Description of the condition
The term 'serious' or 'severe' mental illness is widely used by mental health professionals, but there is no internationally agreed definition for the term, and limited consistency between definitions.
The definition of severe mental illness which is most representative of definitions used in research is that of the National Institute of Mental Health (NIMH) (Schinnar 1990), which has three dimensions.
- Clinical diagnosis: a diagnosis of non-organic psychosis or personality disorder.
- Chronicity: a two-year, or longer history of mental illness or treatment.
- Disability: functional impairment, limiting one or more major life activities (National Institute of Mental Health 1987).
The UK Quality and Outcomes Framework, which encourages General Practices to maintain registers of patients with severe mental illness, uses the following inclusion criteria, based on diagnosis alone: schizophrenia, bipolar disorder and other psychoses (QOF 2009). This is representative of definitions used by the UK Department of Health, and used in practice. Ruggeri 2000 suggested that the total world wide population-based annual prevalence of serious mental illness is approximately two per thousand. Current mental health policy objectives include ensuring optimal quality of life for those with severe mental illness, and providing evidence-based approaches to give people the greatest choice and control over their own lives (DoH 2011).
Those with severe mental illness, especially schizophrenia and schizophrenic-like disorders, often have little to no insight regarding the presence of their illness (McCormack 2013). This means that people with severe mental illness will not understand that they are ill in the same way that third party observers do. The lack of understanding of their illness, ultimately leads to poor treatment compliance and can result in relapse and repeated hospitalisation (Gerhardstein 2013). Some people may feel stigmatised by their illness and may deny its existence, whereas others have a true lack of understanding (Harvey 2013); both, ultimately increase non-compliance. Non-compliance is even more of a problem when people are living in the community and is also often related to the adverse effects of medication, as well as a lack of adequate knowledge about medication (Antai-Otong 1989).
Description of the intervention
Psychoeducation may be defined as the education of a person with a psychiatric disorder regarding the symptoms, treatments, and prognosis of that illness. It is not simply 'providing information', but rather empowering training for patients targeted at promoting awareness, providing tools to manage, cope and live with a chronic psychiatric condition, and changing behaviours and attitudes related to the condition (Colom 2011). Patient education can take a variety of forms and length. Some are as brief as one session (Razali 1997), others are as long as 18 months (Herz 2000). A previous systematic review has shown that the median length of psychoeducation is around 12 weeks (Xia 2011). Therefore, for psychoeducation to be considered 'brief' we have used a cut-off of 10 sessions or less. The terms 'patient education', 'patient teaching', and 'patient instruction' have also been used for this process. All imply that there is a focus on knowledge. The purpose of patient education, ultimately, is to enable the patient to engage in behaviour change and build skills for illness management (Chien 2013). The goal may be to try to prevent hospitalisation or to manage the illness or condition to help the patient attain her/his maximum degree of health and well-being.
How the intervention might work
Education is a gradual process by which a person gains knowledge and understanding through learning. Learning, however, involves more than knowledge and, according to Rankin 1996, it can involve cognitive, affective and psychomotor processes. Learning implies changes in behaviour, skill or attitude (Falvo 1994). Patient education can take a variety of forms depending upon the abilities and interest of the patient and family. For example, the education may take place in small groups or on a one-to-one basis; it may involve the use of videotapes or pamphlets or a combination of these.
Why it is important to do this review
Proposed benefits of psychoeducation as a psychological intervention are that it is clinically focused, straightforward to deliver, and does not require long and complex training (Colom 2011).
However, a key drawback is that psychoeducation traditionally places demands upon therapist time, with programmes often comprising many modules. A recent narrative literature review has suggested that shorter psychoeducation programmes or 'brief psychoeducation' may have long-term positive outcomes in schizophrenia (Rummel-Kluge 2008).
It is therefore important to look at brief psychoeducation programmes.
To assess the efficacy of brief psychoeducational interventions as a means of helping severely mentally ill people when added to 'standard' care, compared with the efficacy of standard care alone.
The secondary objective is to investigate whether there is evidence that a particular kind (individual/ family/group) of brief psychoeducational intervention is superior to others.
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. Where people are given additional treatments within brief psychoeducation, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the brief psychoeducation that is randomised.
Types of participants
Adults suffering from severe mental illness as defined by National Institute of Mental Health 1987. In the absence of a formal diagnosis, we will include people with illness such as schizophrenia, schizophrenia-like disorders, bipolar disorder, depression with psychotic features and/or personality disorder. Studies involving people with dual diagnosis of severe mental illness plus substance abuse will also be included. However, trials involving particIpants with substance abuse alone will not be included. Studies involving people with dementia or mental retardation will also be excluded, as these illnesses are not considered as severe mental disorders. We will include studies involving people with a range of severe mental illness diagnoses but only where the majority of people have a diagnosis of schizophrenia. A majority of the study participants will be required to be within the age range 18 to 65 years.
Types of interventions
1. All didactic interventions of psychoeducation or patient teaching involving individuals or groups considered to be 'brief' will be included. For the purpose of this review, programmes of 10 sessions or less will be considered as 'brief'.
We will define psychoeducational interventions as any group or individual programme involving interaction between information provider and patient. These programmes address the illness from a multidimensional viewpoint, including familial, social, biological and pharmacological perspectives. Patients are provided with support, information and management strategies. Interventions including elements of behavioural training, such as social skills or life skills training, as well as education performed by patient peers, will be excluded from this review. Staff education studies will also be excluded.
