Description of the condition
Severe mental illness (SMI) may be defined according to three dimensions: 1. A non-organic psychotic disorder; 2. Treatment duration lasting for two years or more; and 3. Disability resulting in difficulties in social and occupational functioning (Ruggeri 2000). The narrowest definition of psychosis is described as a break in reality testing as manifested by delusions or hallucinations into which an individual has no insight (APA 1994) and subsequently causes disturbances in functionality and relationships, despite ongoing treatment and care. Psychosis is characterised by psychotic symptoms, for example: distortion of thinking and perception, delusions, hallucinations, disordered thinking and blunting or incongruity of emotional responses. The cluster of schizophrenia and related disorders (e.g. schizoaffective disorder, schizophreniform disorder and delusional disorder) are considered the most common psychotic disorders (WHO 1992). Individuals with “early onset psychosis” or “first episode psychosis” and those who are receiving treatment and support from early intervention services are also regarded as having SMI due to similarities in presentation and impact on treatment duration and disability (NICE 2010). Bipolar disorder is characterised by repeated episodes during which the individual’s mood and activity are substantially disturbed, alternating between elevated mood and activity which is often correlated with psychotic symptoms, and decreased energy and activity (WHO 1992).
Onset of SMI tends to peak around the late teenage years and early adulthood. A 2004 review of previous surveys estimated the 12-month prevalence rate of Type 1 bipolar disorder to be 0.72% and the lifetime prevalence rate to be 0.8% (Waraich 2004). The prevalence of schizophrenic disorders based on a 2005 review of surveys in 46 countries (Saha 2005) found a median of 0.4% for lifetime prevalence up to the point of assessment and 0.3% in the 12-month period prior to assessment. Moreover, the lifetime morbid risk, that is the number of people estimated to develop schizophrenia at some point in their life, was estimated to be "about seven to eight individuals per 1000” (0.7/0.8%). The prevalence of schizophrenia was found to be consistently lower in poorer countries than in richer countries but did not differ between men and women or rural or urban dwellers. In addition to the direct impact of SMI on the health of service users, their siblings are also vulnerable to mental ill health due to the negative impact of psychosis within the family (Sin 2012; Smith 2009).
Description of the intervention
Psychoeducation is an intervention which aims to instil information or knowledge on the illness condition and its management (NICE 2010; Xia 2011). Psychoeducational interventions can be delivered as a group or individual programme involving interaction between the information provider and participants, using different delivery modes, including face-to-face (e.g. Smith 1987), online virtual forum (Rotondi 2010), and a mix of different delivery modes (Szmukler 2003). The purpose of health education involving families of service users with SMI is to enhance their understanding of the illness and promote their management and caring of the service users in their usual environment. Therefore, it is also common that these interventions have multiple components which may consist of, for instance: cognitive and/or behavioural training elements, peer support and/or discussion, with a primary aim of enhancing problem-solving and/or coping with caring-related or illness management issues (Xia 2011).
How the intervention might work
Psychoeducational interventions commonly have education as a cardinal feature and prime aim. The education content often includes information on the illness condition and problem solving and coping strategies for common caring issues, such as managing illness symptoms and related problems encountered by family carers (Birchwood 1992; Szmukler 2003). Such theoretical underpinnings suggest that improved knowledge and understanding of the illness can dispel myths, alleviate anxiety and worries and thus distress in family members of individuals affected by SMI (Birchwood 1992; Smith 1990). This may also enhance their optimism and capability in enlisting community resources concerning their roles and their contribution to service users’ ongoing recovery and management (Birchwood 1992). Some earlier studies have demonstrated that short-term and simple educational interventions are effective in improving family carers’ knowledge about the illness and its management, leading to a reduction in their stress levels, perceived burden and sense of fear, anxiety and isolation (Pakenham 1987; Smith 1987). These changes have also been found to correlate with increased optimism in the family’s role in treatment (Smith 1987) and an improved home life environment (Cozolino 1988). The stress-appraisal and coping theory (Lazarus 1966), a theoretical framework commonly used in many psychoeducational interventions (e.g. Szmukler 2003), goes further asserting that increased knowledge is one of the best mediating factors in stress-appraisal, enhancing participants’ perceived efficacy and coping, if the knowledge also impacts on management strategies. Bandura’s self-efficacy theory (Bandura 1977; Bandura 1988) also finds resonance in some psychoeducational interventions, where the intervention itself does not aim to change the caring situation but shape the participants’ self-efficacy (i.e. how well they believe they could cope with the caring situation) and mediate the correlated perceived burden of care and anxieties. It is therefore common that psychoeducational interventions include general problem-solving and coping strategies as a way to enhance coping and self-efficacy. It is well established that high expressed emotion (EE) (Brown 1958; Brown 1962; Brown 1972) is a strong predictor of relapse. Longitudinal studies suggest that EE is strongly correlated with caregiver burden in addition to service users’ relapse rate, in that caregivers experience a higher level of burden when they are emotionally over-involved, critical or hostile to the service users (or their behaviour). Through relieving the burden of care, psychoeducation may also reduce EE (Gonzalez-Blanch 2010). Especially in multi-modal interventions, psychoeducation plays a significant but not exclusive role in the outcomes of the interventions in changing family members’ attitude, perception and behaviour towards the individual with SMI and/or the illness positively (Birchwood 1992; Leff 1989).
