Methods used in 2006 version

Criteria for considering studies for this review

Types of studies

We included all relevant randomised controlled trials.

Types of participants

We included people with schizophrenia, schizoaffective disorder or other serious chronic mental illness diagnosed by any criteria, irrespective of gender, age or nationality that have:
i. Required the use of neuroleptics for more than three months; and
ii. Developed tardive dyskinesia (diagnosed by any criteria) during neuroleptic treatment; and
iii. For whom the dose of neuroleptic medication had been stable for one month or more.

Types of interventions

1. The benzodiazepine family of drugs (alprazolam, bromazepam, chlordiazepoxide, clobazam, clonazepam, clorazepate dipotassium, diazepam, flunitrazepam, flurazepam, loprazolam, lorazepam, lormetazepam, medazepam, midazolam, nitrazepam, oxazepam, temazepam), any dose or means of administration.
2. Placebo and/or no intervention.

Types of outcome measures

1. Tardive dyskinesia changes
1.1 Improvement in the symptoms of individuals of more than 50% on any tardive dyskinesia scale*
1.2 Any improvement in the symptoms of individuals on any tardive dyskinesia scale, as opposed to no improvement
1.3 Deterioration in the symptoms of individuals, defined as any deleterious change on any tardive dyskinesia scale
1.4 Any adverse effect, other than deterioration of symptoms of tardive dyskinesia, as reported in the trials
1.5 Change in any tardive dyskinesia scale (endpoint ‐ baseline) averaged for each group
1.6 Endpoint scores of any tardive dyskinesia scale averaged for each group

2. General mental state changes
2.1 Deterioration in the psychiatric symptoms defined as deleterious change on any tardive dyskinesia scale
2.2 Endpoint scores of any mental health scale averaged for each group

3. Acceptability of the treatment
3.1 Acceptability of the intervention to the participant group as measured by numbers of people dropping out during the trial

All outcomes were grouped into time periods ‐ short term (less than 6 weeks), medium term (between 6 six weeks and six months) and long term (over six months).

* The primary outcome was clinical efficacy (defined as an improvement in the symptoms of tardive dyskinesia of more than 50%, on any scale, after at least six weeks of intervention).

Previous search methods for identification of studies in 2006

1. Electronic searches

1.1 For the update of 2006
We searched the Cochrane Schizophrenia Group Trials Register (November 2005) using the phrase:

[benzodiazep* or alprazolam or bromazepam or chlordiazepoxide or clobazam or clonazepam or clorazepate dipotassium or diazepam or flunitrazepam or flurazepam or loprazolam or lorazepam or lormetazepam or medazepam or midazolam or nitrazepam or oxazepam or temazepam]

This register is compiled by systematic searches of major databases, hand searches and conference proceedings (see Group Module). The previous updates were searched for relevant randomised trials by searching several electronic databases (Biological Abstracts, the Cochrane Schizophrenia Group's Register of trials, EMBASE, LILACS, MEDLINE, PsycLIT and SCISEARCH).

1.2 For previous versions of this review

1.2.1 Biological Abstracts (January 1982 to February 2002) were searched using the Cochrane Schizophrenia Group's phrase for randomised controlled trials (see Group search strategy) combined with the phrase:

[and (tardive near (dyskine* or diskine*) or (abnormal near movement* near disorder*) or (involuntar* near movement*)] and [benzodiazep* or alprazolam or bromazepam or chlordiazepoxide or clobazam or clonazepam or clorazepate dipotassium or diazepam or flunitrazepam or flurazepam or loprazolam or lorazepam or lormetazepam or medazepam or midazolam or nitrazepam or oxazepam or temazepam]

1.2.2 Cochrane Schizophrenia Group's Register (February 2002) was searched using the phrase:

[benzodiazep* or alprazolam or bromazepam or chlordiazepoxide or clobazam or clonazepam or clorazepate dipotassium or diazepam or flunitrazepam or flurazepam or loprazolam or lorazepam or lormetazepam or medazepam or midazolam or nitrazepam or oxazepam or temazepam]

1.2.3 EMBASE (January 1980 to February 2002) was searched using the Cochrane Schizophrenia Group's phrase for randomised controlled trials (see Group search strategy) combined with the phrase:

[and (tardive dyskinesia in thesaurus ‐subheadings, prevention, drug therapy, side effect and therapy) or (neuroleptic dyskinesia in thesaurus ‐all subheadings) or (tardive and dyskines*) or (movement* and disorder*) or (abnormal and movement* and disorder*)] and [benzodiazep* or alprazolam or bromazepam or chlordiazepoxide or clobazam or clonazepam or clorazepate dipotassium or diazepam or flunitrazepam or flurazepam or loprazolam or lorazepam or lormetazepam or medazepam or midazolam or nitrazepam or oxazepam or temazepam]

1.2.4 LILACS (January 1982 to February 2002) was searched using the Cochrane Schizophrenia Group's phrase for randomised controlled trials (see Group search strategy) combined with the phrase:

