Yoga for schizophrenia

  • Protocol
  • Intervention

Authors


Abstract

This is the protocol for a review and there is no abstract. The objectives are as follows:

To assess the effects of adjunct yoga compared with standard care for the management of schizophrenia.

Background

Description of the condition

Schizophrenia is a relatively common mental disorder with a lifetime prevalence of 0.3% to 0.6% and an incidence of 10.2 to 22.0 per 100,000 person-years (McGrath 2008). It is one of the most debilitating psychiatric disorders. The Diagnostic Statistical Manual of Mental Disorders-IV (DSM-IV) criteria for schizophrenia includes positive and negative symptoms that have a detrimental impact on both social and occupational functioning (Rossler 2005). Schizophrenia accounts for 1.1% of the total disability-adjusted life years (DALYs) making it the fifth leading cause of DALYs worldwide in the 15 to 44 year-old age group (World Health Organization 2008).

Schizophrenia can have a significant impact on a person's ability to function within society due to both positive and negative symptoms The positive symptoms of schizophrenia reflect a distortion of normal functions. Acute sufferers may present with symptoms such as delusions, hallucinations and disorganised speech or behaviour. Chronic sufferers may also develop so-called negative symptoms. Negative symptoms reflect a reduction of normal functions, and include symptoms such as flattened affect, social withdrawal, impaired cognition and apathy. (Duraiswamy 2007; Rossler 2005).

After diagnosis of schizophrenia is made, antipsychotic medication is the first-line treatment. Their mechanism of action is mainly to block dopamine D2 receptors in the mesocortical and mesolimbic dopaminergic pathways. First-generation antipsychotics (e.g., chlorpromazine, fluphenazine, haloperidol) were discovered in the 1950s. They were shown to be effective in the treatment of positive symptoms, but often cause extra-pyramidal side effects (EPSE) (e.g. akathisia (restlessness), tardive dyskinesia (e.g. abnormal tongue movements, head nodding and rocking movements), parkinsonism (tremor, rigidity and bradykinesia (slowness of movement)) and acute dystonia (involuntary muscle spasms)) (Tandon 2010; Van Os 2009).

Newer agents, or second-generation antipsychotics (e.g., olanzapine, quetiapine and risperidone) less frequently cause these EPSE. Second-generation antipsychotics are associated with side effects including weight gain, sedation, sexual dysfunction and metabolic syndrome. Although equally effective in treating positive symptoms as first-generation antipsychotics, their promise of a greater efficacy against negative and cognitive symptoms has not yet been proven. Many people continue to suffer from persistent symptoms and relapses, particularly when they fail to adhere to medical treatment (Tandon 2010; Van Os 2009). This underlines the need for additional non-pharmacological interventions including psychosocial therapies as adjuncts to help alleviate symptoms, and to improve adherence, functional outcome and quality of life (Kern 2009).

Description of the intervention

Yoga originates from India as an ancient Hindu practice incorporating physical postures with breathing exercises seeking to bring about a balance between the mental and physical state (Bussing 2012; Ross 2012; Sherman 2012). The principles behind its practice were first described by Pantajali, and were believed to allow the mind and the body to be prepared for spiritual development (Ross 2012). In the western world, yoga has now been widely adopted as both a method of relaxation and exercise. Hatha yoga is the most widely adopted practice used in the Western world (Collins 1998). Its use of postures (asanas) improves strength, flexibility, co-ordination and endurance and its use of breathing exercises (pranayama) improves respiratory control and concentration. Mantra yoga is another well-known and widely practiced form of Hindu yoga and focuses on the use of chants to achieve mental and spiritual transformation (Sherman 2012). The improvements in cognition and reductions in stress seen in those who practice yoga may be of benefit to those with schizophrenia as schizophrenia is associated with cognitive defects, and relapses of schizophrenia can be associated with stress (Duraiswamy 2007).

