Summary of findings
Description of the condition
Schizophrenia is a group of syndromes, with variable course and prognosis. Schizophrenia is characterised by disorders of perceptions and of form and content of thought (APA 1994).
Schizophrenia is accompanied by significant social or occupational dysfunction (McGrath 2008). The onset of symptoms typically occurs in young adulthood. There are wide variations in reported incidence, psychopathology and course of the illness. A systematic review of epidemiological data indicates that, if the diagnostic category of schizophrenia is considered in isolation, the lifetime prevalence and incidence are 0.30 to 0.66% and 10 to 22 per 100,000 person-years, respectively (McGrath 2008).
Although the precise societal burden of schizophrenia is difficult to estimate, because of the wide diversity of accumulated data and methods employed, cost-of-illness indications uniformly point to disquieting human and financial costs (Mueser 2004). Schizophrenia does not just affect mental health; people with a diagnosis of schizophrenia die 12 to 15 years before the average population, with this mortality difference increasing in recent decades (Saha 2007).
Description of the intervention
Several different psychotherapeutic approaches for schizophrenia have been developed and studied.
Cognitive behavioural therapy (CBT) is defined as a discrete psychological intervention where: i. recipients establish links between their thoughts, feelings or actions with respect to current or past symptoms, and/or functioning; and ii. the re-evaluation of their perceptions, beliefs or reasoning relate to the target symptoms (Jones 2012).
In addition a further component of the intervention involves recipients monitoring their own thoughts, feelings or behaviours with respect to the symptom or recurrence of symptoms; and/or the promotion of alternative ways of coping with the target symptom; and/or the reduction of distress; and/or the improvement of functioning (Jones 2012). CBT for treating psychosis (CBTp) can be standard duration and tends to involve around 16 sessions (12 to 20 sessions) over 4 to 6 months, while brief CBTp involves around 6 to 10 sessions, in less than 4 months.
How the intervention might work
CBT for psychosis focuses on establishing links between thoughts, emotions and behaviours and by challenging dysfunctional thoughts. It challenges delusions using Socratic dialogue and dealing with hallucinations and beliefs underlying the hallucinations. It also uses normalisation techniques as well as behavioural techniques to reduce distress and improve functioning. The key elements of CBTp include: engaging the patient, collaboratively developing a problem list, and deciding on a clear goal for the therapy session. Once the goal had been decided on, a CBTp technique would be used (e.g., guided discovery and Socratic questioning) to identify distortions in thinking style. This would be followed by an agreed task (homework) for the patient to complete by themselves before the following appointment (e.g., attempting to identify these distortions over the next week and trying to correct them). Regular feedback and asking the patient to provide a capsule summary (i.e. personal understanding) of the session are also crucial elements. A formulation (narrative of the person's history) is jointly generated to make sense of the emergence and maintenance of the problem at hand.
Brief CBTp uses the same principles, though therapy is provided within a shorter period of time, focusing on assessment, formulation, working with psychotic symptoms, normalising techniques and relapse prevention.
Why it is important to do this review
CBT is now recognised as an intervention for schizophrenia in clinical guidelines in the United States (American Psychiatric Association; APA 1994) and in the United Kingdom (National Institute for Health and Clinical Excellence; NICE 2009). NICE guidelines suggest that "cognitive behavioural therapy (CBT) is offered to people with schizophrenia. This can be started either during the acute phase or later, including inpatient settings". There is some evidence to suggest that it is effective (Wykes 2008).
There is also some evidence to suggest that brief CBTp has some effect in treating symptoms of schizophrenia (Turkington 2002). If conclusive evidence is found that suggests that brief CBTp is as effective as standard CBTp, it has enormous implications for service delivery, reduction of distress and disability in patients with schizophrenia, and above all, in terms of costs. Finding evidence for therapy that is cost effective is especially important in the current economic climate (Turkington 2002).
This review will also add to the findings of other similar Cochrane reviews assessing the effectiveness of CBT for people with schizophrenia. See Table 1.
To compare the effects of brief cognitive behavioural therapy for people with schizophrenia against standard cognitive behavioural therapy for schizophrenia.
