Systematic review of interventions for treating or preventing antipsychotic-induced tardive dyskinesia

Interventions being assessed

We aimed to evaluate any intervention used for treating or preventing deterioration of symptoms of antipsychotic-induced TD. There is a vast array of strategies to deal with TD – one review identified over 100. 50 Based on our experience with Cochrane reviews in this research area, we grouped the interventions as follows:

1. vitamins

2. GABA agonists

3. benzodiazepines

4. anticholinergics

5. cholinergics

6. calcium channel blockers

7. non-antipsychotic dopaminergics and noradrenergics

8. specific antipsychotic drugs

9. antipsychotic reduction or cessation including intermittent therapy

10. other interventions, including botulin toxin, insulin or lithium, among others.

We compared interventions with other interventions used to treat or prevent deterioration of symptoms of antipsychotic-induced TD of relevance to people in the NHS, placebo or no intervention.

Design and theoretical/conceptual framework

We included randomised or quasi-randomised controlled trials containing data related to antipsychotic-induced TD, irrespective of language or place of publication. We also considered observational studies for inclusion with the following designs: (1) non-randomised controlled trials, (2) prospective cohort studies with a control group and (3) case–control studies. The systematic reviews and the overview of reviews follow Cochrane design and methodology. 53

Target population

We included studies of adults with a diagnosis of antipsychotic-induced TD (according to any criteria), regardless of the primary condition.

Inclusion/exclusion criteria

We excluded studies in which participants had used antipsychotic drugs for < 3 months or in which the antipsychotic doses had not been stable for at least 1 month4 (except in analyses of antipsychotic switch, withdrawal or reduction). In addition, we excluded studies evaluating children and adolescents, or studies evaluating interventions that are not relevant to the NHS.

We also excluded studies that were > 10 years old that otherwise qualified for inclusion, but reported no useable data and in which:

• we contacted study authors requesting data, but received no reply

• we were unable to contact any of the study authors.

Setting/context

Participants may be receiving treatment in any setting, any country or any health-care system.

Search strategy

We attempted to identify all relevant studies regardless of language or publication status (published, unpublished, in press and in progress).

We searched Cochrane Schizophrenia Group’s Study-Based Register of Trials on 16 July 2015 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 Allied and Complementary Medicine Database (AMED), Bioscience Information Service, Cumulative Index to Nursing and Allied Health Literature (CINAHL), EMBASE, MEDLINE, PsycINFO and PubMed, and registries of clinical trials including CT.Gov, International Standard Randomised Controlled Trial Number (ISRCTN) and the World Health Organization’s International Clinical Trials Registry Platform registries] and their monthly updates, hand-searches, grey literature and conference proceedings (see Group’s Module: http://onlinelibrary.wiley.com/o/cochrane/clabout/articles/SCHIZ/frame.html). There are no language, date, document type or publication status limitations for inclusion of records into the register.

We also searched the Cochrane Dementia and Cognitive Improvement Group’s Register of Trials via the Cochrane Register of Studies Online (CRSO; http://crso.cochrane.org/) on 21 July 2015 using the following string:

DEMENTIA:CC AND (*Tardive* OR *Dyskinesia*):TI,AB,KY.

For more information about this register, see the register’s page (www.medicine.ox.ac.uk/alois/content/about-alois).

Finally, we searched EMBASE, MEDLINE, and PsycINFO for observational studies on 9 January 2017, and details of the search strategy can be found in Appendix 3.

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

As some of the Cochrane reviews have not been updated during the past decade, and systematic reviews methods have changed considerably during this period of time, we also cross-checked all included, awaiting assessment, ongoing and excluded studies in the suite of nine Cochrane reviews on antipsychotic-induced TD.

Selection of studies

We uploaded search results into a web-based system (DistillerSR^®, Evidence Partners, Ottawa, ON, Canada; www.systematic-review.ca). At least two reviewers (out of Antonio Grande, Rosie Asher, Hanna Bergman and Karla Soares-Weiser) independently screened all citations and abstracts identified by the search. Two reviewers (Hanna Bergman and Karla Soares-Weiser) inspected all studies from the nine Cochrane reviews on TD. We obtained full reports for potentially eligible studies and these were independently screened by two review authors (Antonio Grande and Rosie Asher). Disagreements were resolved through discussion with reviewers (Hanna Bergman and Karla Soares-Weiser). We documented justifications for excluding studies from the review.

Data extraction and management

Reviewer Rosie Asher extracted data from all included studies. These were cross-checked by Antonio Grande, and further validated by Hanna Bergman. Any disagreements about data extraction were documented and resolved by consensus. Any potential differences or data entry problems were discussed and decisions documented.

If more than one publication was identified reporting data from the same participants, the main publication was considered as the one with more information or with longer-term outcomes; all others were considered companion publications and data were only collected from these if they had not been provided in the main publication.

We attempted to contact authors in order to obtain missing information or for clarification whenever necessary.

We extracted data into tabular format, with an ‘address’ to each point in the document from which each data element had been taken. This allows future researchers to verify extraction and avoid duplication of effort. All data extracted in this way are fully available to researchers. 54

We extracted data from graphs in GetData Graph Digitizer software version 2.26 (GetData Graph Digitizer, S Federov, Moscow, Russia).

Assessment of risk of bias of the included studies

Rosie Asher classified and Hanna Bergman cross-checked studies as being at low, unclear or high risk of bias, based on domain-specific assessments of risk of bias done using the Cochrane Collaboration’s existing risk-of-bias tool. 53 If the raters disagreed, we made the final rating by consensus, with the involvement of another member of the review group. Where inadequate details of randomisation and other characteristics of trials were provided, we contacted authors of the studies in order to obtain further information.

We incorporated these judgements in assessing limitations in study design for outcomes in the summary-of-findings table (see Table 2).

