic searches of four databases: Health Economic Evaluation Database (HEED), National Health Services Health Economic Database (NHS EED), Cost‐Effectiveness Analysis Registry (CEA) and EconLit as well as Cochrane Registry.

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

For this update, HEM and MQA extracted data from included studies. We extracted data presented only in graphs and figures whenever possible. When further information was necessary, we contacted authors of studies in order to obtain missing data or for clarification. We encountered multi‐centre trials, however, we were unable to extract data relevant to each component centre separately; this was because the study was published many years ago, and such data were unavailable (Goldberg 1964).

For the economic analysis had VF and SS found Grade A and B studies (see Types of studies), they would have investigated whether appraisal had already been undertaken by NHS EED using their search tool derived for this purpose. If appraisal had not been undertaken, VF and SS would have applied the NHS EED tool to the data. In this current review, there were only Grade C studies available; therefore, we extracted outcome data directly from the already‐included effectiveness studies. We recognised that much information would be lacking to get results that are both valid and reliable.

2. Management

1. Binary data

For binary outcomes, we calculated 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). For statistically significant results, we used 'Summary of findings' tables to calculate the number needed to treat to provide benefit (NNTB)/to induce harm (NNTH) statistic and its 95% CI.

2. Continuous data

For continuous outcomes, we estimated mean difference (MD) between groups.

1. Cluster trials

Studies increasingly employ 'cluster randomisation' (such as randomisation by clinician or practice), but analysis and pooling of clustered data poses problems. 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, CIs unduly narrow and statistical significance overestimated. This causes type I errors (Bland 1997; Gulliford 1999).

Had we encountered such studies, we would have presented data in a table, with a (*) symbol to indicate the presence of a probable unit of analysis error. In subsequent versions of this review, we will seek to contact first authors of studies to obtain intra‐class correlation coefficients (ICCs) or their clustered data and to adjust for this by using accepted methods (Gulliford 1999). We have sought statistical advice and have been advised that the binary data as presented in a report should be divided by a 'design effect'. This is calculated using the mean number of participants per cluster (m) and the ICC [Design effect = 1+(m‐1)*ICC] (Donner 2002). No cluster trials were identified in this review; however, if in future updates of this review cluster‐randomised studies are identified, where the ICC is not reported it will be assumed to be 0.1 (Ukoumunne 1999).

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 only used data of the first phase of cross‐over studies. This was the case in Millar 1963.

3. Studies with multiple treatment groups

Had we found studies that involved more than two relevant treatment arms, we would have presented the additional treatment arms in comparisons. However, we found no such studies; if, in future updates of this review, if such studies are identified, binary data 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 7.7.3.8 (Combining groups) of the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011). Where the additional treatment arms were 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 60% of data be unaccounted for, we would not reproduce these data or use them within analyses. If, however, more than 60% of those in one arm of a study were lost, but the total loss was less than 40%, we would have marked such data with (*) to indicate that such a result may well be prone to bias.

2. Binary

In the case where attrition for a binary outcome is between 0% and 60% and where these data are not clearly described, had we found such studies, we would have presented data on a 'once‐randomised‐always‐analyse' basis (an intention‐to‐treat analysis). Those leaving the study early would be 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 ‐ would be used for those who did not. We undertook a sensitivity analysis to test how prone the primary outcomes were to change when data only from people who completed the study to that point were 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 clearly outlying people or situations which we had not predicted would arise. When such situations or participant groups arose, we fully discussed these.

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. When such methodological outliers arose, we fully discussed these.

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 ‐ only primary outcomes

2. Investigation of heterogeneity

If inconsistency was high, we have reported this. First, we investigated whether data had been entered correctly. Second, if data were correct, we visually inspected the graph and successively removed outlying studies to see if homogeneity was restored. For this review we decided that should this occur with data contributing to the summary finding of no more than around 10% of the total weighting, we would present data. If not, then we did not pool data and discussed issues. We know of no supporting research for this 10% cut‐off, but we used prediction intervals as an alternative to this unsatisfactory state.

When unanticipated clinical or methodological heterogeneity was obvious, we simply stated hypotheses regarding these for future reviews or versions of this review. We did not anticipate undertaking analyses relating to these.

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.

7. Implication of randomisation

We aimed to include trials in a sensitivity analysis if they were described in some way so as to imply randomisation. For the primary outcomes, we included these studies and if there was no substantive difference when the implied randomised studies were added to those with better description of randomisation, then we entered all data from these studies.

8. Assumptions for lost binary data

Where assumptions had 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/s and when we used data only from people who completed the study to that point. If there was a substantial difference, we reported results and discussed them but continued to employ our assumption.

Where assumptions had to be made regarding missing SDs data (see Dealing with missing data), we compared the findings of the primary outcomes when we used our assumption/s and when we used data only from people who completed the study to that point. A sensitivity analysis was undertaken to test how prone results are to change when completer‐only data only are compared to the imputed data using the above assumption. If there was a substantial difference, we reported results and discussed them.

9. Risk of bias

We analysed the effects of excluding trials that were 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 did not substantially alter the direction of effect or the precision of the effect estimates, then we included data from these trials in the analyses.

10. Imputed values

We also sought to 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 we noted substantial differences 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.

11. Fixed‐effect and random‐effects

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

12. 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.