Criteria for considering studies for this review
Types of studies
All relevant randomised controlled trials. If a trial was described as 'double blind' but implies randomisation, we planned to include such trials in a sensitivity analysis (see Sensitivity analysis). If their inclusion did not result in a substantive difference, they were to remain in the analyses. If their inclusion did result in important, clinically-significant but not necessarily statistically-significant differences, we were not going to add the data from these lower quality studies to the results of the better trials, but would have presented such data within a subcategory. We also decided to exclude quasi-randomised studies, such as those allocating by alternate days of the week.
Where people were given additional treatments within brief CBTp, we planned to include data if the adjunct treatment was evenly distributed between groups and it was only the brief CBTp that was randomised.
Types of participants
Adults, however defined, with schizophrenia or related disorders, including schizophreniform disorder, schizoaffective disorder and delusional disorder, by any means of diagnosis.
We were interested in making sure that information is as relevant to the current care of people with schizophrenia as possible, so proposed to highlight the participants' current clinical state (acute, early post-acute, partial remission, remission) as well as the stage (prodromal, first episode, early illness, persistent) and whether the studies primarily focused on people with particular problems (for example, negative symptoms, treatment-resistant illnesses).
Types of interventions
Brief cognitive behavioural therapy for psychosis (CBTp) versus standard CBTp .
The Jones 2012 Cochrane review defined standard CBTp as a discrete psychological intervention in which:
- Recipients establish links between their thoughts, feelings or actions with respect to the current or past symptoms, and/or functioning; and
- The re-evaluation of their perceptions, beliefs or reasoning relate to the target symptoms.
In addition, a further component of the intervention should involve the following:
- Recipients monitor their own thoughts, feelings or behaviours with respect to the symptom or recurrence of symptoms; and/or
- The promotion of alternative ways of coping with the target symptom; and/or
- The reduction of distress; and/or
- The improvement of functioning.
According to NICE guidelines (NICE 2009) CBTp should be provided on a one-to-one basis, in around 16 sessions (between 12 to 20 sessions), and using a manual over 4 to 6 months.
We define brief CBTp as the same as standard CBTp except that treatment is delivered within 6 to 10 regular sessions given in less than 4 months and using a manual.
Types of outcome measures
All outcomes were to be divided into short-term (within 6 months of the onset of therapy), medium-term (within 6 to 12 months of the onset of therapy) and long-term (over 12 months since the onset of therapy).
1. Global state
1.1 Clinically-important response as defined by the individual studies (for example global impression less than much improved, or less than 50% reduction on a specified rating scale).
2. Leaving the study early
3. Mental state
3.1 Clinically-important change in general mental state
3.2 Any change in general mental state
3.3 Average endpoint general mental state score
3.4 Average change in general mental state scores
3.5 Clinically-important change in specific symptoms
3.6 Any change in specific symptoms
3.7 Average endpoint specific symptom score
3.8 Average change in specific symptom scores
4. Service use
4.1 Clinically-important engagement with services
4.2 Any engagement with services
4.3 Average endpoint engagement score
4.4 Average change in engagement scores
4.5 Compliance with medication/treatment
4.6 Number of hospitalisations
4.7 Number of days in hospital
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
1.1 Any cause (except suicide)
1.2 Sudden unexpected suicide
2. General functioning
2.1 Average endpoint general functioning score
2.2 Average change in general functioning scores
2.3 Clinically-important change in specific aspects of functioning, such as social or life skills
2.4 Any change in specific aspects of functioning, such as social or life skills
2.5 Average endpoint specific aspects of functioning, such as social or life skills
2.6 Average change in specific aspects of functioning, such as social or life skills
3. Satisfaction with treatment
3.1 Leaving the study early: specific reason
3.2 Recipient of care satisfied with treatment
3.3 Recipient of care average satisfaction score
3.4 Recipient of care average change in satisfaction scores
3.5 Carer satisfied with treatment
3.6 Carer average satisfaction score
3.7 Carer average change in satisfaction scores
4. Adverse effects
4.1 Any general adverse effects
4.2 Average endpoint general adverse effect score
4.3 Average change in general adverse effect scores
4.4 Clinically-important change in specific adverse effects
4.5 Any change in specific adverse effects
4.6 Average endpoint specific adverse effects
4.7 Average change in specific adverse effects
5. Economic costs
We planned to carry out economic appraisal.