Risk-of-bias assessment for observational studies was performed by a senior systematic reviewer (Artemisia Kakourou) using a tool that is currently being tested by Cochrane. 59 The following domains were assessed: (1) confounding and selection bias (including confounders measured and addressed, use of matching and methods of adjustment), (2) performance bias (including any considerations of co-intervention), (3) missing data, (4) detection (for cohort studies) or recall bias (for case–control studies) and (5) selective reporting bias.

Data analysis

Variation in efficacy according to characteristics of individuals and studies

Visual inspection of the forest plots was used to evaluate the potential statistical heterogeneity (differences between the true intervention effects in the different studies). Heterogeneity was quantified by estimating the between-study variance τ²- and the I²-statistics,62,63 which measures the percentage of observed variation that can be attributed to true differences between the studies. 62 In forest plots and meta-analyses, τ² was estimated using the restricted maximum likelihood estimator,64 whereas its 95% CIs were estimated by the Q-profile method. 65

Summarising and interpreting results

We used the Grading of Recommendations, Assessment Development and Evaluation (GRADE) approach66–68 to assess the evidence of the various interventions. For all NHS-prioritised interventions and outcomes, we have presented a summary-of-findings table (see Table 2) based on the GRADE results.

Investigation of heterogeneity

We considered a degree of heterogeneity inevitable, and hence we planned to explore only important heterogeneity (I² ≥ 75%) using metaregression or subgroup analyses for the effect modifiers: (1) risk of bias in the different study designs; (2) length of antipsychotic use; (3) underlying disease (dementia or schizophrenia); (4) sex/age; (4) type of treatment use, specifically first- or second-generation antipsychotics; and (5) whether or not other concomitant drug interventions were used. Analyses were homogeneous with no important heterogeneity (I² ≥ 75%).

Sensitivity analyses

To ensure that our imputations did not bias our results, we planned to restrict the analyses to studies considered to be at low, and low or unclear risk of selection and detection bias. However, all studies were at unclear risk of selection and detection bias, and we did not carry out this restricted analysis.

Planning of future studies

To judge the sufficiency of the evidence for the comparison of switching to any FGAs versus any SGAs, we calculated the conditional power of an updated meta-analysis for the particular comparison as described in Sutton et al. 69 We further investigated whether or not hypothetical future studies are likely to alter the meta-analysis results using extended funnel plots. 70 Given the small number of studies available, a fixed-effect inverse-variance meta-analysis model was assumed for this analysis.

Power of an updated meta-analysis based on simulations of new studies

We estimated the power of an updated meta-analysis through the simulation of (sufficiently similar) hypothetical ‘new’ studies and calculating the proportion of times that the meta-analysis result would be statistically significant. 69 The event rate was assumed to be equal to that observed, and the number of simulations on which we estimated power was 1000.

Extended funnel plots

We further assessed whether or not future studies are likely to alter the meta-analysis result via extended funnel plots. 70 A colour code appended in conventional funnel plots illustrates where the result of an updated meta-analysis would lie, depending on the effect estimate and the standard error of a hypothetical new study to be added to the evidence base.

Studies included in overview

Studies excluded from this review

Randomised controlled trials

Detailed risk-of-bias assessments of all included studies are in Appendix 7.

Overall risk of bias for the included studies was rated as being high to unclear. It is astonishing to note that only one of the studies was rated as being free from risk of selection bias. 137 The remaining trials reported inadequately on randomisation and allocation concealment. Furthermore, seven studies were rated as being at high risk of performance bias and 13 were rated as being of unclear risk. This was mainly a result of trials being open label, or poor reporting of blinding. One study was rated as being at high risk of detection bias and 18 were rated as being of unclear risk; this is mainly because of poor reporting. Ten studies were rated as being at high risk of attrition bias (because of high or imbalanced dropout rates) and two at unclear risk. Thirteen studies were rated as being at high risk of reporting bias as a result of selective reporting of outcome measures, and 12 were rated at an unclear risk. We sought information from study authors where risk of bias was rated as being unclear.

As a post hoc comparison, we evaluated risk of bias in studies published within the past 20 years (1997–2011) compared with older studies published until 1996 (Figure 3). We found that methodological quality had improved only marginally over time on most risk-of-bias categories (selection, performance, attrition and reporting biases). There was no change for detection bias, and other bias had improved over time.

FIGURE 3.

Old (1973–96) vs. new (1997–2011) studies risk of bias.

Observational studies

Detailed risk-of-bias assessments of all included studies are in Appendix 3 (see Table 4).

Overall risk of bias for the included observational studies was rated as being high to unclear. None of the observational studies was free from risk of selection bias, one study reported controlling for baseline confounding, and three studies reported a reliable outcome assessment. For the domains of incomplete outcome data and selective outcome reporting, none of the studies reported mechanisms to avoid bias (Figure 4).

FIGURE 4.

Overview of included observational studies risk of bias.

Comparison 1: reduced dose of antipsychotics versus continuing antipsychotics

Two very small randomised trials97,98 conducted with schizophrenia or schizoaffective disorder inpatients and outpatients in the UK and USA reported on reduced doses compared with standard doses of flupentixol and fluphenazine. Evidence was of very low quality (see Table 2); therefore, we are uncertain of the results:

• TD symptoms improved to a clinically important extent for significantly more people allocated to antipsychotic reduction than antipsychotic continuation after 44–48 weeks (very low-quality evidence, two RCTs,97,98 17 people; RR 0.42, 95% CI 0.17 to 1.04; I² = 0%).

• There was no significant difference in deterioration of TD symptoms at 44–48 weeks (very low-quality evidence, two RCTs,97,98 17 people; RR 0.61, 95% CI 0.11 to 3.31; I² = 33%).

