Primary outcomes

1. Tardive dyskinesia (TD)

   1. No clinically important improvement in the symptoms of individuals, defined as more than 50% improvement on any TD scale ‐ any time period.

2. Adverse effects

   1. No clinically significant extrapyramidal adverse effects ‐ any time period.

Secondary outcomes

1. Tardive dyskinesia (TD)

   1. Any improvement in the symptoms of participants on any TD scale, as opposed to no improvement.

   2. Deterioration in the symptoms of participants, defined as any deleterious change on any TD scale.

   3. Mean change in severity of TD during the trial period.

   4. Mean difference (MD) in severity of TD at the end of the trial.

2. General mental state changes

   1. Deterioration in general psychiatric symptoms (such as delusions and hallucinations) defined as any deleterious change on any scale.

   2. MD in severity of psychiatric symptoms at the end of the trial.

3. Acceptability of the treatment

   1. Acceptability of the intervention to the participant group as measured by numbers of people leaving the trial early.

4. Adverse effects

   1. Use of any anti‐parkinsonism drugs.

   2. Mean score/change in extrapyramidal adverse effects.

   3. Acute dystonia.

5. Other adverse effects, general and specific

6. Hospital and service utilisation outcomes

   1. Hospital admission.

   2. Mean change in days in hospital.

   3. Improvement in hospital status (e.g. change from formal to informal admission status, use of seclusion, level of observation).

7. Economic outcomes

   1. Mean change in total cost of medical and mental health care.

   2. Total indirect and direct costs.

8. Social confidence, social inclusion, social networks or personalised quality of life measures

   1. No significant change in social confidence, social inclusion, social networks or personalised quality of life measures.

   2. Mean score/change in social confidence, social inclusion, social networks or personalised quality of life measures.

9. Behaviour

   1. Clinically significant agitation.

   2. Use of adjunctive medication for sedation.

   3. Aggression to self or others.

10. Cognitive state

    1. No clinically important change.

    2. No change, general and specific.

'Summary of findings' table

We used the GRADE approach to interpret findings (Schünemann 2008) and GRADEpro to import data from Review Manager 5 (RevMan 2014) 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 the available data on all outcomes we rated as important to patient care and decision making. This summary was used to guide our conclusions and recommendations. We selected the following main outcomes for inclusion in the 'Summary of findings' table.

1. Tardive dyskinesia.

   1. Not improved to a clinically important extent.

   2. Deteriorated.

2. Mental state.

   1. Deterioration.

3. Adverse effect.

   1. Any adverse event.

   2. Adverse effects: no clinically significant extrapyramidal adverse effects.

4. Acceptability of treatment.

   1. Leaving the study early.

5. Social confidence, social inclusion, social networks or personalised quality of life measures.*

   1. No significant change in social confidence, social inclusion, social networks or personalised quality of life measures for either recipients of care or carers.

* Outcome designated important to patients. We wished to add perspectives from people's personal experience with TD to the research agenda. A consultation with service users was planned where the previously published version of a review in the Cochrane TD series (Soares‐Weiser 2011; Table 1) and a lay overview of the review gave the foundation for the discussions. The session was planned to provide time to reflect on current research on TD and consider gaps in knowledge. The report is not completed but we will add a link to it within this review but have added one figure showing service‐user expression of frustration concerning this neglected area of research (Figure 2). Informed by the results of the consultation, for this review, we included outcomes important to service users to the summary of findings Table for the main comparison.

Figure 2

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Message from one of the participants of the public and patient involvement consultation of service user perspectives on tardive dyskinesia research.

1. Cochrane Schizophrenia Group’s Register

We searched Cochrane Schizophrenia Group’s Study‐Based Register of Trials on July 16, 2015 and April 26, 2017 using the following string:*Tardive Dyskinesia* in Healthcare Condition Field of Study. In such a study‐based register, searching the major concept retrieves all the synonym keywords and relevant studies because all the studies have already been organised based on their interventions and linked to the relevant topics.The Cochrane Schizophrenia Group’s Register of Trials 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, handsearches, 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.

2. Details of previous electronic searches

See Appendix 1.

1. Reference searching

We searched the reference lists of all included studies to identify more studies.

2. Personal contact

Where necessary, we contacted the first author of each included study for information regarding unpublished trials. We noted the outcome of this contact in the 'Characteristics of included studies' or 'Characteristics of excluded studies' tables.

1. Extraction

For the 2015 update, two review authors (HB and RA) extracted data from all included studies. We discussed any disagreement and documented decisions, requesting that a third review author (KSW) helped clarify issues and we documented these final decisions. We extracted data presented only in graphs and figures whenever possible, but included only if two review authors independently had the same result. We attempted to contact authors through an open‐ended request to obtain missing information or for clarification whenever necessary. If studies were multi‐centre, where possible, we extracted data relevant to each component centre separately.