Main outcomes for 'Summary of findings' table
We planned to use the GRADE approach to interpret findings (Schünemann 2008) and use GRADE profiler (GRADE PRO) to import data from RevMan 5.2 (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 rate as important to patient care and decision making. We aimed to select the following main outcomes for inclusion in the 'Summary of findings' table:
- Global state
- Leaving the study early
- Mental state
- Service use
- Quality of life
- Satisfaction with treatment
- Economic outcomes
Where possible, we planned to use binary outcomes of clear clinical utility.
Search methods for identification of studies
1. Cochrane Schizophrenia Group’s Trials Register
The Trials Search Coordinator (TSC) searched the Cochrane Schizophrenia Group’s Registry of Trials using the following phrase (Auguest 21, 2013):
(*Cognitive* or *Cognitive Behavioural Therapy*) in Interventions Field of STUDY
The Cochrane Schizophrenia Group’s Registry of Trials is compiled by systematic searches of major resources (including AMED, BIOSIS, CINAHL, EMBASE, MEDLINE, PsycINFO, PubMed, and registries of Clinical Trials) and their monthly updates, handsearches, grey literature, and conference proceedings (see Group Module). There are no language, date, document type, or publication status limitations of inclusion of records in the register.
Searching other resources
1. Reference searching
We inspected the references of all identified studies for further relevant studies.
2. Personal contact
We also planned to contact the first author of each included study for information regarding unpublished trials.
Data collection and analysis
Selection of studies
Two authors (FN and SF) independently inspected citations from the searches and identified relevant abstracts. A random 20% sample was independently re-inspected by DK to ensure reliability. Full reports of the abstracts meeting the review criteria or references/abstracts authors disagreed on, were obtained and inspected by FN and SF. Again, a random sample of 20% of reports were re-inspected by DK in order to ensure reliable selection. Where it was not possible to resolve disagreement by discussion, we planned to contact the authors of the study for clarification. However, this did not happen. Review authors were not blinded to the name(s) of the study author(s), their institution(s) or publication sources at any stage of the review.
Data extraction and management
One author (FN) extracted data from all included (or excluded in this case) studies. In addition, to ensure reliability, SF independently extracted data from a random sample of these studies, comprising three of the total. Again, any disagreement was to be discussed, decisions documented and, if necessary, authors of studies were to be contacted for clarification. With remaining problems DK was to help clarify issues and these final decisions were to be documented. Data presented only in graphs and figures were planned to be extracted whenever possible, but would have be included only if two review authors independently had the same result. We planned to contact authors through an open-ended request in order to obtain missing information or for clarification whenever necessary. If studies were multi-centre, where possible, we had planned to extract data relevant to each component centre separately. However, we did not undertake these steps as none of the studies fulfilled the review's inclusion criteria.
Data would have been extracted onto standard, simple forms.
2.2 Scale-derived data
We planned to include continuous data from rating scales only if:
a. the psychometric properties of the measuring instrument had been described in a peer-reviewed journal (Marshall 2000); and
b. the measuring instrument had not been written or modified by one of the trialists for that particular trial.
Ideally the measuring instrument should have been either 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 planned to note if this was 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 decided to primarily use endpoint data, and only use change data if the former were not available. Endpoint and change data were to be combined in the analysis as we were going to use mean differences (MD) rather than standardised mean differences (SMDs) 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 aimed to apply the following standards to all data before inclusion: a) standard deviations and means are reported in the paper or obtainable from the authors; b) when a scale starts from the finite number zero, the standard deviation, 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) which can have values from 30 to 210) the calculation described above was modified to take the scale starting point into account. In these cases skew is present if 2SD>(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 endpoint data from studies of less than 200 participants were to be entered as 'Other data' within the 'Data and analyses' section of the review, rather than into statistical analysis. Skewed endpoint data pose less of a problem when looking at means if the sample size is large and data from trials with over 200 participants are entered into syntheses.
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. Skewed change data were to be entered into statistical analysis.
2.5 Common measure
To facilitate comparison between trials, we intended 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, we planned 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 2005a; Leucht 2005b). If data based on these thresholds were not available, we planned to use the primary cut-off presented by the original authors.
2.7 Direction of graphs
Where possible, we planned to enter data in such a way that the area to the left of the line of no effect indicates a favourable outcome for brief CBTp compared with standard CBTp. Where keeping to this made it impossible to avoid outcome titles with clumsy double-negatives (e.g. 'Not un-improved') we planned to report data where the left of the line indicates an unfavourable outcome. This was to be noted in the relevant graphs.