• The number relapsing was not significantly different in the antipsychotic reduction group (1/4) and the antipsychotic maintenance group (0/4) at 44–48 weeks (one RCT,97 eight people; RR 3.00, 95% CI 0.16 to 57.36).

• The number of people leaving the study early was not significantly different in the antipsychotic reduction group (1/4) and the antipsychotic maintenance group (3/4) (very low-quality evidence, one RCT,97 eight people; RR 0.33, 95% CI 0.06 to 1.99).

For this comparison there were no studies that reported on adverse events or social confidence, social inclusion, social networks or personalised quality of life.

Comparison 2: switch to a different antipsychotic versus antipsychotic withdrawal (with placebo)

Two small randomised trials101,108 conducted with schizophrenic inpatients in Canada and Taiwan reported on switching to risperidone or haloperidol compared with placebo and withdrawing antipsychotics. Evidence was rated as being of low to very low quality (see Table 2); therefore, we are uncertain of the results:

• TD symptoms improved to a clinically important extent for significantly more people allocated to antipsychotic switch to risperidone than those allocated to placebo at 12 weeks (low-quality evidence, one RCT,105–109 42 people; RR 0.45, CI 0.23 to 0.89).

• There was no significant difference in the use of antiparkinsonism drugs between switching to risperidone or haloperidol compared with placebo at 8–12 weeks (two comparisons from one RCT,99–103 48 people; RR 2.08, CI 0.74 to 5.86; I² = 0%).

• General mental state was measured using the continuous BPRS scale (see Some specific outcomes). There was no significant difference between switching to risperidone compared with placebo on the average end-point score of the BPRS at 12 weeks (one RCT,105–109 42 people; MD –4.30, CI –10.48 to 1.88).

• Using antipsychotics did not significantly increase the chances of a person leaving the study early at 12 weeks (very low-quality evidence, one RCT,105–109 50 people; RR 0.60, CI 0.16 to 2.25).

For this comparison there were no studies that reported on deterioration of TD symptoms or social confidence, social inclusion, social networks or personalised quality of life.

Comparison 3a: switch to one antipsychotic versus switch to a different antipsychotic

Six small randomised trials101,104,110,112,115,117 of inpatients and outpatients with schizophrenia and schizoaffective disorder conducted in in Canada, South Africa, Taiwan and the USA reported on switching to a SGA (amisulpride, clozapine, olanzapine, risperidone, quetiapine, ziprasidone) compared with switching to a different antipsychotic, either a FGA (haloperidol, unspecified FGA) or another SGA. Evidence was rated as being of low to very low quality (see Table 2); therefore, we are uncertain of the results:

• There were no significant differences on clinically important improvement in TD symptoms at 6 months between quetiapine and haloperidol (low-quality evidence, one RCT,110,111 45 people; RR 0.80, 95% CI 0.52 to 1.22) or between olanzapine and risperidone (very low-quality evidence, one RCT,115,116 60 people; RR 1.25, 95% CI 0.82 to 1.90).

• The number of people in need of antiparkinsonism drugs was significantly lower in the group allocated to quetiapine than in the group allocated to haloperidol (one RCT,110,111 45 people; RR 0.45, 95% CI 0.21 to 0.96), but there was no significant difference between the groups allocated to risperidone or haloperidol (one RCT,99–103 37 people; RR 0.68, 95% CI 0.34 to 1.35).

• Extrapyramidal symptoms at 6 months, as measured by the ESRS, were lower among participants on olanzapine than in those on risperidone (one RCT,115,116 60 people; MD –0.70, 95% CI –1.33 to –0.07), but there was no significant difference in extrapyramidal symptoms at 6 months, as measured by on SAS, at 6 months between participants on olanzapine and those receiving amisulpride (one RCT,112–114 54 people; MD –0.35, 95% CI –2.44 to 1.74).

• There were no significant differences in general adverse events at 6 months, as measured on the UKU scale, between patients on olanzapine (one RCT,112–114 53 people; MD 0.08, 95% CI –1.85 to 2.01) or amisulpride (one RCT,112–114 53 people; MD –0.55, 95% CI –2.33 to 1.23) and thos receiving an unspecified FGA, or between those on olanzapine and those on amisulpride (one RCT,112–114 54 people; MD 0.63, 95% CI –0.93 to 2.19).

• There were no significant differences in deterioration of mental state at 1 year between patients on quetiapine and those on haloperidol (one RCT,110,111 45 people; RR 1.83, 95% CI 0.62 to 5.39), or at 6 months between patients on olanzapine and those on risperidone (one RCT,115,116 60 people; RR 1.00, 95% CI 0.15 to 6.64) or at 6 months, measured on the BPRS, between patients on olanzapine and those on amisulpride (one RCT,112–114 54 people; MD 1.32, 95% CI –1.94 to 4.58).

• People allocated to olanzapine were less likely to leave the study early, that is after 6–18 months, than those allocated to risperidone (two RCTs,115–118 170 people; RR 0.73, 95% CI 0.57 to 0.95; I² = 0%) or quetiapine (one RCT,117,118 116 people; RR 0.70, 95% CI 0.54 to 0.90).

• There were no significant differences at 6 months to 1 year in acceptability of treatment, defined as not leaving the study early, between patients receiving olanzapine or amisulpride and those receiving an unspecified FGA,112–114 or between those receiving clozapine or quetiapine and those receiving haloperidol,104,110,111 or between patients receiving olanzapine and those receiving amisulpride112–114 or ziprasidone,117,118 or between those on quetiapine and those on risperidone or ziprasidone,117,118 or between patients on ziprasidone and those on risperidone. 117,118

For this comparison there were no studies that reported on deterioration of TD symptoms or social confidence, social inclusion, social networks or personalised quality of life.