With its increasing popularity, research into the effect of yoga on both physical and mental health has identified key benefits of yoga. It has been shown to both reduce stress and improve cognitive function in healthy people (Bangalore 2012), and has been shown to be useful as a complementary therapy for many health conditions, including an improvement in blood pressure control and mental health conditions including depression and anxiety disorders (Bussing 2012). Its benefits in other mental health conditions has lead to research into the role of yoga as a complementary therapy for the management of schizophrenia (Duraiswamy 2007). A systematic review of randomised controlled trials indicated that yoga could also be of benefit as an add-on treatment to reduce both positive and negative symptoms of schizophrenia and to improve the health-related quality of life of people with schizophrenia (Duraiswamy 2007; Vancampfort 2012).

How the intervention might work

Yoga has been identified to have a role in regulating the autonomic nervous system (Varambally 2012), decreasing sympathetic tone, creating a reaction the opposite to the 'fight or flight' reaction. There is a subsequent effect on the limbic system and hypothalamic pituitary axis leading to a reduction in blood cortisol levels. This leads to a regulation of heart rate and blood pressure, which has obvious cardiovascular benefits (Damodaran 2002). Yoga also emphasises a focus on relaxed breathing and this internal concentration is thought to reduce stress by minimising mental focus on external stressors or threats (Bangalore 2012). The decrease in cortisol levels is also thought to have an effect on the better control of blood glucose, cholesterol and total lipids. Since antipsychotic medication for the treatment of schizophrenia is associated with dyslipidaemia, diabetes and obesity, yoga may be a useful adjuvant to therapy to minimise these effects (Bangalore 2012).

The improvement in the physical health of these patients could have a direct improvement in their mental health. Yoga is also identified to have a role in improving sleep (Collins 1998). There is also thought to be a role of oxytocin, a hormone related to improved mood, analogues of which have been suggested as possible treatment of schizophrenia (Bangalore 2012; Feifel 2011). It has been reported that plasma levels of oxytocin are higher in people after practice of yoga (Varambally 2012).

In addition, yoga has been shown to have psychosocial benefits including a sense of autonomy, improved perceptions of competence, enhanced body image, self-efficacy and distraction from mental imbalance due to focuses on breathing and positions (Vancampfort 2011).

Why it is important to do this review

The practice of yoga has shown promising results in other areas for benefiting health, yet its use for people with schizophrenia is under-researched in comparison with many other physical and mental health conditions. To the best of our knowledge, there is currently no meta-analysis available assessing the effectiveness of yoga as an adjunct to standard care treatment for schizophrenia. Therefore, the aim of this review is to systematically assess and meta-analyse the effectiveness of yoga in people with schizophrenia.

In a time of increasing patient choice, this review will aim to investigate the potential benefits of yoga – if indeed there are any – and expectantly aid the integration of yoga into clinical practice.

This review will build on the work already carried out by one of the authors of this review. In a systematic review Vancampfort 2012 concluded that there is a place for yoga in add-on treatment for schizophrenia. There have been several studies comparing the effects of yoga and other forms of exercise as add-on therapies for the management of schizophrenia (Vancampfort 2011), however in this review we will focus only on comparisons of yoga with control groups consisting of standard care.

Objectives

To assess the effects of adjunct yoga compared with standard care for the management of schizophrenia.

Methods

Criteria for considering studies for this review

Types of studies

All relevant randomised controlled trials. If a trial is described as 'double blind' but implies randomisation, we will include such trials in a sensitivity analysis (see Sensitivity analysis). If their inclusion does not result in a substantive difference, they will remain in the analyses. If their inclusion does result in important clinically significant but not necessarily statistically significant differences, we will not add the data from these lower quality studies to the results of the better trials, but will present such data within a subcategory. We will exclude quasi-randomised studies, such as those allocating by alternate days of the week. We will also exclude cross-over studies where participants receive different treatments sequentially, because of potential carry-over effects from all treatments. Where people are given additional treatments within the group receiving yoga, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the allocation of yoga that is randomised.

Types of participants

We will consider all people with a diagnosis of schizophrenia or related disorders, including schizophreniform disorder, schizoaffective disorder and delusional disorder. This includes diagnoses made by any means. We are interested in making sure that information is as relevant to the current care of people with schizophrenia as possible so propose to clearly highlight the current clinical state (acute, early post-acute, partial remission, remission) as well as the stage (prodromal, first episode, early illness, persistent) and as to whether the studies primarily focused on people with particular problems (for example, negative symptoms, treatment-resistant illnesses). We will not exclude trials due to their age, nationality or gender of the participants.

