Intervention Protocol

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Behavioural interventions for reducing weight gain in schizophrenia

  1. Guy Faulkner1,*,
  2. Markus J Duncan1,
  3. Margaret Hahn2,
  4. Gary Remington3,
  5. Tony Cohn4

Editorial Group: Cochrane Schizophrenia Group

Published Online: 15 OCT 2013

DOI: 10.1002/14651858.CD010781


How to Cite

Faulkner G, Duncan MJ, Hahn M, Remington G, Cohn T. Behavioural interventions for reducing weight gain in schizophrenia (Protocol). Cochrane Database of Systematic Reviews 2013, Issue 10. Art. No.: CD010781. DOI: 10.1002/14651858.CD010781.

Author Information

  1. 1

    University of Toronto, Faculty of Kinesiology and Physical Education, Toronto, Ontario, Canada

  2. 2

    Center for Addiction and Mental Health, Complex Mental Illness, Toronto, Canada

  3. 3

    University of Toronto, Centre for Addiction and Mental Health, Toronto, Ontario, Canada

  4. 4

    Centre for Addiction and Mental Health, Schizophrenia Program and MAPS, Toronto, Ontario, Canada

*Guy Faulkner, Faculty of Kinesiology and Physical Education, University of Toronto, 55 Harbord St, Toronto, Ontario, On M5S 2W6, Canada. guy.faulkner@utoronto.ca.

Publication History

  1. Publication Status: New
  2. Published Online: 15 OCT 2013

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Background

  1. Top of page
  2. Background
  3. Objectives
  4. Methods
  5. Acknowledgements
  6. Contributions of authors
  7. Declarations of interest
  8. Sources of support
 

Description of the condition

 

Obesity and schizophrenia

Obesity is a common problem for people with schizophrenia, a problem that has been exacerbated more recently with the increased use of second generation antipsychotics, many of which are associated with the risk of weight gain and metabolic disturbance (Allison 1999; Homel 2002; Casey 2004, De Hert 2011). The prevalence of obesity in people with schizophrenia has been reported to be anywhere from one and a half to four times higher than the general population (Silverstone 1988; Coodin 2001; ADA/APA 2004; Gurpegui 2012). For people with schizophrenia, there is a marked increase in standardised mortality ratios for both natural and unnatural causes of death and much of this increment may be attributed to the increased prevalence of coronary heart disease risk (Cohn 2004; Goff 2005; Henderson 2005; Mackin 2005; Saari 2005), and related obesity in this population (Coodin 2001; Daumit 2003; Susce 2005). The significance and recognition of this prevalence and its impact on premature mortality and morbidity has led to the development of consensus statements on its management (ADA/APA 2004; De Nayer 2005). Despite this, evidence from a systematic review suggests that the all-cause standardised mortality ratio between persons with schizophrenia and the general population has risen steadily since the 1970s (Saha 2007).

 

Mechanisms of weight gain in schizophrenia

It is difficult to identify the relative contributions of disease-specific factors such as genetics, the side effects of medications, and lifestyle factors such as diet and physical inactivity on the prevalence of obesity in schizophrenia. In a meta-analysis, every antipsychotic medication except ziprasidone and molindone was associated with some degree of weight gain after just 10 weeks of treatment (Allison 1999). The effects were greatest with olanzapine and clozapine, which increased body weight by approximately 4 to 4.5 kilograms.

To date, there is no consensus on what pharmacological factors may be involved in this weight gain particularly regarding the newer antipsychotics. As reviewed elsewhere (Ananth 2004; Reynolds 2010), a range of potential weight-inducing mechanisms such as dopaminergic blockage; increased appetite due to the interaction of antipsychotic medication with dopamine, serotonin, and histamine neuronal receptors; increased leptin; and increases in systemic levels of various cytokines and soluble cytokine receptors could be implicated. It is important to note, however, that obesity was commonly reported before antipsychotics were widely introduced (Baptista 2002). In terms of lifestyle factors, physical activity is one important component of weight management and research consistently demonstrates that people with schizophrenia are less physically active than the general population (Brown 1999; Cohn 2004; Daumit 2005, Vancampfort 2011). Similarly, a recent systematic review suggests that people with schizophrenia have a diet high in fat and low in fibre and vitamins (Dipasquale 2013). Furthermore individuals with schizophrenia may consume more calories than population controls (Strassnig 2003a). As with the general population, the aetiology of obesity appears complex and multifactorial. Consequently, intervention strategies must also target a broad range of factors that may contribute to weight gain in this population.