2.8 Economic data
No studies were included in this review.
Assessment of risk of bias in included studies
No trials were included, if trials had been included FN was to assess risk of bias by using criteria described in the Cochrane Handbook (Higgins 2011). The set of criteria is based on evidence of associations between overestimate of effect and high risk of bias in study domains such as sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting. If trials had been included SF would have indpendently assessed a random sample of included trials for risk of bias, to ensure reliability.
Again, if the raters had included trials, where there was disagreement, the final rating was to be made by consensus, with the involvement of DK. Where inadequate details of randomisation and other characteristics of trials were provided, we planned to contact authors of the studies in order to obtain further information. Non-concurrence in 'Risk of bias' assessment was to be reported, but if disputes arose as to which rating a domain was to be allocated, resolution was to be made by discussion.
The level of risk of bias was to be noted in both the text of the review and in the 'Summary of findings' table, and reported in 'Risk of bias' tables.
Measures of treatment effect
1. Binary data
For binary outcomes we planned to calculate a standard estimation of the risk ratio (RR) and its 95% confidence interval (CI). It has been shown that RRs are more intuitive (Boissel 1999) than odds ratios and that odds ratios tend to be interpreted as RRs by clinicians (Deeks 2000). The number needed to treat for an additional harmful outcome (NNTH) 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 planned to calculate illustrative comparative risks.
2. Continuous data
For continuous outcomes we planned to estimate mean difference (MD) between groups. We preferred not to calculate effect size measures (standardised mean difference (SMD)). However, if scales of considerable similarity were used, we were going to presume there was a small difference in measurement, and we were going to 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, confidence intervals 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 planned to present data in a table, with a (*) symbol to indicate the presence of a probable unit of analysis error. In subsequent versions of this review we planned to seek to contact first authors of such studies to obtain intra-class correlation coefficients (ICCs) for their clustered data and to adjust for this using accepted methods (Gulliford 1999).
Where clustering was incorporated into the analysis of primary studies, we planned to present these data as if from a non-cluster randomised study, but adjust for the clustering effect.
Statistical advice suggested 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 were been appropriately analysed taking into account ICCs and relevant data documented in the report, synthesis with other studies would be possible using the generic inverse variance technique.
2. Cross-over trials
A major concern of cross-over trials is the carry-over effect. It occurs if an effect (e.g. pharmacological, physiological or psychological) of the treatment in the first phase is carried over to the second phase. As a consequence, on entry to the second phase the participants can differ systematically from their initial state despite a wash-out phase. For the same reason, cross-over trials are not appropriate if the condition of interest is unstable (Elbourne 2002). As both effects are very likely in severe mental illness, we would only have used data from the first phase of cross-over studies.
3. Studies with multiple treatment groups
Where a study involved more than two treatment arms, if relevant, the additional treatment arms were to be presented in comparisons. If data were binary these were to be simply added and combined within the two-by-two table. If data were continuous we planned to combine data following the formula in section 22.214.171.124 of the Cochrane Handbook (Higgins 2011). Where the additional treatment arms were not relevant, these data were not to be reproduced.
Dealing with missing data
1. Overall loss of credibility
At some degree of loss of follow-up, data must lose credibility (Xia 2009). If, for any particular outcome, more than 50% of data were unaccounted for, we planned not to reproduce these data or use them within analyses. If, however, more than 50% of those in one arm of a study were lost, but the total loss was less than 50%, we were going to address this within the 'Summary of findings' table/s by downgrading quality. We also planned to downgrade quality within the 'Summary of findings' table/s should the loss be 25% to 50% in total.
In the case where attrition for a binary outcome was between 0% and 50% and where these data were not clearly described, we planned to present data on an intention-to-treat (ITT) basis. Those leaving the study early were all assumed to have the same rates of negative outcome as those who completed, with the exception of the outcome of death and adverse effects. For these outcomes the rate of those who stayed in the study - in that particular arm of the trial - was to be used for those who did not. We planned to undertake a sensitivity analysis testing how prone the primary outcomes were to change when data only from people who complete the study to that point were compared to the ITT analysis using the above assumptions.
In the case where attrition for a continuous outcome was between 0% and 50%, and data only from people who complete the study to that point were reported, we planned to reproduce these.