Comparison 3b: specific antipsychotic versus other drug – haloperidol versus tetrabenazine

A very small randomised trial96 conducted with psychiatric inpatients in the USA compared haloperidol with tetrabenazine. The evidence was rated as being of very low quality (see Table 2); therefore, we are uncertain of the results:

• There was no significant difference in clinically important improvement in TD symptoms at 18 weeks between patients receiving haloperidol and those receiving tetrabenazine (very low-quality evidence, one RCT,96 13 people; RR 1.07, 95% CI 0.51 to 2.23).

• There was no significant difference in deterioration of TD symptoms at 18 weeks between patients receiving haloperidol and those receiving tetrabenazine (very low-quality evidence, one RCT,96 13 people; RR 0.86, 95% CI 0.07 to 10.96).

• At 18 weeks there was no significant difference in the proportion of participants who had left the study early between the haloperidol (2/7 participants) and tetrabenazine groups (0/6 participants) (very low-quality evidence, one RCT,96 13 people; RR 4.38, 95% CI 0.25 to 76.54).

For this comparison there were no studies that reported on adverse events, mental state or on social confidence, social inclusion, social networks or personalised quality of life.

Comparison 4: withdrawal of anticholinergics versus continuation of anticholinergics

A very small randomised trial119 conducted in schizophrenia patients in Germany compared stopping biperiden after 1 week or after 4 weeks. The evidence was rated as being of very low quality (see Table 2); therefore, we are uncertain of the results:

• There was no significant difference at 7 weeks in the proportion of people leaving the study early between those withdrawn from anticholinergic therapy (1/6 participants) and those who continues (0/4 participants) (very low-quality evidence, one RCT,119 10 people; RR 2.14, 95% CI 0.11 to 42.52).

For this comparison there were no studies with useable data on clinically important improvement or deterioration of TD symptoms, adverse events, mental state or on social confidence, social inclusion, social networks or personalised quality of life.

Comparison 5: benzodiazepines versus placebo, treatment as usual or active placebo (with antipsychotic management)

Four small randomised trials75,89,120,122 conducted with psychiatric inpatients and outpatients in China and the USA compared diazepam or clonazepam and antipsychotic continuation with placebo, TAU or phenobarbital as active placebo and antipsychotic continuation. The evidence was rated as being of very low quality (see Table 2); therefore, we are uncertain of the results:

• There was no significant difference in ‘no clinically important improvement of TD symptoms’ at 5–10 weeks between patients on benzodiazepines and those receiving placebo or no treatment (very low-quality evidence, two RCTs,89,121,122 32 people; RR 1.12, 95% CI 0.60 to 2.09; I² = 14%). One trial found that clonazepam was more beneficial than phenobarbital (as active placebo) at 2 weeks (very low-quality evidence, one RCT,120 21 people; RR 0.44, 95% CI 0.20 to 0.96).

• There was no significant difference in deterioration of TD symptoms at 5–10 weeks (very low-quality evidence, two RCTs,89,121,122 30 people; RR 1.48, 95% CI 0.22 to 9.82; I² = 19%).

• One study reported on mental state average end-point scores using the BPRS scale and noted no difference between the diazepam and TAU groups at 10 weeks (one RCT,89 11 people; MD –0.50, 95% CI –13.83 to 12.83).

• One trial found no significant difference in the number of participants experiencing adverse events after 2 weeks’ treatment with clonazepam or phenobarbital (as active placebo) (very low-quality evidence, one RCT,120 21 people; RR 1.53, 95% CI 0.97 to 2.41). All participants allocated to clozapine (10) and 7 out of 11 participants allocated to phenobarbital experienced an adverse event.

• Three studies reported that no participants left the study early. 75,120–122 One study reported that 2 out of 33 participants allocated to diazepam, but none (out of 23) allocated to TAU, left the study early and, subsequently, found no significant difference between the two groups at 10 weeks (very low-quality evidence, one RCT,89 56 people; RR 2.73, 95% CI 0.15 to 48.04).

For this comparison there were no studies that reported on social confidence, social inclusion, social networks or personalised quality of life.

Comparison 6: vitamin E versus placebo (with antipsychotic management)

Thirteen randomised trials90–95,123,127–130,137,138 in psychiatric inpatients and outpatients in China (one study138), Hong Kong (one study94), Israel (two studies90,91), India (one study127), Switzerland (one study95), the UK (one study130) and the USA (six studies92,93,123–126,128,129,131–137) reported on vitamin E (gamma-tocopherol) and antipsychotic continuation compared with placebo and antipsychotic continuation. The evidence was rated as being of low to very low quality (see Table 2); therefore, we are uncertain of the results. After up to 1 year:

• There was no significant difference between the vitamin E and placebo groups in the numbers of patients experiencing no clinically important improvement in TD symptoms (low-quality evidence, six RCTs,93–95,123–126,130–137 264 people; RR 0.95, 95% CI 0.89 to 1.01; I² = 0%).

• The number of participants who showed deterioration of TD symptoms was significantly lower in the vitamin E group than in the placebo group (low-quality evidence, five RCTs,93–95,123–126,130 85 people; RR 0.23, 95% CI 0.07 to 0.76; I² = 0%)

• One study131–137 measured adverse events (extrapyramidal symptoms) using the SAS and found no significant difference between the vitamin E and placebo groups (very low-quality evidence, 104 people; MD 1.10, 95% CI –1.02 to 3.22).

• There was no significant difference in the incidence of any adverse event (very low-quality evidence, nine RCTs,90–93,95,123–128,130 205 people; RR 1.21, 95% CI 0.35 to 4.15; I² = 0%).

• There was no significant difference in mental state, as measured by the BPRS, between vitamin E and placebo groups (three RCTs,127,129,131–137 165 people; MD –0.20, 95% CI –3.21 to 2.82; I² = 38%).