[and (tardive and (dyskinesia* or diskinesia*)) or (drug induced movement disorders in thesaurus)] and [benzodiazep* or alprazolam or bromazepam or chlordiazepoxide or clobazam or clonazepam or clorazepate dipotassium or diazepam or flunitrazepam or flurazepam or loprazolam or lorazepam or lormetazepam or medazepam or midazolam or nitrazepam or oxazepam or temazepam]

1.2.5 MEDLINE (January 1966 to February 2002) was searched using the Cochrane Schizophrenia Group's phrase for randomised controlled trials (see Group search strategy) combined with the phrase:

[and (movement‐disorders in MeSH / explode all subheadings) or (anti‐dyskinesia‐agents in MeSH / explode all subheadings) or (dyskinesia‐drug‐induced in MeSH / explode all subheadings) and (psychosis in MeSH / explode all subheadings) or (schizophrenic disorders in MeSH / explode all subheadings) or (tardive near (dyskine* or diskine*)) or (abnormal* near movement* near disorder*) or (involuntar* near movement*)] and [benzodiazep* or alprazolam or bromazepam or chlordiazepoxide or clobazam or clonazepam or clorazepate dipotassium or diazepam or flunitrazepam or flurazepam or loprazolam or lorazepam or lormetazepam or medazepam or midazolam or nitrazepam or oxazepam or temazepam]

1.2.6 PsycLIT (January 1974 to February 2002) was searched using the Cochrane Schizophrenia Group's phrase for randomised controlled trials (see Group search strategy) combined with the phrase:

[and (explode movement‐disorders in DE) or (explode tardive‐dyskinesia in DE) or (tardive near (dyskine* or diskine*) or (abnormal* near movement* near disorder*) or (involuntar* near movement*)] and [benzodiazep* or alprazolam or bromazepam or chlordiazepoxide or clobazam or clonazepam or clorazepate dipotassium or diazepam or flunitrazepam or flurazepam or loprazolam or lorazepam or lormetazepam or medazepam or midazolam or nitrazepam or oxazepam or temazepam]

1.2.7 SCISEARCH ‐ Science Citation Index
Each of the included studies was sought as a citation on the SCISEARCH database. Reports of articles that had cited these studies were inspected in order to identify further trials.

2. Reference searching
We examined references cited in all included trials in order to identify more studies.

3. Personal contact
If issues around or within any study were unclear we contacted the first author for clarification and attempted to contact the first author of all included and excluded studies in order to identify additional trials.

Data collection and analysis

The first review was undertaken by John McGrath (Queensland, Australia) and Karla Soares (Tel Aviv, Israel) in 1996. The first update (2002) was undertaken by Karla Soares (KSW) and Paul Umbrich (Leeds, UK). The reviewers had a similar protocol for identifying studies and if there was any disagreement, it was discussed and resolved. For the update of 2006, we (Seth Bhoopathi PSB, KSW) applied the following methods.

1. Selection of trials
The principal reviewer PSB (Paranthaman Bhoopathi) inspected the citations identified from the search and identified potentially relevant abstracts. KSW (Karla Soares) was contacted and she inspected the citations independently. We discussed and reported any disagreement, and where there was still doubt, we acquired the full article for further inspection. Once we had obtained the full articles we decided if the studies met the review criteria.

2. Assessment of methodological quality
We allocated trials to three quality categories, as described in the Cochrane Collaboration Handbook (Higgins 2005). The categories are defined below:
A. Low risk of bias (adequate allocation concealment)
B. Moderate risk of bias (some doubt about the results)
C. High risk of bias (inadequate allocation concealment).
For the purpose of the analysis in this review, trials were included if they met the Cochrane Handbook criteria A or B.

3. Data management

3.1 Data extraction
PSB undertook data extraction during the update. All data was discussed with KSJM, the decisions documented and, where necessary, we contacted the study authors to help resolve the issue.

3.2 Intention to treat analysis
We excluded data from studies where more than 50% of participants in any group were lost to follow up (this does not include the outcome of 'leaving the study early'). In studies with less than 50% dropout rate, we considered people leaving early to have had the negative outcome, except for the event of death. We analysed the impact of including studies with high attrition rates (25‐50%) in a sensitivity analysis. If inclusion of data from this latter group did result in a substantive change in the estimate of effect we did not add their data to trials with less attrition, but presented them separately.

4. Data analysis
4.1 Binary data
For binary outcomes, we calculated a standard estimation of the risk ratio (RR) and its 95% confidence interval (CI). We also calculated the number needed to treat statistic (NNT). If we found heterogeneity we used a random effects model (see section 5).

4.2 Continuous data
4.2.1 Normally distributed data: continuous data on clinical and social outcomes are often not normally distributed. To avoid the pitfall of applying parametric tests to non‐parametric data, we applied the following standards to all data before inclusion: (a) standard deviations and means were reported in the paper or were obtainable from the authors; (b) when a scale started from the finite number zero, the standard deviation, when multiplied by two, was less than the mean (as otherwise the mean is unlikely to be an appropriate measure of the centre of the distribution, (Altman 1996); (c) if a scale started from a positive value the calculation described above was modified to take the scale starting point into account. In these cases skew is present if 2SD>(S‐Smin), where S is the mean score and Smin is the minimum score. Endpoint scores on scales often have a finite start and end point and these rules can be applied to them. When continuous data are presented on a scale which includes a possibility of negative values (such as change on a scale), it is difficult to tell whether data are non‐normally distributed (skewed) or not. Skewed data from studies of less than 200 participants would have been entered in additional tables rather than into an analysis. Skewed data poses less of a problem when looking at means if the sample size is large and would have been entered into a synthesis.