Types of interventions

1. Yoga therapy

Participants receiving yoga in addition to standard care. Yoga, however defined by the study can incorporate any of the major subtypes such as Mantra, Laya, Hatha and Raja (Bangalore 2012). "Yoga" also includes any of the definitions including breathing exercises and/or meditation and/or body postures.

Standard care is defined as treatment a participant would receive had they not been involved in any research trial, given a diagnosis of schizophrenia. This normally includes a biological, psychological and social approach to care including antipsychotic medication, and utilisation of services including hospital stay, day hospital attendance and community psychiatric nursing involvement.

2. Control group

People receiving standard care, as defined above, for the management of their schizophrenia without yoga intervention.

For a study to be included, the yoga therapy intervention and control group have to have a similar duration and approach to standard care.

Types of outcome measures

All outcomes will be divided into short term (less than six months), medium term (seven to 12 months) and long term (over one year).

Primary outcomes

1. Mental state

1.1 Clinically significant change in mental state - as defined by each study
1.2 Any change in mental state
1.3 Average endpoint or change scores from mental state scales

2. Global state

2.1 Relapse
2.2 Clinically significant change in global state - as defined by each study
2.3 Any change in global state
2.4 Average endpoint or change scores from global state scales

3. Social functioning

3.1 Clinically significant change in social functioning - as defined by each study
3.2 Any change in social functioning
3.3 Average endpoint or change scores from global state scales

4. Adverse Effects

4.1 At least one adverse effect
4.2 Average endpoint or change scores from adverse effect scales
4.3 Specific adverse effects

Secondary outcomes
1. Quality of life

1.1 Significant change in quality of life - as defined by each study
1.2 Any change in quality of life
1.3 Average endpoint or change scores from quality of life scales

2. Change in cognition

2.1 Clinically important change in overall cognitive functioning - as defined by each study

3. Leaving the study early

3.1 Any reason
3.2 Specific reason

4. Costs of care
4.1 Direct costs of care
4.2 Indirect costs of care

5. Effect on physical health

5.1 Significant change in physical health

6. Service use

6.1 Admission to hospital
6.2 Length of stay in hospital

7. 'Summary of findings' table

We will use the GRADE approach to interpret findings (Schünemann 2008) and will use GRADE profiler (GRADEPRO) to import data from RevMan 5.1 (Review Manager) to create 'Summary of findings' tables. These tables will 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 available data on all outcomes we rate as important to patient-care and decision making. We aim to select the following main outcomes for inclusion in the 'Summary of findings' table.

  1. Mental state

  2. Relapse

  3. Social functioning

  4. Adverse effects

  5. Quality of life

  6. Significant change in physical health

  7. Costs of care - direct and indirect

Search methods for identification of studies

Electronic searches

Cochrane Schizophrenia Group Trials Register

The Trials Search Co-ordinator will search the Cochrane Schizophrenia Group’s Trials Register using the phrase:

[(*yoga* in title, abstract and index terms of REFERENCE) or (*yoga* in interventions of STUDY)]

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

Searching other resources

1. Reference searching

We will inspect references of all included studies for further relevant studies.

2. Personal contact

We will contact the first author of each included study for information regarding unpublished trials.

Data collection and analysis

Selection of studies

Review authors AK and JC will independently inspect citations from the searches and identify relevant abstracts. AK and JC will then compare findings to ensure reliability. Where disputes arise, the full report will be acquired for more detailed scrutiny. Full reports of the abstracts meeting the review criteria will be obtained and inspected by JC. These identified reports will then be re-inspected by AK in order to ensure reliable selection. Where it is not possible to resolve disagreement by discussion, we will attempt to contact the authors of the study for clarification.

Data extraction and management

1. Extraction

Review authors AK and JC will extract data from all included studies independently and compare the results of extracted data from all of the studies. Any disagreement will be discussed, decisions documented and, if necessary, we will contact the authors of studies for clarification. Data presented only in graphs and figures will be extracted whenever possible, but will only be included if two review authors independently have the same result. We will attempt to contact authors through an open-ended request in order to obtain missing information or for clarification whenever necessary. If studies are multi-centre, where possible, we will extract data relevant to each component centre separately.