2. Standard care is defined as the normal level of psychiatric care provided in the area where the trial was carried out.
Types of outcome measures
All outcomes will be divided into short term (up to 12 weeks), medium term (13-52 weeks) or long term (over 52 weeks) and will be interpreted as defined by each of the studies.
1.1 Compliance with medication
1.2 Compliance with follow-up
1. Global state
1.1 Overall improvement
1.2 Use of additional medication
1.3 Average endpoint in global state score
1.4 Average change in global state scores
1.5 Average dose of drug
2. Mental state
2.1 Clinically important change in general mental state
2.2 Any change in general mental state
2.3 Average endpoint general mental state score
2.4 Average change in general mental state scores
3. Social functioning
3.1 Clinically important change in social functioning
3.2 Any change in social functioning
3.3 Average endpoint in social functioning score
3.4 Average change in social functioning scores
4. Adverse effects/event
4.1 Clinically important general adverse effects
4.2 Any general adverse effects
4.3 Any serious, specific adverse effects
4.4 Average endpoint general adverse effect score
4.5 Average change in general adverse effect scores
4.6 Clinically important change in specific adverse effects
4.7 Any change in specific adverse effects
4.8 Average endpoint specific adverse effects
4.9 Average change in specific adverse effects
5. Quality of life
5.1 Clinically important change in quality of life
5.2 Any change in quality of life
5.3 Average endpoint quality of life score
5.4 Average change in quality of life scores
5.5 Clinically important change in specific aspects of quality of life
5.6 Any change in specific aspects of quality of life
5.7 Average endpoint specific aspects of quality of life
5.8 Average change in specific aspects of quality of life
6.1 Improvement of understanding of his/her illness and need for treatment - recipient/family member
6.2 Level of knowledge about expected and undesired effects of medication - recipient/family member
7.1 Level of psychiatric symptoms
7.2 Symptom control skills
7.3 Problem-solving skills
7.4 Social skills
8. Global functioning
8.1 Clinically important change in general functioning
8.2 Any change in general functioning
8.3 Average endpoint in general functioning score
8.4 Average change in general functioning scores
9. Service utilisation
9.1 Use of outpatient treatment
9.2 Length of hospitalisation
10. Expressed emotion
10.1 Clinically important change in expressed emotion
10.2 Any change in expressed emotion
10.3 Average endpoint general expressed emotion score
10.4 Average change in general expressed emotion scores
11. Satisfaction with care
11.1 Clinically important change in satisfaction
11.2 Any change in satisfaction
11.3 Average endpoint in satisfaction score
11.4 Average change in satisfaction scores
12. Health economic outcomes
12.1 Treatment costs
13. '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 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 will 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:
1.1 Compliance with medication
3. Global state
3.1 Overall improvement
4. Mental state
4.1 Clinically important change in general mental state
5. Social function
5.1 Clinically important change in social functioning
6. Adverse effects
6.1 Clinically important general adverse effects
7. Quality of life
7.1 Clinically important change in quality of life
Search methods for identification of studies
We plan to search the Cochrane Schizophrenia Group register using the phrase:
[*Psychoeducat* in interventions of STUDY]
This register is compiled by systematic searches of major databases, hand searches and conference proceedings (see Group Module).
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 SZ and MBJ will independently inspect citations from the searches and identify relevant abstracts. A random 20% sample will be independently re-inspected by JX 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 SZ. A random 20% of reports will be re-inspected by MBJ 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
Review authors SZ and MBJ will extract data from all included studies. In addition, to ensure reliability, JX 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, we will contact the authors of studies for clarification. With any remaining problems CEA (see Acknowledgements) will help clarify issues and these final decisions will be documented. If we find data presented only in graphs and figures, we will attempt to extract the data whenever possible, but only include 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.
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 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 a 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 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 (BPRS, 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 brief psychoeducation. 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 SZ and MBJ 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 the 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 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 mean difference (MD) between groups. We prefer not to calculate effect size measures (standardised mean difference 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 the 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 126.96.36.199 (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.
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 (ITT)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 ITT analysis using the above assumptions.
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 CIs available for group means, and either '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 I
Heterogeneity between studies will be investigated by considering the I
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.
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 the fixed-effect model for all analyses. The reader is, however, able to choose to inspect the data using the random-effects model.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses
1.1 Primary outcomes
We plan to compare brief group psychoeducation and brief individual psychoeducation, for primary outcomes only.
1.2 Clinical state, stage or problem
We propose to undertake this review and provide an overview of the effects of brief psychoeducation 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 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.
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 fixed-effect model, however, we will also synthesise data for the primary outcome using a random-effects model to evaluate whether this alters the significance of the results.
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 and the contact author of this protocol.
We would like to thank Clive Adams for offering to help with disputes, if they arise, in the review stage of trial selection and data extraction.
We also thank Alia Ahmed for peer reviewing this protocol.
Contributions of authors
JX - development and writing of protocol
SZ - will be primary review author for trial selection and data extraction.
MBJ - help and advice with development and writing of protocol.
Declarations of interest
All authors have no known conflict of interest, however JX recieved a grant from the Cochrane Schizophrenia Group to complete this protocol.
Sources of support
- Cochrane Schizophrenia Group, UK.Provided grant to lead author to help complete this protocol
- Cochrane Collaboration Programme Grant 2011, UK.