Despite the various benefits of psychoeducation for family carers mentioned above, some studies suggest these benefits are sometimes short-lived (e.g. Pakenham 1987; Smith 1987). Moreover, improved knowledge, though often achieved through psychoeducation, does not necessarily have a significant impact on other intricate/primary outcomes, such as EE, family beliefs and behaviour towards the service users with SMI (Birchwood 1992; Chan 2009). Some researchers therefore suggest augmenting psychoeducation with more intensive and complex interventions (such as family therapy and cognitive behaviour therapy) conducted over a longer period of time (Chan 2009; Leff 1989).
Why it is important to do this review
Many people have a sibling; for instance, in the UK over 80% of the general population has at least one sibling (Smith 2009). The sibling relationship often outlives other relationships, including marriages and parenthood (Sin 2012). The quality of the sibling relationship, especially during adolescence and early adulthood, is a predictive factor in siblings’ future involvement in caring for a brother or sister who has SMI (Greenberg 1999), as well as being associated with a higher quality of life (Smith 2007) and a more promising recovery trajectory (Birchwood 2003) for individuals with a diagnosis of SMI. Siblings are both natural agents to promote service users’ recovery and vulnerable to mental ill health due to the negative impact of psychosis within the family (Friedrich 2008; Sin 2008; Sin 2012). Current research into siblings’ experiences and needs suggest that they often do not regard themselves as carers and are hardly involved with statutory health or social services, unlike their parents who often act as the primary carers (Sin 2012; Smith 2009). Nonetheless, siblings’ experiences of subjective and objective burden of caring may be similar to that of the primary carers (Magliano 1999). Similarly, siblings’ adaptation and grief over the onset of psychosis in their brother or sister may be similar to that experienced by other family members (Patterson 2002). A small body of research in early onset psychosis (Sin 2012) and schizophrenia (Friedrich 2008) highlights siblings’ need for information about the illness, ways to promote recovery in the service user and coping strategies, all of which are key elements in many psychoeducation programmes. Existing systematic reviews on psychoeducation (e.g. NICE 2010; Xia 2011) and family intervention (e.g. Pharoah 2010) have focused on the service user and overall family outcomes, missing the opportunity to evaluate the effectiveness of psychoeducational interventions for siblings directly. This systematic review aims to address this knowledge gap by investigating the effectiveness of psychoeducation in improving the wellbeing of siblings of individuals affected by SMI. We also aim to identify the active essential ingredients in such interventions to inform the development of future psychoeducational interventions targeting siblings directly, which may further enhance benefits for service users.
To assess the effectiveness of psychoeducation compared with usual care or any other intervention in promoting wellbeing and reducing distress of siblings of people affected by SMI.
The secondary objective is, if possible, to determine which type of psychoeducation is most effective.
Criteria for considering studies for this review
Types of studies
All relevant randomised controlled trials that compare psychoeducation for siblings of people with SMI with usual care or any other intervention. 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.
Types of participants
Brothers and sisters of all ages of adolescents (aged 11 to 17) and adults (aged 18 and over) with severe mental illness as defined in the former section 'Description of the condition', and treated in any setting. Studies with populations including siblings of people with diagnoses other than SMI as defined by this review, e.g. severe depression/anxiety (as these diagnoses are covered by other Cochrane review groups), will be included but only if ≥ 50% have a psychosis-related disorder or if data specific to siblings of people with SMI are reported independently. Study populations including people other than siblings of individuals with SMI, for instance other family members or carers, will be included if the data specific to siblings are published or obtainable from the study authors.
The definition of siblings is inclusive to incorporate modern society family structures that often extend beyond the traditional or biological families (NICE 2010). Therefore, in addition to biological siblings, half-, adopted-, and step-siblings are included.