2. Management
2.1 Forms

We will extract data onto standard, simple forms.

2.2 Scale-derived data

We will include continuous data from rating scales only if:

a) the psychometric properties of the measuring instrument have been described in a peer-reviewed journal (Marshall 2000); and
b) the measuring instrument has not been written or modified by one of the trialists for that particular trial.

Ideally, the measuring instrument should either be i. a self-report or ii. completed by an independent rater or relative (not the therapist). We realise that this is not often reported clearly, in 'Description of studies' we will note if this is the case or not.

2.3 Endpoint versus change data

There are advantages of both endpoint and change data. Change data can remove a component of between-person variability from the analysis. On the other hand, calculation of change needs two assessments (baseline and endpoint) which can be difficult in unstable and difficult to measure conditions such as schizophrenia. We have decided primarily to use endpoint data, and only use change data if the former are not available. Endpoint and change data will be combined in the analysis as we will use mean differences (MD) rather than standardised mean differences (SMD) throughout (Higgins 2011).

2.4 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 aim to apply the following standards to all data before inclusion:
a) standard deviations (SDs) and means are reported in the paper or obtainable from the authors;
b) when a scale starts from the finite number zero, the SD, when multiplied by two, is 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 (such as the Positive and Negative Syndrome Scale (PANSS), (Kay 1986)) which can have values from 30 to 210), the calculation described above will be modified to take the scale starting point into account. In these cases skew is present if 2 SD > (S-S min), where S is the mean score and 'S min' is the minimum score.

Endpoint scores on scales often have a finite start and end point and these rules can be applied. Skewed data pose less of a problem when looking at means if the sample size is large (> 200) and we will enter these into the syntheses. We will present skewed endpoint data from studies of less than 200 participants as other data within the data and analyses section rather than enter such data into statistical analyses.

When continuous data are presented on a scale that includes a possibility of negative values (such as change data), it is difficult to tell whether data are skewed or not. We will present and enter change data into statistical analyses.

2.5 Common measure

To facilitate comparison between trials, we intend to convert variables that can be reported in different metrics, such as days in hospital (mean days per year, per week or per month) to a common metric (e.g. mean days per month).

2.6 Conversion of continuous to binary

Where possible, efforts will be made to convert outcome measures to dichotomous data. This can be done by identifying cut-off points on rating scales and dividing participants accordingly into 'clinically improved' or 'not clinically improved'. It is generally assumed that if there is a 50% reduction in a scale-derived score such as the Brief Psychiatric Rating Scale (Overall 1962) or the PANSS (Kay 1986), this could be considered as a clinically significant response (Leucht 2005; Leucht 2005a). If data based on these thresholds are not available, we will use the primary cut-off presented by the original authors.

2.7 Direction of graphs

Where possible, we will enter data in such a way that the area to the left of the line of no effect indicates a favourable outcome for yoga intervention. Where keeping to this makes it impossible to avoid outcome titles with clumsy double-negatives (e.g. 'Not improved') we will report data where the left of the line indicates an unfavourable outcome. This will be noted in the relevant graphs.

Assessment of risk of bias in included studies

Again, review authors AK and JC will work independently to assess risk of bias by using criteria described in the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011) to assess trial quality. This set of criteria is based on evidence of associations between overestimate of effect and high risk of bias of the article such as sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting.

If the raters disagree, the final rating will be made by consensus, with the involvement of another member of the review group. Where inadequate details of randomisation and other characteristics of trials are provided, we will contact authors of the studies in order to obtain further information. Non-concurrence in quality assessment will be reported, but if disputes arise as to which category a trial is to be allocated, again, we will resolve these by discussion.

The level of risk of bias will be noted in both the text of the review and in the 'Summary of findings' table.

Measures of treatment effect

1. Binary data

For binary outcomes, we will 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 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 CIs 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/s, where possible, we will calculate illustrative comparative risks.