• There was no significant difference in acceptability of treatment (leaving the study early) [very low-quality evidence, medium term (overall ≈20% loss to follow-up), eight RCTs,90–92,94,123–126,128,129,138 232 people; RR 1.07, 95% CI 0.64 to 1.80; I² = 0%].

For this comparison there were no studies that reported on social inclusion, social networks or personalised quality of life.

Comparison 7: buspirone versus placebo (with antipsychotic management)

One small randomised trial,78 conducted with psychiatric inpatients in China, reported on buspirone and antipsychotic continuation compared with placebo and antipsychotic continuation. Evidence was rated as being of low quality (see Table 2); therefore, we are uncertain of the results:

• The number of participants reporting clinically important improvement in TD symptoms after 6 weeks was signficicantly higher in the buspirone group than in the placebo group (low-quality evidence, one RCT,78 42 people; RR 0.53, 95% CI 0.33 to 0.84).

• Acceptability of treatment, measured by the number of participants leaving the study early, could not be estimated, as the included study did not report any events.

For this comparison there were no studies that reported on deterioration of TD symptoms, adverse events, mental state or on social confidence, social inclusion, social networks or personalised quality of life.

Comparison 8: hypnosis and relaxation versus treatment as usual (with antipsychotic management)

One very small randomised trial,139 conducted with psychiatric inpatients in the USA, reported on hypnosis or relaxation and antipsychotic continuation compared with TAU and antipsychotic continuation. The evidence was rated as being of very low quality (see Table 2); therefore, we are uncertain of the results:

• Clinically important improvement in TD symptoms after eight sessions was reported by significantly more participants in the hypnosis or relaxation group than in the TAU group (very low-quality evidence, one RCT,139 15 people; RR 0.45, 95% CI 0.21 to 0.94).

• There was no significant difference in deterioration of TD symptoms after eight sessions between the hypnosis or relaxation group and the TAU group (very low-quality evidence, one RCT,139 15 people; RR 0.18, 95% CI 0.01 to 3.81).

• Acceptability of treatment (leaving the study early) could not be estimated, as the included study reported no events.

For this comparison there were no studies that reported on adverse events, mental state or on social confidence, social inclusion, social networks or personalised quality of life.

Risk of bias

We planned to restrict the analyses to studies considered to be at low, and low or unclear, risk of selection and detection bias. None of the included studies was rated as being at a low risk of both selection and detection bias. Studies were rated as being either at an unclear risk of bias or at a low and unclear risk (see Appendix 7, Table 13), except Glover,139 which was the only study rated as being at high risk of selection bias. Glover139 was the only study that investigated hypnosis and relaxation.

Imputed values

We would have undertaken a sensitivity analysis to assess the effects of including data from cluster randomised trials in which we used imputed values for the intracluster correlation coefficient in calculating the design effect. However, we identified no cluster randomised trials for inclusion.

No clinical improvement of tardive dyskinesia symptoms

Only one study110 comparing ‘switch to FGA’ with ‘switch to SGA’ reported the outcome ‘no clinical improvement’. The odds ratio (OR) comparing these two treatments was 1.96 (95% CI 0.56 to 6.92), indicating an insignificant advantage of ‘switch to SGA’ compared with ‘switch to FGA’. The wide CI surrounding the effect estimate suggests that the existing evidence might not be adequate to conclude which of the two interventions is more effective. The power curve in Figure 5 shows the power of an updated meta-analysis considering that a new study with sample size indicated in the horizontal axis is added to the evidence base. The power of a meta-analysis including a new study with a small sample size would remain low (e.g. we would achieve a power of < 40% randomising 100 more patients). To achieve a power of 80% for the meta-analysis, a new study with a total sample size of 800 patients would need to be designed and included in the meta-analysis model. The extended funnel plot could not be drawn given the availability of a single study.

FIGURE 5.

Power curves with 95% CIs for the outcome ‘no clinical improvement of TD symptoms’ for the comparison ‘switch to FGA’ vs. ‘switch to SGA’.

Total discontinuation rates

Three studies comparing ‘switch to FGA’ to ‘switch to SGA’ and reporting ‘total discontinuation rates’ were available. The resulting OR was 0.54 (95% CI 0.21 to 1.42) in favour of a ‘switch to FGA’ using the fixed-effect inverse-variance meta-analysis model. For a new study to make an important contribution to the existing evidence by rendering the power of the meta-analysis 80%, it would have to have a total sample size of ≥ 1000 patients (Figure 6). The implications of including a hypothetical new study in the meta-analysis are illustrated in the extended funnel plot of Figure 7. The inclusion of an additional study lying in the left-hand light-green region of Figure 7 would result in the updated meta-analysis showing a significant result in favour of a ‘switch to FGA’. As none of the existing studies lies in this region, it is considered unlikely that a new trial will change meta-analysis conclusions. The possibility that a meta-analysis would change the inference in favour of a ‘switch to SGA’ is even smaller, as it would require the inclusion of a study with a very small standard error (smaller than 0.1) demonstrating a favoured outcome for the particular treatment. Thus, despite the fact that meta-analysis is inconclusive, it is not likely that a new study would change its conclusions given that its sample size is not substantially large.

FIGURE 6.

Power curves with 95% CIs for the outcome ‘total discontinuation rates’ for the comparison ‘switch to FGA’ vs. ‘switch to SGA’.

FIGURE 7.

Extended funnel plot for the outcome ‘total discontinuation rates’ for the comparison ‘switch to FGA’ vs. ‘switch to SGA’: contours for impact of a new study.

The search

This area of research does not seem to be active. We have identified additional data, but most trials pre-date the year 2000, with only six studies (of prioritised interventions) published between 2000 and 2011. Possible explanations for this include lack of concern with TD in the research community, discouragement regarding the possibility of identifying effective treatments, or, more positively, decreased emergence of the problem in research-active communities because of more thoughtful use of antipsychotic drugs.