3.2 Standard deviations
If standard deviations (SDs) were not reported, we planned to first try to obtain the missing values from the study authors. If not available, where there were 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 planned to calculate them according to the rules described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). When only the SE was reported, SDs were to be calculated by the formula SD = SE * square root (n). Chapters 7.7.3 and 16.1.3 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) present detailed formula for estimating SDs from P values, t or F values, CIs, ranges or other statistics. If these formula did not apply, we were going to 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 planned to examine the validity of the imputations in a sensitivity analysis excluding imputed values.
3.3 Last observation carried forward
We anticipated that in some studies the method of last observation carried forward (LOCF) would be employed. 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 were reported, if less than 50% of the data had been assumed, we planned to present and use these data and indicate that they were the product of LOCF assumptions.
Assessment of heterogeneity
1. Clinical heterogeneity
We planned to consider all included studies initially, without seeing comparison data, to judge clinical heterogeneity. We were to simply inspect all studies for clearly outlying people or situations which we had not predicted would arise. When such situations or participant groups arose, these were to be fully discussed.
2. Methodological heterogeneity
We planned to consider all included studies initially, without seeing comparison data, to judge methodological heterogeneity. We planned to inspect all studies for clearly outlying methods which we had not predicted would arise. When such methodological outliers arose, these were to be fully discussed.
3. Statistical heterogeneity
3.1 Visual inspection
We planned to visually inspect graphs to investigate the possibility of statistical heterogeneity.
3.2 Employing the I
We planned to investigate heterogeneity between studies 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 (Egger 1997). These are described in section 10.1 of the Cochrane Handbook (Higgins 2011). We planned to locate protocols of included randomised trials. If the protocol was available, outcomes in the protocol and in the published report were to be compared. If the protocol was not available, outcomes listed in the methods section of the trial report was to be compared with the reported results.
2. Funnel plot
Funnel plots may be useful in investigating reporting biases, but are of limited power to detect small-study effects. We decided not to use funnel plots for outcomes where there were 10 or fewer studies, or where all studies were of similar size. In other cases, where funnel plots were possible, we planned to 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, while the random-effects model takes into account differences between studies even if there is no statistically-significant heterogeneity. There is, however, a disadvantage of the random-effects model. It puts added weight onto small studies which often are the most biased. Depending on the direction of effect these studies can either inflate or deflate the effect size. We planned to apply a random-effects model for all analyses because of the heterogeneity of the data available.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses - only primary outcomes
We proposed to assess the effects of brief CBTp for people with schizophrenia in general. In addition, we decided to try to report data on subgroups of people in the same clinical state, stage and with similar problems.
2. Investigation of heterogeneity
If inconsistency was high, this was to be reported. First we were going to investigate whether data were entered correctly. Second, if data were correct, the graph was to be visually inspected and outliers were to be successively removed to see if homogeneity was restored. For this review we decided that should this occur with data contributing to the summary finding of no more than around 10% of the total weighting, data would be presented. If not, data would not be pooled and issues would 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 were obvious, we were going to state hypotheses regarding these for future reviews or updates of this review.
1. Implication of randomisation
We aimed to include trials in a sensitivity analysis if they were described in some way as to imply randomisation. For the primary outcomes we planned to include these studies and if there was no substantive difference when the implied randomised studies were added to those with a better description of randomisation, then all data were to be employed from these studies.
2. Assumptions for lost binary data
Where assumptions had to be made regarding people lost to follow-up, or missing SDs (see Dealing with missing data), we planned to compare the findings of the primary outcomes when we used our assumption compared with completer data only. If there was a substantial difference, we planned to report results and discuss them but continue to employ our assumption.
3. Risk of bias
We planned to analyse the effects of excluding trials that were judged to be at high risk of bias across one or more of the domains of randomisation (implied as randomised with no further details available), allocation concealment, blinding and outcome reporting for the meta-analysis of the primary outcome. If the exclusion of trials at high risk of bias did not substantially alter the direction of effect or the precision of the effect estimates, then data from these trials were to be included in the analysis.
4. Imputed values
We also planned to 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 were noted in the direction or precision of effect estimates in any of the sensitivity analyses listed above, we planned to not pool data from the excluded trials with the other trials contributing to the outcome, but present them separately.