 

Health effects of obesity

Obesity doubles the risk of all-cause mortality, coronary heart disease, stroke and type 2 diabetes, increases the risk of some cancers, musculoskeletal problems and loss of function, and carries negative psychological consequences (DoH 2004). Being an obese or overweight adult is associated with large decreases in life expectancy and increases in early mortality in recent US population data, and these decreases are similar to those seen with smoking (Peeters 2003). The burden of obesity in schizophrenia will be at least comparable in terms of premature mortality and morbidity, and is likely to have important deleterious effects on mortality and health (Fontaine 2001).

Quality of life is further reduced for people with schizophrenia with high body mass index (Kurzthaler 2001; Strassnig 2003b; Faulkner 2007a) and those gaining weight (Allison 2003). Furthermore, Weiden 2004 reported a significant, positive association between obesity, subjective distress from weight gain and medication non-compliance in a sample of people with schizophrenia. People with schizophrenia face the combined challenges of living with the illness, and for many, obesity and related illnesses. This combination is a major public health problem (Wirshing 2004) and carries considerable human cost. Recognition of this has lead to growing concern with how best to intervene (Green 2000; Le Fevre 2001; Osborn 2001; Birt 2003; Catapana 2004).

 

Description of the intervention

 

Treatment of obesity in the general population

The treatment of obesity consists of behavioural, pharmacological, and surgical interventions. Current guidelines state that behavioural interventions should always be used before, and then in conjunction with the latter options (Snow 2005). In terms of behavioural interventions, strategies should combine diet, exercise and psychological/behavioural components. In a previously published Cochrane review (Shaw 2005), cognitive-behaviour therapy, when combined with a diet/exercise intervention, was found to increase weight loss compared with diet/exercise alone by 4.9 kg (CI -7.3 to -2.4). Behaviour therapy alone was found to result in significantly greater weight loss (-2.5 kg) than placebo when assessed as a stand-alone weight loss strategy (CI -1.7 to -3.3). Bariatric surgery could be considered as a treatment option for patients with a body mass index (BMI) of 40 kg/m2 or greater, and who have failed an adequate lifestyle modification programme (with or without adjunctive pharmacological therapy) (see Hamoui 2004 in the context of schizophrenia). Pharmacological interventions for weight loss in the context of schizophrenia will be discussed in greater detail in a concurrent Cochrane review (Hahn (in progress)).

Overall, existing evidence suggests that even effective treatments for adult obesity only produce modest weight loss (approximately 2-5 kg) compared to no treatment or usual care. Given such modest weight loss in studies in the adult population, it might be expected that interventions may be difficult for people with schizophrenia given the range of social and cognitive difficulties associated with the illness. Another implication is that the best treatment of obesity is its prevention. However, modest weight loss is a worthwhile outcome of interventions. There is evidence that loss of body weight by as little as 5% to 10% may reduce some of the health risks associated with adult obesity (Wilding 1997). Furthermore, sustained changes in health behaviours as a result of such interventions, e.g., increased levels of physical activity, may reduce risk of mortality and morbidity independent of any weight loss (Wei 1999). Increasing levels of physical activity are also associated with a range of mental health benefits in this population (Faulkner 1999).

 

How the intervention might work

Behavioural interventions typically seek to help individuals decrease caloric intake and increase energy expenditure.

 

Why it is important to do this review

We believe there is a sufficient volume of material to split the previous Cochrane review (Faulkner 2007b) into separate reviews focusing on behavioural and pharmacological interventions independently. There are at least seven systematic reviews examining either behavioural interventions (Werneke 2003; Loh 2006, Caemmerer 2012), pharmacological interventions (Werneke 2002, Maayan 2010), or both (Faulkner 2003, Faulkner 2007b). This Cochrane review updates and extends these recent reviews by focusing on evidence from randomised controlled trials. Furthermore, the recent systematic review by Caemmerer and colleagues (Caemmerer 2012) focused specifically on antipsychotic-related weight gain, and excluded one study as a result. We are interested in identifying and including all randomised controlled trials to reduce or prevent excess weight, regardless of aetiology, in all people with schizophrenia or schizophrenia-like illnesses.

 

Objectives

  1. Top of page
  2. Background
  3. Objectives
  4. Methods
  5. Acknowledgements
  6. Contributions of authors
  7. Declarations of interest
  8. Sources of support

To determine the effects of behavioural strategies for reducing or preventing weight gain in people with schizophrenia.