2. Continuous data

For continuous outcomes, we will estimate the MD between groups. We prefer not to calculate effect size measures (SMD). However, if scales of very considerable similarity are used, we will presume there is a small difference in measurement, and we will calculate effect size and transform the effect back to the units of one or more of the specific instruments.

Unit of analysis issues

1. 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, CIs unduly narrow and statistical significance overestimated. This causes type I errors (Bland 1997; Gulliford 1999).

Where clustering is not accounted for in primary studies, we will 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 we will seek to contact first authors of 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 will 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, we will only use data of the first phase of cross-over studies.

3. Studies with multiple treatment groups

Where a study involves more than two treatment arms, if relevant, the additional treatment arms will be presented in comparisons. If data are binary, these will be simply added and combined within the two-by-two table. If data are continuous, we will combine data following the formula in section 7.7.3.8  (Combining groups) of the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011). Where the additional treatment arms are not relevant, we will not use these data.

Dealing with missing data

1. Overall loss of credibility

At some degree of loss of follow-up, data must lose credibility (Xia 2009). We choose that, for any particular outcome, should more than 50% of data be unaccounted for, we will not reproduce these data or use them within analyses, (except for the outcome 'leaving the study early'). If, however, more than 50% of those in one arm of a study are lost, but the total loss is less than 50%, we will address this within the 'Summary of findings' table/s by down-rating quality. Finally, we will also downgrade quality within the 'Summary of findings' table/s should loss be 25% to 50% in total.

2. Binary

In the case where attrition for a binary outcome is between 0% and 50% and where these data are not clearly described, we will present data on a 'once-randomised-always-analyse' basis (an intention-to-treat analysis). Those leaving the study early are 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 stay in the study - in that particular arm of the trial - will be used for those who did not. We will undertake a sensitivity analysis to test how prone the primary outcomes are to change when data only from people who complete the study to that point are compared with the intention-to-treat analysis using the above assumptions.

3. Continuous
3.1 Attrition

In the case where attrition for a continuous outcome is between 0% and 50%, and data only from people who complete the study to that point are reported, we will reproduce these.

3.2 Standard deviations (SDs)

If SDs are not reported, we will first try to obtain the missing values from the authors. If not available, where there are missing measures of variance for continuous data, but an exact standard error (SE) and CIs available for group means, and either a 'P' value or 't' value available for differences in mean, we can calculate them according to the rules described in the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011). When only the SE is reported, SDs are calculated by the formula SD = SE * square root (n). Chapters 7.7.3 and 16.1.3 of the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011) present detailed formulae for estimating SDs from P values, t or F values, CIs, ranges or other statistics. If these formulae do not apply, we will calculate the SDs according to a validated imputation method which is based on the SDs of the other included studies (Furukawa 2006). Although some of these imputation strategies can introduce error, the alternative would be to exclude a given study’s outcome and thus to lose information. We nevertheless will examine the validity of the imputations in a sensitivity analysis excluding imputed values.

3.3 Last observation carried forward

We anticipate that in some studies the method of last observation carried forward (LOCF) will be employed within the study report. As with all methods of imputation to deal with missing data, LOCF introduces uncertainty about the reliability of the results (Leucht 2007). Therefore, where LOCF data have been used in the trial, if less than 50% of the data have been assumed, we will present and use these data and indicate that they are the product of LOCF assumptions.

Assessment of heterogeneity

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, these will be fully discussed.

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 these will be fully discussed.

3. Statistical heterogeneity
3.1 Visual inspection

We will visually inspect graphs to investigate the possibility of statistical heterogeneity.

3.2 Employing the I2 statistic

Heterogeneity between studies will be investigated by considering the I2 method alongside the Chi2 'P' value. The I2 provides an estimate of the percentage of inconsistency thought to be due to chance (Higgins 2003). The importance of the observed value of I2 depends on i. magnitude and direction of effects and ii. strength of evidence for heterogeneity (e.g. 'P' value from Chi2  test, or a CI for I2). An I2 estimate greater than or equal to around 50% accompanied by a statistically significant Chi2 statistic, will be interpreted as evidence of substantial levels of heterogeneity (Section 9.5.2 - Higgins 2011). When substantial levels of heterogeneity are found in the primary outcome, we will explore reasons for heterogeneity (Subgroup analysis and investigation of heterogeneity).