Types of interventions
1. Psychoeducation/ Psychoeducational intervention
In a previous Cochrane review (Xia 2011), psychoeducational interventions are defined as programmes involving interaction between information providers and service users and/or carers in either an individual or group format. To qualify as a psychoeducational intervention, the education element that instils knowledge or information on the illness condition and its management, must be significant within the design and be prominent in terms of time duration within the overall content/duration of the multi-modal interventions (comprising at least 50% of the total duration based on the programme’s manual content) and be professionally led, although co-facilitation by a lay-person is not excluded. Brief interventions that focus purely on didactic education or health-information giving using textual or video materials solely, will be classified as bibliotherapy rather than psychoeducation (NICE 2010). Such bibliotherapies, which do not include interactions between the professional facilitator and the participants, will be excluded. Mutual support groups that from the outset are facilitated solely by lay-persons or family members or siblings will also be excluded. The target participants of psychoeducation interventions may be the person with SMI or their family members or both. This review is concerned with psychoeducational interventions that target/include siblings as participants although other family members or relatives and the service users may also be included in the interventions.
We consider interventions with a short duration (10 sessions or less; or where the number of sessions is not stated but are delivered over a 10-week period, or less) as ‘brief’ and interventions of longer duration (more than 10 sessions, or where the number of sessions is not stated but are delivered over a period longer than 10 weeks) as ‘standard’, in line with a previous review on psychoeducation targeting service users with schizophrenia (Xia 2011).
Any intervention that meets the criteria as defined above will be included. Psychoeducational interventions that use different modes of delivery or design may be compared with each other. For studies in which people are given additional treatments within psychoeducation, data will only be included if the adjunct treatment is evenly distributed between groups and it is only psychoeducation that is randomly assigned.
2. Placebo, no intervention, usual or standard care or any other intervention other than psychoeducation
Any intervention other than psychoeducation whose content, mode of delivery and design are clearly defined, e.g. counselling, cognitive behavioural therapy, family therapy, will be included as a comparison, in addition to placebo, no intervention, usual or standard care. Usual or standard care is defined as the normal level of psychiatric care/services provided in the geographical area for siblings where the trial was carried out. These care/services provided for siblings of service users, in most circumstances, are minimal and most often include sign-posting to information and voluntary services for carers/families (Sin 2012; Smith 2009).
Types of outcome measures
Since psychoeducation usually aims to impact on outcomes ranging from immediate changes (such as changes in knowledge) to changes in more intricate behavioural and attitudinal outcomes that may take longer to change, all outcomes will be treated as either short term (less than one month), medium term (two to five months) or long term (more than six months) following completion of the psychoeducational intervention.
1. Siblings’ psychosocial wellbeing
1.1 Average change or endpoint scores in wellbeing scores; generic or specific to the siblings’ adjustment to psychosis in their brother or sister; physical, psychological, social, cognitive, or functioning.
2. Siblings' quality of life
2.1 Average change or endpoint scores in quality of life scores; generic or specific to the siblings’ adjustment to psychosis in their brother or sister; physical, psychological, social, cognitive, or functioning.
3. Siblings’ distress
3.1 Average change or endpoint scores in emotional distress as experienced by siblings specifically depression or anxiety.
3.2 Average change or endpoint scores in worry or fear scales as experienced by siblings.
1. Siblings’ knowledge about SMI
1.1 Average change or endpoint scores in siblings' knowledge of SMI
1.2 Average change or endpoint scores in siblings’ understanding of the service user's illness or behaviour
2. Siblings’ coping (attitude, perception and behaviours towards the service user)
2.1 Average change or endpoint scores in siblings' coping
2.2 Average score/ change in siblings’ perceived efficacy in coping
2.3 Average change in siblings’ attitudes towards the service user or towards SMI
2.4 Average change in siblings’ behaviour towards the service user or towards psychosis
3. Siblings’ perceived social support or use of social/community support services
3.1 Average change in siblings' perception of or perceived social support scores
3.2 Average change in siblings' community and/or social service utilisation
4. Siblings’ satisfaction with the intervention
4.1 Leaving the study early
4.2 Siblings' satisfied with the intervention
4.3 Average change in satisfaction score with care for either siblings or the service users
5. Adverse effects/events affecting siblings
5.1 Any general adverse effects affecting siblings
5.2 Suicide and all causes of mortality in siblings
6. Service users’ mental state
6.1 Any change in service users' general mental state
6.2 Clinically important change in specific symptoms
6.3 Average endpoint general mental state scores
7. Service users’ quality of life
7.1 Average change or endpoint scores in service users’ quality of life
7.2 Average change or endpoint scores in service users’ specific aspects of quality of life, i.e. social functioning
7.3 Average change or endpoint scores in service users' specific aspects of quality of life, i.e. family relationships
8. 'Summary of findings' table
We will use the GRADE approach to interpret findings (Schünemann 2008) and will use GRADE profiler (GARDEPRO) 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 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.