In addition to RCTs, we identified eight small prospective cohort studies that reported on efficacy of interventions (mostly antipsychotics) for the treatment of TD.

Few data

The great majority of studies testing treatments for people with TD are short and very small. This whole review of many comparisons shows that only hundreds, not thousands, of people have been randomised, and no one with dementia and TD. Any effect of treatment is likely to be subtle and so substantial sample sizes are needed to show differences with acceptable confidence. This also applies to observational studies, in which eight prospective studies reported on 200 patients with TD.

Many outcomes were not measured at all by included studies. We may have been overambitious in hoping for some of these outcomes in TD trials, but simple reporting of social impact and quality of life does not seem unreasonable, and is of particular interest to patients and carers.

Outcomes

Completeness

We excluded 22 studies of prioritised interventions published between 1971 and 2004 because they did not report data that could be used in the review. We contacted the study authors wherever possible, but no further information was available.

As part of this work, the service user consultation participants highlighted their preferred outcomes (Box 2). These largely correlated with the perspectives of the clinicians and reviewers – listing clear, clinically meaningful effects on TD, adverse effects or leaving the study early – as being of importance. The consultation added the outcome of some measure of social confidence/inclusion/networks and/or quality of life. There were no data for the measure of social confidence/inclusion/networks and/or quality of life, but in reality all others were incomplete – perhaps with the exception of vitamin E. The large trials – or enough small trials on the same topic – have just not been undertaken. The difficulty of carrying out randomised studies in this area should not be underestimated. However, time and time again pioneering triallists have proved that it is possible.

Another problem is that there seems to be little evidence of collaboration; no two trials are the same. With collaborative effort we could have enough people randomised across time to have answers to some practical issues. Currently, we cannot even be confident that dose reduction really helps. Of course, researchers will always be attracted to try the next compound, but this overview illustrates that there are enough ‘loose ends’ in the past work regarding entirely practical interventions to encourage some large collaborative efforts in randomisation.

This overview – and the clear incompleteness of the data on this old, well-recognised condition – also, we think, serves to encourage some consideration about trial design. Past work does not serve people with TD particularly well. In the 30 years of, largely, pilot studies, trial methodology within mental health has evolved, with larger pragmatic trials becoming more prevalent. The service user consultation has provided outcomes fitting with a pragmatic randomised trial design (see Box 2). This trial, which need not be that expensive, could be undertaken wherever TD is a concern and need not be constrained to the somewhat fragmented services often seen in ‘Western’ medicine.

Applicability

Most trials in this review were hospital based, but nevertheless featured the type of patients likely to be encountered in everyday care. Many of the interventions are readily accessible. The outcomes pose a greater problem of applicability. Scale-derived findings may be applicable, but even the original measures do not really describe how findings are relevant to day-to-day care. Whenever possible, we have extracted outcomes such as ‘improved/not improved to a clinically important extent’. For the degree of importance of the change, we have to trust the judgement of triallists from a wide variety of backgrounds and care cultures.

Missing studies

We have made every effort to identify relevant trials. However, these studies are all small and it is likely that we have failed to identify other studies of limited power. It is likely that such studies would also not be in favour of the intervention investigated; if they had been so, it is more likely that they would have been published in accessible literature. We do not, however, think it likely that we have failed to identify large relevant studies.

Introducing bias

We have tried to be balanced in our appraisal of the evidence, but could have inadvertently introduced bias. We have tried to intentionally add bias towards treatments useful within the NHS, but have found no other innovations that really hold promise. We welcome comments or criticisms. We tried to ensure that searches for trials were wide-ranging, covering as many data sources as possible, but we still could easily have missed studies. We think it unlikely, however, that we would have missed large trials with important outcomes.

It is an unavoidable fact that many of the authors were familiar with this literature for many years before undertaking this full overview. However, the PPI exercise was undertaken, largely, blind to the results of the Cochrane reviews and in time to pre-date (and therefore direct) the construction of the summary-of-findings tables.

Use of crossover design

Triallists find it difficult to identify people with both TD and schizophrenia to participate in trials. 95 Randomised crossover designs are used in the hope of improving the power of the study to find outcomes of interest. In this design, participants are initially randomised to one of the experimental interventions and then, at a prespecified time, cross over to the treatment that they did not receive at first. Conditions with a more stable time course than TD are better suited for crossover studies. 164

The carry-over effect introduces additional difficulties. Many substances used to treat TD may well persist in the body for long periods after discontinuation; unless crossover studies include a mid-study washout period (which ensure that the participant is free from the inital treatment before starting the next arm of the study), any effect of treatment may continue into the second, placebo, arm of the trial – the ‘carry-over effect’. In addition, carry-over may involve the regrowth or retreat of neuroreceptors. This slow rebalancing, if started, could continue long after all traces of intervention drugs are gone, so the physiological half-life of the experimental treatment may not be the only variable to consider when thinking through the issues of carry-over. TD is also an unstable condition, and people with TD may not remain compliant with medication. All these factors make the arguments for not using crossover methodology strong, despite the initial attraction. 164–166

Planning of future studies

The relative effectiveness and safety of a ‘switch to FGA’ compared with a ‘switch to SGA’ is considered to be of great importance in terms of deterioration of symptoms of antipsychotic-induced TD. However, only a handful of studies examined that particular comparison – one and three studies for the outcomes ‘no clinical improvement of TD symptoms’ and ‘total discontinuation rates’ were available, respectively. NMA did not offer any additional advantage or further insight on the ‘switch to FGA versus switch to SGA’ comparison; no indirect evidence feeding this comparison existed and, thus, the network estimates were identical to their pairwise meta-analysis counterparts (see Appendix 4).