 

Methods

  1. Top of page
  2. Background
  3. Objectives
  4. Methods
  5. Acknowledgements
  6. Contributions of authors
  7. Declarations of interest
  8. Sources of support
 

Criteria for considering studies for this review

 

Types of studies

We will include all relevant randomised controlled trials. Where a trial is described as 'double-blind', but only implies that the study is randomised, these trials will be included in a sensitivity analysis. If there is no substantive difference within primary outcomes (see types of outcome measures) when these 'implied randomisation' studies are added, then they will be included in the final analysis. If there is a substantive difference, only clearly randomised trials will be used and the results of the sensitivity analysis described in the text. Quasi-randomised studies, such as those allocating by using alternate days of the week, will be excluded.

 

Types of participants

People diagnosed with schizophrenia or schizophrenia-like illnesses (such as schizoaffective disorder, schizophreniform disorder, and delusional disorder) using any criteria. Trials will not be excluded due to age, nationality or sex of participants. Trials will be included regardless of length of the participant's illness, stage of illness, treatment setting, current clinical state, or symptom cluster.

 

Types of interventions

Randomised controlled trials of weight loss (treatment) and weight maintenance (prevention) will be included in this review. To be included in the review, the primary outcome of the trial has to be weight loss or maintenance. All types of behavioural or "lifestyle" interventions will be considered for inclusion. Typically, interventions incorporate dietary and/or exercise components. While the topic of exercise therapy for schizophrenia is the focus of another Cochrane Review (Gorczynski 2010), the primary outcomes assessed within that review are changes in mental health outcomes following exercise, as opposed to weight loss. Additionally, some weight interventions may include cognitive/behavioural components. These treatments attempt to enhance dietary restraint by providing adaptive dietary strategies and by discouraging maladaptive dietary practices, and by increasing motivation to be more physically active (Shaw 2005). Studies will be considered based on the following subcategories.

 

1. Treatment of weight gain

 
1.1 Cognitive/behavioural intervention

These refer to studies promoting changes in diet and/or physical activity including elements of cognitive and/or behavioural modification.

 
1.2. Exercise/dietary intervention

These refer to studies promoting changes in diet and/or physical activity without elements of cognitive and/or behavioural modification.

 
1.3 Cognitive/behavioural intervention plus pharmacological adjunct

These refer to studies promoting changes in diet and/or physical activity including elements of cognitive and/or behavioural modification with an adjunctive pharmacological treatment. Cognitive/behavioural modification caused primarily by a pharmacological adjunct, such as conditioning caused by medication effects, will not be considered part of a cognitive/behavior intervention (e.g. steatorhea and accompanying discomfort caused by orlistat leading to conditioned dietary intake changes).

 
1.4 Exercise/dietary intervention plus pharmacological adjunct

These refer to studies promoting changes in diet and/or physical activity with an adjunctive pharmacological treatment but without elements of cognitive and/or behavioural modification.

 
1.5 Standard care

We define this as care that a person would normally receive had they not been included in the research trial.

 
1.6 Pharmacological adjunct

We define this as any additional medication provided to the participant as part of engaging in the research trial, regardless of current licensing status or whether it was used off-label.

 

2. Prevention of weight gain

 
2.1 Cognitive/behavioural intervention

These refer to studies promoting changes in diet and/or physical activity including elements of cognitive and/or behavioural modification.

 
2.2. Exercise/dietary intervention

These refer to studies promoting changes in diet and/or physical activity without elements of cognitive and/or behavioural modification.

 
2.3 Cognitive/behavioural intervention plus pharmacological adjunct

These refer to studies promoting changes in diet and/or physical activity including elements of cognitive and/or behavioural modification with an adjunctive pharmacological treatment.

 
2.4. Exercise/dietary intervention

These refer to studies promoting changes in diet and/or physical activity with an adjunctive pharmacological treatment but without elements of cognitive and/or behavioural modification (beyond that caused by the pharmacological adjunct, e.g. conditioning caused by medication effects such as steatorhea caused by orlistat).

 
2.5 Standard care

We define this as care that a person would normally receive had they not been included in the research trial.

 
2.6 Pharmacological adjunct

We define this as any additional medication provided to the participant as part of engaging in the research trial, regardless of current licensing status or whether it was used off-label.

 

Types of outcome measures

All outcomes will be divided into short-term follow-up (less than 12 weeks), medium-term follow-up (12-52 weeks) and long-term follow-up (over one year).