Assessment of reporting biases

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 Systemic reviews of Interventions (Higgins 2011). We will try to locate protocols of included randomised trials. If the protocol is available, outcomes in the protocol and in the published report will be compared. If the protocol is not available, outcomes listed in the methods section of the trial report will be compared with actually 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 again described in Section 10 of the Cochrane Handbook for Systemic 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 will not use funnel plots for outcomes where there are 10 or fewer studies, or where all studies are of similar sizes. In other cases, where funnel plots are possible, we will seek statistical advice in their interpretation.

Data synthesis

We chose to use the random-effects model for analyses, however there is no closed argument for preference for use of fixed-effect or random-effects models. The random-effects method incorporates an assumption that the different studies are estimating different, yet related, intervention effects. The random-effects model also takes into account differences between studies even if there is no statistically significant heterogeneity. However, a disadvantage to the random-effects model is that it puts added weight onto small studies which often are the most biased ones which can either inflate or deflate the effect size.

Subgroup analysis and investigation of heterogeneity

1. Subgroup analyses
1.1 Primary outcomes

We do not anticipate a need for any subgroup analysis.

1.2 Clinical state, stage or problem

We propose to undertake this review and provide an overview of the effects of yoga for people with schizophrenia in general. In addition, however, we will try to report data on subgroups of people in the same clinical state, stage and with similar problems.

2. Investigation of heterogeneity

If inconsistency is high, this will be reported. First, we will investigate whether data have been entered correctly. Second, if data are correct, we will visually inspect the graph and remove outlying studies 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, data will be presented. If not, data will not be pooled and issues will be discussed. We know of no supporting research for this 10% cut-off but are investigating use of prediction intervals as an alternative to this unsatisfactory state.

When unanticipated clinical or methodological heterogeneity are 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.

Sensitivity analysis

1. Implication of randomisation

We aim to include trials in a sensitivity analysis if they are described in some way as to imply randomisation. For the primary outcomes, we will include these studies and if there is no substantive difference when the implied randomised studies are added to those with better description of randomisation, then all data will be employed from these studies.

2. Assumptions for lost binary data

Where assumptions have to be made regarding people lost to follow-up (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumption/s and when we use data only from people who complete the study to that point. If there is a substantial difference, we will report results and discuss them but will continue to employ our assumption.

Where assumptions have to be made regarding missing SDs data (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumption/s and when we use data only from people who complete the study to that point. A sensitivity analysis will be undertaken to test how prone results are to change when completer-only data only are compared to the imputed data using the above assumption. If there is a substantial difference, we will report results and discuss them but will continue to employ our assumption.

3. Risk of bias

We will analyse the effects of excluding trials that are 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 does not substantially alter the direction of effect or the precision of the effect estimates, then data from these trials will be included in the analysis.

4. Imputed values

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

If substantial differences are noted in the direction or precision of effect estimates in any of the sensitivity analyses listed above, we will not pool data from the excluded trials with the other trials contributing to the outcome, but will present them separately.

5. Fixed and random effects

All data will be synthesised using a random-effects model, however, we will also synthesise data for the primary outcome using a fixed-effect model to evaluate whether this alters the significance of the results.

Acknowledgements

We would like to acknowledge the advice and guidance of Professor Clive Adams and Claire Irving in the development of this protocol. The Cochrane Schizophrenia Group Editorial Base in Nottingham produces and maintains standard text for use in the Methods section of their reviews. We have used this text as the basis of what appears here and adapted it as required. The search term has been developed by the Trial Search Co-ordinator of the Cochrane Schizophrenia Group, Samantha Roberts and the contact author of this protocol.

We would also like to thank Yan Liu for peer reviewing this protocol.

Contributions of authors

Abigail Knowles - development and writing of protocol.

Jonathan Chadwick - development and writing of protocol.

Davy Vancampfort - advice for development and writing of protocol.

Declarations of interest

Authors have no known conflicts of interest.

Sources of support

Internal sources

  • The University of Nottingham, UK.

  • Nottinghamshire Healthcare NHS Trust, UK.

External sources

  • No sources of support supplied

Ancillary