5. Fixed-effect and random-effects
All data were to be synthesised using a random-effects model, however we were going to synthesise data for the primary outcome using a fixed-effect model to evaluate whether the greater weights assigned to larger trials with greater event rates, altered the significance of the results compared to the more evenly distributed weights in the random-effects model.
Description of studies
We did not find any studies that fulfilled the inclusion criteria.
Results of the search
We found 576 records through electronic searching of the Cochrane Schizophrenia Register; 262 of these were duplicates leaving 173 records for screening (Figure 1). After screening, 53 full text articles were obtained for further assessment but only 7 were potentially relevant, these were closely assessed for inclusion but none of these could eventually be included in the review. Seven studies therefore are in the Excluded studies section of the review.
|Figure 1. Study flow diagram.|
There are no included studies in this review.
We assessed seven studies carefully for inclusion but all were excluded as none compared brief CBTp to standard CBTp. Four excluded studies used interventions that were not brief CBTp, such as compliance therapy (Kemp 1998, O’Donnell 2003) or group CBT (Levine 1998). One study compared brief CBT for psychosis with care as usual for in-patients with psychosis. This group used a five week CBTp programme, with 15 to 20 hours of therapy but did not specify the number of sessions and compared this to supportive therapy (Lewis 2002). Turkington 2000 conducted a randomised controlled trial of brief CBT for psychosis delivered by experts, compared with befriending. Two trials compared brief CBTp to standard care rather than standard CBTp (Turkington 2002; Wykes 2005).
There are no ongoing studies of which we are aware.
There are no trials currently awaiting assessment.
Risk of bias in included studies
No studies could be included in this review, hence we were unable to assess risk of bias.
Effects of interventions
Excluded studies demonstrate that trials of brief CBTp are possible, but no trials comparing standard duration therapy have been conducted. We had hoped to gather information on global and mental state, issues around use of services, quality of life, satisfaction with treatment and costs. Such data are not available from randomised trials of care ( Summary of findings for the main comparison).
1. Definition of 'brief'
We defined brief CBTp as therapy comprising 6 to 10 sessions delivered in less than 4 months. This cut-off was based on the observation that current standard CBTp treatments typically span 12 to 20 sessions over 4 to 6 months (NICE 2009). We located empirical studies of the efficacy of brief CBTp by asking experts in a variety of areas about available research and by searches of Psychological Abstracts. In the absence of a clear definition for schizophrenia, we adopted our definition after a careful review of the literature on brief CBT in depression. Currently there is more literature on brief CBT for depression and anxiety disorders than for schizophrenia. Although standard CBT for depression is considered by most to be delivered between 10 and 20 sessions (for example, Cully 2008; Hazlett-Stevens 2002), there is no agreement as to how many sessions should be included in brief CBT for depression. Churchill et al (Churchill 2001) described brief psychological interventions for depression to be delivered in 20 or fewer sessions, while Cully 2008 described brief CBT for depression to be delivered in between 4 and 8 sessions. We think that the definition of 'brief CBT' used in this review is reasonable and in broad agreement with practitioners' views.
2. Dearth of evidence
We did not find any study which compared brief CBT for psychosis (CBTp) with the standard form of CBTp. Seven studies had some form of brief therapy used for schizophrenia and could be relevant but none of these studies met the inclusion criteria. The literature on brief CBTp is practically nonexistent, as even those studies which employed brief therapy in one of the arms (but without comparison to standard CBTp) did not clearly meet the criteria for ‘brief’ therapy’. We structured our review by diagnostic category, as there has been no empirical investigation of the efficacy of brief CBTp across different disorders (Bond 2002).
We found seven studies which used brief CBT for schizophrenia (6 to 10 sessions), but none compared brief CBTp with standard CBTp - the simple 'dose-ranging' question of this review. Researchers were more interested in the effects the brief CBTp versus other - different - approaches. Two studies used other techniques (psycho-education - Kemp 1998; O’Donnell 2003) or formats (group CBTp - Levine 1998; Wykes 2005). One study compared CBT for psychosis with care as usual in in-patients with psychosis (Lewis 2002). Lewis 2002 used a 5 week CBTp programme with 15 to 20 hours of therapy, but did not specify the number of sessions. Turkington 2000 is a trial of brief CBT for psychosis versus befriending and Turkington 2002 a randomised trial of brief CBTp delivered by trained nurses versus treatment as usual. The Wykes 2005 study compared seven weeks of group CBTp against care as usual for voices.