Figures 6 and 7 imply that, although the meta-analysis can be considered reasonably robust to the addition of new studies with a small sample size, conclusions might change if large studies are added. If further studies are to be designed and conducted, a total sample size of 1000 patients would give a good prospect of reaching a conclusive result for both outcomes. Decisions on whether or not new studies are to be conducted should take into account the feasibility of such a sample size. In any case, informed and evidence-based decisions would require the systematic assessment of existing evidence before embarking into new research. 167,168

Outcomes

• Measure the extent to which service users feel informed about their treatment and the possibility of adverse effects such as TD.

• Measure patients’ access to quality information about TD.

• For people who have developed lifelong TD as a result of taking medication, to what extent do organisations/individuals take responsibility? Are service users supported or encouraged to seek accountability?

• Measuring clinician awareness of TD as a side effect of psychiatric medications.

• Measuring the level of reporting with regard to incidences of TD.

• Measuring social confidence, social inclusion, social networks, personalised quality-of-life measures and employment.

• Measuring public awareness of TD (Figure 10).

FIGURE 10.

Key outcomes of interest.

Future research

• Understanding the causal mechanisms that result in TD as well as developing methods to assess individuals’ risk of developing TD as a result of medication consumption.

• Understanding the prevalence of medication-related TD.

• What psychological therapies are effective in managing the symptoms of TD?

• Is peer support effective in managing the symptoms of TD?

It is important to note that the above list of recommendations reflects the context within which they were suggested, either as additional outcomes to be considered within future TD research or as future research projects.

However, it was clear that almost all of the recommendations relating to ‘outcomes’ could equally be important areas of interest for future research in and of themselves. Moreover, some studies that are not solely focused on ascertaining the prevalence of medication-related TD may be improved by including an outcome measure to understand the prevalence of TD among their participant group.

Megan Rees

I really enjoyed the session and given I had little prior experience of working in the field of TD, I found the group’s discussions very enlightening.

When it came to the most important outcomes for research, attendees unanimously supported the goals of research included in the Cochrane review. Preventing and treating the symptoms of TD were, for obvious reasons, a key concern of service users. However, attendees were quick to highlight important outcomes that appeared to be missing from the research. One such ‘missing’ outcome referred to as ‘informed prescribing’ particularly struck me. After watching a rather graphic video of the effects of TD, there was a palpable sense of injustice. A number of attendees wondered how many people who are prescribed antipsychotics are made aware of such severe side effects and expressed how important it is that service users are given the opportunity to make an informed choice before taking medication. If, as the review found, we are unable to effectively prevent or treat this particular side effect, some emphasis must be placed on giving service users enough information that they are able to essentially own their decisions when it comes to medication. This would at least mitigate against the feeling of powerlessness and subjugation that many people feel when they experience medication side effects that they were not initially made aware of.

The group made a number of highly insightful suggestions throughout the day but it was their focus on outcomes relating to empowerment and autonomy that were so striking given that these outcomes were conspicuous by their absence in the research that has taken place so far.

Dawn Marie-Walker

I really enjoyed the session, and was reassured by the passionate responses from the service users that this research is really worthwhile.

Since being part of this work, one of my PhD [doctor of philosophy] students from Saudi Arabia has had a nephew with severe mental health difficulties. His nephew has been given vast amounts of medication, including anti psychotics, and what has resulted, from the description of my student, as TD.

Although initially my colleagues and I thought TD was a declining problem (due to having far more knowledge about it and medication regimes), it appears that it is still a grave problem internationally. Also in dementia, where antipsychotics are prescribed off licence, it may also be more of a problem.

Ruth Sayers

I appreciated the openness and engagement of the people who attended the workshop. Individual accounts of experiencing TD differed considerably, but all showed clearly the level of distress, vulnerability and stigmatisation that can be associated with tardive dyskinesia. Lack of awareness of TD was compared with the growing awareness of Tourette’s, and the efforts being made to de-stigmatise that condition, especially with young people.

Several felt angry that they had not been given sufficient information at the time of prescribing about side effects of antipsychotics to make an informed choice – to enable them to balance the risks for themselves. There were many questions raised about how much was known, and how much doctors know, or reported, about TD, and therefore whether the actual prevalence is known, in the UK or elsewhere. Suggestions about what might help people included greater knowledge and an opportunity to avoid TD, and personal and social support to cope with the stigmatising condition. I hope that the workshop raised some important issues for further exploration.

EMBASE

Date searched: 9 January 2017.

Date range searched: 1974 to 2017 week 2.

Number of results: 696.

Ovid MEDLINE In-Process & Other Non-Indexed Citations and Ovid MEDLINE

Date searched: 9 January 2017.

Date range searched: 1946 to 9 January 2017.

Number of results: 2072.

PubMed

Date searched: 9 January 2016.

Date range searched: up to 9 January 2017.

Number of results: 377.

PsycINFO

Date searched: 9 January 2017.

Date range searched: 1806 to January week 1 2017.

Number of results: 167.

Included studies

Description of excluded studies

Thirty studies (31 references) were excluded at full-text screening. Reasons for exclusion were: not an observational study (seven studies), observational study with no control group (19 studies), study only measuring prevalence (three studies) or no treatment was provided (one study). Table 5 shows full references and reasons for exclusion per study.