- Siblings' wellbeing
- Siblings' quality of life.
- Siblings’ distress.
- Siblings’ knowledge about SMI.
- Siblings' coping.
- Satisfaction with care for either siblings or the service users.
- Adverse effects/ events affecting siblings.
- Service users' mental state.
Search methods for identification of studies
No language restriction will be applied, within the limitations of the search.
The Trials Search Co-ordinator will search the Cochrane Schizophrenia Group Trials Register register using the phrase:
[(*Sibling* or *brother* or *Sister* or *family* or *relative* or *relation* or *carer*) AND (*Psychoeducat*) in interventions of STUDY or title of REFERENCE) OR (*family Psychoeducat* or *Psychoeducation family* or *Psychoeducational family* 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
We will perform the review and meta-analyses following the recommendations of Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). The analyses will be performed using Review Manager (RevMan 5.1).
Selection of studies
Two review authors (JS and CJ) will independently inspect titles and abstracts from the searches for relevance. A random 20% sample will be independently re-inspected by IJN and EB to ensure reliability. Where disputes arise, the full report will be acquired for more detailed scrutiny. Full reports of any study that appears relevant will be obtained and inspected by JS and CJ who will independently assess each text for eligibility based on the above inclusion criteria. Again, a random 20% of reports will be re-inspected by IJN and EB 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. We will keep a record of all excluded and included studies. If it is not possible to obtain sufficient information to judge whether a study is eligible for inclusion, we will record the study as ‘awaiting assessment’.
Data extraction and management
Review authors JS and CJ will extract data from all included studies. In addition, to ensure reliability, EB and IJN 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, CH 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 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. Partial use of a validated instrument will only be included if complete subscale results are available for interpretation.
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 in ‘other tables’ within the data 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 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 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 JS, CJ and IJN 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, authors of the studies will be contacted 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). For binary data presented in the 'Summary of findings' table, where possible, we will calculate illustrative comparative risks as the number needed to treat/harm (NNT/H) statistic with its confidence intervals is intuitively attractive to clinicians but is problematic both in its accurate calculation in meta-analyses and interpretation (Hutton 2009).
2. Continuous data
For continuous outcomes, we will estimate 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 18.104.22.168 (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 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.
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 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 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 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 to use the random-effects model for all analyses. The reader is, however, able to choose to inspect the data using the fixed-effect model.
We will conduct three syntheses which compare psychoeducation with i) all comparators (treatment as usual (TAU), standard care, placebo, any other active treatment), ii) all comparators, excluding any active treatment (TAU, standard care, placebo only); and iii) any active treatment only.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses - only primary outcomes
1.1 Siblings of service users with different diagnoses
We are interested in whether siblings of service users with different diagnoses (e.g. schizophrenia, Type I bipolar disorder, early onset psychosis) would have similar benefits/effects from the interventions. We propose to undertake comparisons only for primary outcomes to minimise the risk of multiple comparisons.
1.2 Intervention types
We anticipate subgroup analyses investigating the different lengths of intervention durations: interventions with brief duration (10 sessions or less or, where the number of sessions is not stated but which is delivered within 10 weeks or less) and interventions with longer duration (more than 10 sessions or where the number of sessions is not stated but which is delivered in more than 10 weeks). We will also present data on intervention programmes using an individual (i.e. one information provider seeing one participant or participants from one family) and using a group format (i.e. more than two participants or participants from one family/service users involved in the sessions). These data, although synthesised overall, will, if possible, be presented in subgroups. We propose to undertake comparisons only for primary outcomes to minimise the risk of multiple comparisons.
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.
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 with 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.
We acknowledge expert statistical advice from Peter Milligan, Statistician, Florence Nightingale School of Nursing and Midwifery, King's College London.
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.
We would like to thank Johannes Quart and Lisa Oerding for peer reviewing this protocol.
Contributions of authors
All authors prepared the protocol.
Declarations of interest
Authors JS, CH and IJN are working on a randomised controlled trial on developing and evaluating the preliminary efficacy of online psychoeducational intervention for siblings of individuals with first episode psychosis, which is expected to complete by end of 2014.
Sources of support
- None, Not specified.No sources of support provided
- National Institute for Health Research, UK.Jacqueline Sin is funded by a National Institute for Health Research (Doctoral Research Fellowship)