 

Primary outcomes

 
1. Weight or another indicator of body mass (e.g. body mass index, waist measurement, waist-to-hip ratio)

1.1 Total body weight (lbs/kg)
1.2 Change in weight
1.3 Total BMI
1.4 Change in BMI
1.5 Total waist circumference
1.6 Change in waist circumference
1.7 Total waist-to-hip circumference ratio
1.8 Change in waist-to-hip circumference ratio
1.9 Total percentage body fat
1.10 Change in percentage body fat
1.11 Any change in weight (as defined by individual studies)*
1.12 Clinically important change in BMI (as defined by individual studies)
1.13 Clinically important change in waist circumference (as defined by individual studies)
1.14 Clinically important change in waist-to-hip circumference ratio (as defined by individual studies)
1.15 Clinically important change in total percentage body fat (as defined by individual studies)

 
2. Leaving the study early

2.1 Any reason
2.2 Adherence to prescribed intervention
2.3 Proportion of sessions attended
2.4 Adherence to guidelines after intervention is complete/during follow-up.

 

Secondary outcomes

 
1. Global measures

1.1 Clinically important change in global measure
1.2 Continuous measures of global state

 
2. Mental state (with particular reference to the positive and negative symptoms of schizophrenia)

2.1 Clinically important change in general mental state
2.2 Average endpoint general mental state score
2.3 Average change in general mental state scores
2.4 Clinically important change in specific symptoms (positive symptoms of schizophrenia, negative symptoms of schizophrenia, depression, mania)
2.5 Average endpoint specific symptom score
2.6 Average change in specific symptom scores

 
3. Well-being and quality of life measures

3.1 Clinically important change in quality of life
3.2 Average endpoint quality of life score
3.3 Average change in quality of life scores
3.4 Clinically important change in specific aspects of quality of life
3.5 Average endpoint specific aspects of quality of life
3.6 Average change in specific aspects of quality of life

 
4. Adverse effects - general and specific

4.1 Clinically important general adverse effects
4.2 Average endpoint general adverse effect score
4.3 Average change in general adverse effect scores
4.4 Clinically important specific adverse effects
4.5 Average endpoint specific adverse effects
4.6 Average change in specific adverse effects
4.7 Death - suicide and natural causes

 
5. Other outcomes measures

5.1 Cardiovascular measures
5.2 Laboratory measures
5.3 Compliance
5.4 Economic outcomes
5.5 Other extractable outcomes.

 
6. '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 (Review Manager) to create 'Summary of findings' tables. These tables provide outcome-specific information concerning the overall quality of evidence from each included study in the comparison, the magnitude of effect of the interventions examined, and the sum of available data on all outcomes rated 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. Weight: total or change
  2. Weight: BMI - total or change
  3. Weight: waist circumference - total or change
  4. Wieght: Waist-to-hip circumference ratio - total or change
  5. Weight: body composition - total or change in percentage fat
  6. Leaving the study early - any reason
  7. Leaving the study early - adherence to prescribed intervention

 

Search methods for identification of studies

 

Electronic searches

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

[((*weight* or *body mass* or * bmi* or *obes* or * eat* or *fat* or *exercise* or *diet* or *sport* or *physical therap* or *physical activit*) in REFERENCE Title, abstract or Index Term fields) or (*diet* or *nutrition* or *exercise* or *weight* in STUDY INTERVENTION) or (*weight* or *obes* or *body mass* or *diet* or * eat* or *waist* in STUDY Health care condition)]

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. Handsearching

If we find any appropriate journals and conference proceedings relating to behavioural interventions for weight management in schizophrenia, we will search these manually, and contact authors when relevant abstracts are found.

 

3. 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 GF and MD will independently inspect citations from the searches and identify relevant abstracts. 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 MD. Any disagreements will be discussed and reported and if consensus cannot be reached, we will obtain the full report and repeat the assessment process until agreement is reached. A random 20% of abstracts will be re-inspected by GF 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. No blinding to the names of authors, institutions and journal of publication will take place.

 

Data extraction and management

 

1. Extraction

Review author MD will extract data from all included studies. In addition, to ensure reliability, GF will independently extract data from a random sample of these studies, comprising 10% of the total. Again, any disagreement will be discussed, decisions documented and, if necessary, authors of studies will be contacted for clarification. With remaining problems MH and GR will help clarify issues and these final decisions will be documented. Data presented only in graphs and figures will be extracted whenever possible, but included only 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 multicentre, where possible, we will extract data relevant to each component centre separately.