Criteria for considering studies for this review

Measures of treatment effect

Methods for direct treatment comparisons

Initially, standard pairwise meta-analysis was performed for all pairwise comparisons with at least two studies using the random-effects inverse variance model in Stata. 175

Methods for indirect and mixed comparisons

Network meta-analysis integrates direct and indirect evidence for each pairwise comparison to derive relative treatment effects between all competing treatments. We intended to perform NMA using the methodology of multivariate meta-analysis in which different treatment comparisons are handled as different outcomes using the ‘network’ package (which includes the ‘mvmeta’ command) in Stata. 156,176 As a result of the substantial number of treatment nodes and the version of Stata available, however, analysis using the ‘network’ package was not feasible and we performed NMA using graph theoretical methods as described in Rücker. 177,178 To this aim, we used the ‘netmeta’ package in R. 179 We also used available Stata routines to present the evidence base and to illustrate the results. 180 We produced a plot to present jointly the relative ranking of treatments for ‘no clinical improvement’ and ‘total discontinuation rates’, and we used a hierarchical cluster analysis to group interventions in meaningful subsets. 180

Assessment of statistical heterogeneity

Measures and tests for heterogeneity

Between-study variance τ² was estimated in both pairwise and NMA using the DerSimonian and Laird estimator. 175 We assessed statistical heterogeneity based on the magnitude of the estimated parameter. We also compared the magnitude of τ² with empirical distributions derived in Turner et al. 181 and Rhodes et al. 182

Sensitivity analysis

We planned to perform the following four sensitivity analyses to ensure the robustness of the NMA results:

1. analysis restricted to studies rated as being at low risk of selection bias

2. analysis restricted to studies rated as being at low or unclear risk of selection bias

3. analysis restricted to studies rated as being at low risk of detection bias

4. analysis restricted to studies rated as being at low or unclear risk of detection bias.

Summary

The primary outcome (no clinical improvement of TD symptoms) was reported in 46 studies (one three-arm study and 45 two-arm studies), including 1560 patients. Total discontinuation rates were reported in 78 studies (one four-arm study, one three-arm study and 76 two-arm studies) with 2965 patients. The number of studies and the number of participants per comparison with available direct data are given in Table 6.

Pairwise meta-analysis results

From the available comparisons with direct data described in Table 6, we kept data only for those that compared interventions described in Chapter 5, Prioritisation of interventions. Table 7 and Figures 12 and 13 show the available direct estimates for outcomes ‘no clinical improvement of TD symptoms’ and ‘total discontinuation rates’ for comparisons including interventions of priority with at least two studies available. Direct evidence suggests that ‘switch to olanzapine’ appears to be associated with lower discontinuation rates than ‘switch to risperidone’, whereas no important differences were detected between ‘vitamin E and AP continuation’ and ‘placebo with AP continuation’ for the outcome ‘total discontinuation rates’. In terms of no clinical improvement of TD symptoms, ‘vitamin E and AP continuation’ has an insignificant advantage over ‘placebo with AP continuation’. The comparison of ‘antipsychotic maintenance/TAU (including AP)’ versus ‘antipsychotic reduction (reduced dose FGA)’ is not statistically significant, but the overall treatment effect estimate does not rule out a beneficial effect of the second intervention.

FIGURE 12.

Pairwise meta-analysis results for active treatments vs. placebo (with AP continuation) for outcome ‘no clinical improvement of TD symptoms’ (comparisons with more than two studies, random-effects model, different heterogeneity parameters across comparisons). Heterogeneity was estimated using the method-of-moments estimator.

FIGURE 13.

Pairwise meta-analysis results for active treatments vs. placebo (with AP continuation) for outcome ‘total discontinuation rates’ (comparisons with more than two studies, random-effects model, different heterogeneity parameters across comparisons). Heterogeneity was estimated using the method-of-moments estimator.

Network meta-analysis results

Sensitivity analysis merging switch to antipsychotics

As a sensitivity analysis, we further conducted a NMA for the subnetwork of Figure 18 in which all switches to SGAs were merged into a ‘switch to SGA (any)’ treatment node, and all switches to FGAs were merged into a ‘switch to FGA (any)’ treatment node. The Caroff et al. ,117,118 Chan et al. ,115,116 Glazer et al. 189,190 and Kazamatzuri et al. 169 studies were excluded from this analysis as they examined either second- or first-generation antipsychotics only, and thus were representing a single treatment node. The network plot for this analysis is represented in Figure 20. Nodes and edges are weighted according to the number of studies involved in each treatment.

FIGURE 20.

Network plot for the second subnetwork of Figure 18 for the outcome ‘total discontinuation rates’, in which switch to first- and second-generation antipsychotics have been merged to ‘switch to FGA (any)’ and ‘switch to SGA (any)’ treatment nodes, respectively.

As the network presented in Figure 20 comprised only four trials, we did not perform NMA as the validity of the results of such an analysis would be questionable. The comparison ‘switch to FGA (any) versus switch to SGA (any)’ was informed by three studies, resulting in a pairwise meta-analysis OR of 0.54 (95% CI 0.21 to 1.42) in favour of ‘switch to FGA’. There is no indirect evidence to enrich the available information for this comparison and, thus, the use of NMA does not contribute to the knowledge regarding the relative effectiveness of the two interventions.

Evaluation of inconsistency

We intended to evaluate the consistency assumption using the loop-specific approach in Stata using a common heterogeneity within each loop (but different across loops). 180 We also intended to further assess the assumption of consistency in the entire network simultaneously using the design-by-treatment interaction model in Stata. 156,176 However, for the outcome ‘no clinical improvement of TD symptoms’ all loops were formed by multiarm studies only (consistent by definition) and, thus, consistency could not be evaluated. For the outcome ‘total discontinuation rates’ only one loop was formed for the subnetwork illustrated in Figure 18, ‘switch to olanzapine – switch to quetiapine – switch to haloperidol’; the inconsistency factor using the loop-specific approach was estimated at 1.45, with a (truncated) CI (0 to 4.51) indicating a lack of evidence of inconsistency.

Relative ranking of treatments

Table 11 shows the p-scores of the treatments involved in the outcomes ‘no clinical improvement of TD symptoms’ and ‘total discontinuation rates’ (networks of Figures 14 and 17), which are frequent analogues of SUCRAs. 171,172

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