1. Dance Therapy

Dance therapy (in groups or individually), for any length of time, as an adjunctive treatment for schizophrenia or schizophrenia‐like disorders, regardless of any other biological, psychological or social intervention being used.

We employed The American Dance Therapy Association's (ADTA) definition of dance therapy ‐ "the psychotherapeutic use of movement as a process which furthers the emotional, social, cognitive, and physical integration of the individual"‐ as a standard for inclusion, however, we did not need the therapy to be formally stated as dance therapy, for example, it may be stated as body‐oriented psychological therapy (BPT). We considered any intervention using dance or movement as a therapeutic tool.

2. Standard/routine care

The care that a person with schizophrenia would normally receive had they not been included in the research trial. We considered 'waiting list control groups' as standard care.

3. Other treatments

These include any other biological, psychological or social treatments such as medication, problem‐solving therapy, psycho‐education programmes, social skills training, cognitive‐behavioural therapy, family therapy or psychodynamic psychotherapy.

4. Non intervention

Untreated control groups.

Primary outcomes

Secondary outcomes

Updated search(2012)

1. Cochrane Schizophrenia Group Trials Register (July 2012)

The Trials Search Co‐ordinator searched the Cochrane Schizophrenia Group’s Trials Register (10th July 2012)

The ‘Intervention’ field was searched using the phrase:

*danc*

The Cochrane Schizophrenia Group’s Trials Register is compiled by systematic searches of major databases, handsearches of journals and conference proceedings (see Group Module). Incoming trials are screened by the Trial Search Co‐ordinator and assigned to relevant existing or new review titles.

2. Chinese main medical databases (1 January 2007 to 17 September 2012)

1. Extraction

For this update, JR and JX extracted data from the included study. We extracted data presented only in graphs and figures where possible. When further information was necessary, we contacted the authors of the study in order to obtain missing data or for clarification. If we had identified studies that were multicentre, where possible, we planned to extract the data relevant to each component centre separately.

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). The Number Needed to Treat/Harm (NNT/H) statistic with its confidence intervals is intuitively attractive to clinicians but is problematic both in its accurate calculation in meta‐analyses and interpretation (Hutton 2009). For binary data presented in the 'Summary of findings' table, where possible, we calculated illustrative comparative risks.

2. Continuous data

For continuous outcomes we estimated mean difference (MD) between groups. We would prefer not to calculate effect size measures (standardised mean difference (SMD)). However, if scales of very considerable similarity had 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. 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, confidence intervals (CIs) unduly narrow and statistical significance overestimated. This causes type I errors (Bland 1997; Gulliford 1999).

If clustering had not been accounted for in primary studies, we planned to present data in a table, with a (*) symbol to indicate the presence of a probable unit of analysis error. In subsequent versions of this review, if we include cluster randomised trials, we will seek to contact first authors of such studies to obtain intra‐class correlation coefficients (ICCs) for their clustered data and to adjust for this by using accepted methods (Gulliford 1999). Where clustering has been incorporated into the analysis of primary studies, we will present these data as if from a non‐cluster randomised study, but adjust for the clustering effect.

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). If the ICC is not reported it will be assumed to be 0.1 (Ukoumunne 1999).

If cluster studies have been appropriately analysed taking into account ICCs and relevant data documented in the report, synthesis with other studies would be possible using the generic inverse variance technique.

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, if we had included cross‐over trials, we intended only to use the data of the first phase of cross‐over studies.

3. Studies with multiple treatment groups

No studies with multiple treatment groups were included.

In future updates of this review, if an included study involves more than two treatment arms, if relevant, we will present the additional treatment arms in comparisons. If data are binary, we will simply add and combine them 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 are not relevant, we will 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 40% of data be unaccounted for, we would not reproduce these data or use them within analyses. If, however, more than 40% of those in one arm of a study were lost, but the total loss was less than 40%, we addressed this within the 'Summary of findings' table by down‐rating quality. Finally, we also downgraded quality within the 'Summary of findings' table for losses of 25% to 40% in total.

2. Binary

In the case where attrition for a binary outcome was between 0% and 40% and where these data were not clearly described, we presented data on a 'once‐randomised‐always‐analyse' basis (an intention‐to‐treat analysis). Those leaving the study early were all assumed to have the same rates of negative outcome as those who completed, with the exception of the outcome of death and adverse effects. For these outcomes the rate of those who stayed in the study ‐ in that particular arm of the trial ‐ were used for those who did not. We undertook a sensitivity analysis to test how prone the primary outcomes were to change when 'completer' data only were compared to the intention‐to‐treat analysis using the above assumptions.

3. Continuous

1. Clinical heterogeneity

We will consider all included studies initially, without seeing comparison data, to judge clinical heterogeneity. We will simply inspect all studies for clearly outlying people or situations which we had not predicted would arise. When such situations or participant groups arise, we will discuss these fully.

2. Methodological heterogeneity

We will consider all included studies initially, without seeing comparison data, to judge methodological heterogeneity. We will simply inspect all studies for clearly outlying methods which we had not predicted would arise. When such methodological outliers arise, we will discuss these fully.

3. Statistical heterogeneity

1. Subgroup analyses ‐ only primary outcomes

2. Investigation of heterogeneity

There is only one included study.

In future updates, if we include more studies, if inconsistency is high, we will report this. First, we will investigate whether data had been entered correctly. Second, if data are correct, we will visually inspect the graph and successively remove outlyingstudies to see if homogeneity is restored. For this review, we have decided that should this occur with data contributing to the summary finding of no more than around 10% of the total weighting, we will present data. If not, then we will not pool data and we will discuss these issues. We know of no supporting research for this 10% cut‐off, but we use prediction intervals as an alternative to this unsatisfactory state.

When unanticipated clinical or methodological heterogeneity is obvious we will simply state hypotheses regarding these for future reviews or versions of this review. We do not anticipate undertaking analyses relating to these.

1. Implication of randomisation

We 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 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 entered all 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 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.

If assumptions had to be made regarding missing SDs data (see Dealing with missing data), we planned to compare 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 would have been undertaken to test how prone results were to change when completer‐only data only were compared to the imputed data using the above assumption. If there had been a substantial difference, we would have reported results and discussed them but we would have continued to employ our assumption

3. Risk of bias

We planned to analyse 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 would have included data from these trials in the analysis.

4. Imputed values

We also intended to undertake a sensitivity analysis to assess the effects of including data from trials if we used imputed values for ICC in calculating the design effect in cluster randomised trials.

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

5. Fixed‐effect and random‐effects

We used a fixed‐effect model to calculate data from the one included study.