 

2. Management

 
2.1 Extraction

We will extract data onto standard, simple forms.

 
2.2 Scale-derived data

We will include continuous data from rating scales only if:

  • the psychometric properties of the measuring instrument have been described in a peer-reviewed journal (Marshall 2000); and
  • 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 the 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 to primarily 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:

  • standard deviations (SDs) and means are reported in the paper or obtainable from the authors;
  • when a scale starts from the finite number zero, the standard deviation (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);
  • 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 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 behavioural interventions. 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 MD and GF 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 MH. 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

 

1.1 Data types

We will assess outcomes using continuous (for example, changes in weight), categorical (for example, one of three categories on a behaviour scale, such as 'little change', 'moderate change' or 'much change') or dichotomous measures (for example, either 'no important changes' or 'important changes' in a person's weight). Currently RevMan does not support categorical data so we will be unable to analyse these.

 

1.2 Intention-to-treat analysis

We will assume that participants who left before study completion e.g. withdrawn by an investigator or left of their own volition, for binary outcomes, to have had a negative outcome. We will test the effects of this assignment in a sensitivity analysis. For continuous data it is impossible to manage the data in this way, therefore we will present 'completer' data.

 

1.3 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.

 

1.4. 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 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 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. 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 to 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

If standard deviations (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 confidence intervals (CIs) available for group means, and either the '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 confidence interval 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 understand that 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. This often seems to be true to us and the random-effects model takes into account differences between studies even if there is no statistically significant heterogeneity. There is, however, a disadvantage to the random-effects model. It puts added weight onto small studies which often are the most biased ones. Depending on the direction of effect, these studies can either inflate or deflate the effect size. We choose random-effects model for all analyses. The reader is, however, able to choose to inspect the data using the fixed-effect model.

 

Subgroup analysis and investigation of heterogeneity

 

1. Subgroup analyses

No subgroup analysis is anticipated

 

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, the graph will be visually inspected and outlying studies will be successively removed 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 SD 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

  1. Top of page
  2. Background
  3. Objectives
  4. Methods
  5. Acknowledgements
  6. Contributions of authors
  7. Declarations of interest
  8. Sources of support

We would like to thank the Ontario Mental Health Foundation for providing financial support for this review. We would also like to thank Claire Irving of the Cochrane Schizophrenia Group for her help and support and Dr Ranganath D Rattehalli for peer reviewing 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 was developed by the Trial Search Co-ordinator of the Cochrane Schizophrenia Group, Samantha Roberts and the contact author of this protocol.

 

Contributions of authors

  1. Top of page
  2. Background
  3. Objectives
  4. Methods
  5. Acknowledgements
  6. Contributions of authors
  7. Declarations of interest
  8. Sources of support

Guy Faulkner, Tony Cohn, and Gary Remington contributed to the original protocol on interventions to reduce weight in schizophrenia (Faulkner 2007).

Mark Duncan updated the protocol to reflect the division between behavioural and pharmacological interventions.

Margaret Hahn assisted in writing the protocol.

 

Declarations of interest

  1. Top of page
  2. Background
  3. Objectives
  4. Methods
  5. Acknowledgements
  6. Contributions of authors
  7. Declarations of interest
  8. Sources of support

Tony Cohn has received speaker fees from Pfizer Canada Inc. Margaret Hahn has received speaker fees from Novartis. Gary Remington has served as a consultant or speaker for Novartis, Laboratorios Farmacéuticos Rovi, and Roche. 

 

Sources of support

  1. Top of page
  2. Background
  3. Objectives
  4. Methods
  5. Acknowledgements
  6. Contributions of authors
  7. Declarations of interest
  8. Sources of support
 

Internal sources

  • University of Toronto, Canada.

 

External sources

  • Ontario Mental Health Foundation, Canada.

References

Additional references

  1. Top of page
  2. Abstract
  3. Background
  4. Objectives
  5. Methods
  6. Acknowledgements
  7. Contributions of authors
  8. Declarations of interest
  9. Sources of support
  10. Additional references
  11. References to other published versions of this review
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References to other published versions of this review

  1. Top of page
  2. Abstract
  3. Background
  4. Objectives
  5. Methods
  6. Acknowledgements
  7. Contributions of authors
  8. Declarations of interest
  9. Sources of support
  10. Additional references
  11. References to other published versions of this review
Faulkner 2007b