For change data (endpoint minus baseline), the situation was even more problematic. In the absence of individual patient data it is impossible to know if data are skewed, though this is likely. After consulting the ALLSTAT electronic statistics mailing list, we presented change data in MetaView in order to summarise available information. In doing this, we assumed either that data were not skewed or that the analyses could cope with the unknown degree of skew. Without individual patient data it is impossible to test this assumption. Where both change and endpoint data were available for the same outcome category, we presented only the endpoint data. We acknowledge that by doing this much of the published change data were excluded, but we argue that endpoint data is more clinically relevant and that if change data were to be presented along with endpoint data, it would be given undeserved equal prominence. Authors of studies reporting only change data are being contacted for endpoint figures. Non‐normally distributed data were reported in the 'other data types' tables.

Skewed data: continuous data on clinical and social outcomes are often not normally distributed. To avoid the pitfall of applying parametric tests to non‐parametric data, we applied the following standards to all data before inclusion: (a) standard deviations and means were reported in the paper or were obtainable from the authors; (b) when a scale starts from a finite number (such as zero), the standard deviation, when multiplied by two, was less than the mean (as otherwise the mean was unlikely to be an appropriate measure of the centre of the distribution ‐ (Altman 1996)). Endpoint scores on scales often have a finite start and end point and this rule can be applied to them.

4.2.2 Summary statistic: for continuous outcomes, we estimated a weighted mean difference (WMD) between groups. Again, if we found heterogeneity (see section 5) we used a random effects model.

4.2.3 Valid scales: A wide range of instruments is available to measure mental health outcomes. These instruments vary in quality and many are not valid, or even ad hoc. For outcome instruments some minimum standards have to be set. It has been shown that the use of rating scales which have not been described in a peer‐reviewed journal (Marshall 2000) is associated with bias; therefore we excluded the results of such scales. However, as it was expected that therapists would frequently also be the rater, such data were included but commented on as 'prone to bias'.

Whenever possible we took the opportunity to make direct comparisons between trials that used the same measurement instrument to quantify specific outcomes. Where continuous data were presented from different scales rating the same effect, both sets of data were presented as well as the general direction of effect.

4.2.4 Endpoint versus change data: where possible we presented endpoint data and if both endpoint and change data were available for the same outcomes, then we reported only endpoint data in this review.

4.2.5 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 (Divine 1992) ‐ whereby p values are spuriously low, confidence intervals unduly narrow and statistical significance overestimated ‐ causing type I errors (Bland 1997, Gulliford 1999). Secondly, RevMan does not currently support meta‐analytic pooling of clustered dichotomous data, even when these are correctly analysed by the authors of primary studies, since the 'design effect' (a statistical correction for clustering) cannot be incorporated.

Where clustering was not accounted for in primary studies, we presented the data in a table, with an (*) symbol ‐ to indicate the presence of a probable unit of analysis error. Subsequent versions of this review will seek to contact first authors of studies to seek intra‐class correlation coefficients of their clustered data and to adjust for these using accepted methods (Gulliford 1999). Where clustering has been incorporated into the analysis of primary studies, then we will also present these data in a table. No further secondary analysis (including meta‐analytic pooling) will be attempted until there is consensus on the best methods of doing so, and until RevMan, or any other software, allows this. A Cochrane Statistical Methods Workgroup is currently addressing this issue. In the interim, individual studies will be very crudely classified as positive or negative, according to whether a statistically significant result (P < 0.05) was obtained for the outcome in question, using an analytic method that allowed for clustering.

5. Test for heterogeneity
Firstly, we considered all the included studies within any comparison to judge clinical heterogeneity. Then we used visual inspection of graphs to investigate the possibility of statistical heterogeneity. This was supplemented using, primarily, the I‐squared statistic. This provides an estimate of the percentage of variability due to heterogeneity rather than chance alone. Where the I‐squared estimate was greater than or equal to 75%, we interpreted it as indicating the presence of high levels of heterogeneity (Higgins 2003). If inconsistency was high, we did not summate the data, but the data were presented separately and we investigated the reasons for heterogeneity. The studies responsible for heterogeneity were not added to the main body of homogeneous trials by us, but summated and presented separately and reasons for heterogeneity investigated.

6. Addressing publication bias
We entered data from all included studies into a funnel graph (trial effect against trial size) in an attempt to investigate the likelihood of overt publication bias (Davey Smith 1997).

7. Sensitivity analyses
We analysed the effect of including studies with high attrition rates in a sensitivity analysis.

8. General
Where possible, we entered data in such a way that the area to the left of the line of no effect indicated a favourable outcome for benzodiazepines.