2. Management

1. Binary data

For binary outcomes, we planned to 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 (ORs) and that ORs tend to be interpreted as RR by clinicians (Deeks 2000).

2. Continuous data

For continuous outcomes, we planned to estimate MD between groups. We preferred not to calculate effect size measures SMD. However, had scales of very considerable similarity been used, we would have presumed there was a small difference in measurement, and we would have calculated effect size and transformed the effect back to the units of one or more of the specific instruments.

1. Cross‐over studies

This area of research commonly uses cross‐over studies where one person is randomly allocated the treatment only to be crossed over to receive the comparison after a designated time. Often a period of drug free 'washout' is used between the interventions to try and ensure that no carry‐over effects of the first intervention remain before commencing the second treatment. The statistical methods for including cross‐over studies in meta‐analyses have developed considerably (Curtin 2002a; Curtin 2002b; Curtin 2002c; Elbourne 2002).

However, there is a clinical problem. Antipsychotic‐induced TD seems to result from the prolonged blockade of specific receptor sites in the brain resulting in changes (dopamine receptor hypersensitivity) that develop over long periods of time and are likely to be slow to reverse. Should an experimental intervention successfully begin the downgrading of the dopamine receptor sites, it seems probable that this downgrading could take a long time to start and, once started, be equally slow to stop. Therefore, it seems entirely feasible that the drugs could have an effect even after they had been expelled from the body within the washout period. In addition, cross‐over studies usually assume that the investigated condition should be stable (Elbourne 2002), and TD is not a stable condition. Consequently, we only used data of the first phase of cross‐over studies in this review because of the nature of the condition under review.

2. 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 intraclass 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, causing type I errors (Bland 1997; Gulliford 1999). We planned to deal with clustering in this review as described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011; Section 16.3).

3. Studies with multiple treatment groups

Where a study involved more than two treatment arms, we would have presented the additional relevant treatment arms in comparisons. We would not have reproduced irrelevant additional treatment arms.

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 in analyses. However, if more than 50% of participants in one arm of a study were lost, but the total loss was less than 50%, we addressed this within the 'Summary of findings' table by downgrading quality. We also downgraded quality within the 'Summary of findings' table should loss be 25% to 50% in total.

2. Binary

In the case where attrition for a binary outcome was between 0% and 50% and where these data were not clearly described, we presented data on a 'once‐randomised‐always‐analyse' basis (an intention‐to‐treat (ITT) analysis). We assumed all participants leaving the study early had no improvement. We undertook a sensitivity analysis testing how prone the primary outcomes were to change by comparing data only from people who completed the study to that point to the ITT 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 and discussed in the text if they arose.

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 in the text if they arose.

3. Statistical heterogeneity

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 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We tried to locate protocols of included randomised trials. Where the protocol was available, we compared outcomes in the protocol and in the published report. Where the protocol was not available, we compared outcomes listed in the methods section of the trial report with the 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 described in Chapter 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 did not plan to use funnel plots for outcomes where there were 10 or fewer studies, or where all studies were of similar sizes. In other cases, where funnel plots were possible, we planned to seek statistical advice in their interpretation.

1. Subgroup analyses

2. Investigation of heterogeneity

We would have reported inconsistency if it appeared high. First, we would have investigated whether data had been entered correctly. Second, if data had been entered correctly, we would have visually inspected the graph and removed outlying studies to see if homogeneity was restored. Should this have occurred with no more than 10% of the data being excluded, we would have presented the data. If not, we would have pooled the data and discussed the issues.

If unanticipated clinical or methodological heterogeneity had been obvious, we would have simply stated hypotheses regarding these for future reviews or updated versions of this review. We prespecified no characteristics of studies that may be associated with heterogeneity except quality of trial method. If no clear association could have been shown by sorting studies by the methodological quality, we would have performed a random‐effects meta‐analysis. Should another characteristic of the studies have been highlighted by the investigation of heterogeneity, perhaps some clinical heterogeneity not hitherto predicted or plausible causes of heterogeneity, we would have discussed these post hoc reasons and analysed and presented the data. However, should the heterogeneity have been substantially unaffected by use of random‐effects meta‐analysis and no other reasons for the heterogeneity have been clear, we would have presented the final data without a meta‐analysis.

1. Implication of randomisation

We aimed to include trials in a sensitivity analysis if they were described in some way as to imply randomisation. For the primary outcomes, we would have 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 would have used all the data from these studies.

2. Assumptions for lost binary data

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

3. Duration of follow‐up

We would have undertaken a third sensitivity analysis to compare primary outcomes between short‐term (less than six weeks), medium‐term (between six weeks and six months) and long‐term (over six months) trials.