It is easy to surmise, but difficult to be sure as to why there is a dearth of evidence for the comparison which is the focus of this review. The firm evidence is that we did not find any studies. We cannot know if brief CBTp is as effective, less effective or even more effective than standard courses of the same therapy. This lack of evidence for brief CBTp has serious implications for research and practice.
Summary of main results
We did not find any study which compared brief CBTp with the standard form of CBTp. Seven studies used some form of brief therapy for schizophrenia and could be relevant, but none of these studies met the review's inclusion criteria.
Potential biases in the review process
Although as authors we have interests in CBT for psychosis (FN has published on CBT for psychosis and culturally-adapted CBT for psychosis and DK has pioneered CBT for psychosis techniques.
Potential biases in the review process are limited by following Cochrane methodology. The search for trials was thorough with no language, date, document type, or publication status limitations. We strictly followed the review protocol in the process of study selection, data extraction and analysis.
Agreements and disagreements with other studies or reviews
We know of no other reviews focusing on this comparison.
Implications for practice
For people with schizophrenia
Cognitive behavioural therapy (CBT) may have benefit for people with schizophrenia but this has not been convincingly shown by fair testing and review of trials (Buckley 2007; Jones 2012). If offered the therapy, people with schizophrenia may wish to opt for the standard course, a brief course or none at all. All would seem reasonable choices given the dearth of evidence. If brief therapy is an option, and agreed upon, it may be that the person with schizophrenia would want to help with generation of higher-grade evidence than this review currently attains.
The conclusions of Jones 2012 (standard duration CBTp versus psychological interventions for schizophrenia) state "trial-based evidence suggests no clear and convincing advantage for cognitive behavioural therapy over other - and sometime much less sophisticated - therapies for people with schizophrenia." This finding concurs with that of the review of supportive therapy for schizophrenia (Buckley 2007), whose 2013 (in press) update states "when we compared supportive therapy to cognitive behaviour therapy, we again found no significant differences in primary outcomes." Clinicians are, therefore, left in a difficult position - being advised to provide around 16 sessions of CBT (NICE 2009) - but often being unable to provide this duration of therapy (Kingdon 2006). If the therapy is available, there is no evidence that a brief course is contraindicated. It seems likely that offer of the longer course will result in more commitment of finite resources and, therefore, less resources for other treatments.
For funders and managers
NICE guidelines recommend that CBT should be provided for all patients with schizophrenia (NICE 2009), using a manual and around 16 sessions. However, the same guidelines describe most studies as delivering between 12 and 20 sessions. Current evidence suggests that only about 50% of those suffering from schizophrenia in the United Kingdom have access to CBT (Kingdon 2006).
One way to overcome this huge gap in the provision of CBTp is to provide brief CBTp. This has the potential to reduce the gap by almost half if the effectiveness of brief CBT can be demonstrated against standard CBT. Increasingly CBTp is also being provided using online tools or mobile phone-based applications (for example clintouch.com). Brief CBTp will also be better suited to this form of intervention delivery, especially through the use of mobile phone applications ('apps'), but also through use of guided self-help material. If, however, the effectiveness of brief CBTp cannot be demonstrated against standard CBTp, and the effectiveness of even the latter is open to interpretation and doubt (Buckley 2007; Jones 2012), commissioners and funders of care may, understandably, wish to consider if investment in this area is a priority.
Implications for research
Excluded studies suggest further reviews relevant to CBTp are indicated ( Table 2). We feel that the consideration of the brief versus standard duration of CBTp remains a legitimate comparison. It may, however, be appropriate that an update of this review should expand the review's scope to 'brief cognitive behavioural therapy for people with schizophrenia' and so allow other comparisons involving a brief therapy to be included.
2. Randomised trials
An important question to be addressed in future research is whether brief CBT can be feasible in psychotic disorders. There are studies which compare brief with standard CBT for non-psychotic disorders (Bond 2002). Many CBT treatments for non-psychotic disorders lead to significant clinical improvement and symptom reduction, relative to other forms of psychotherapy, when delivered in a brief format (Bond 2002). Some approaches to increase the efficiency of CBT treatments include adapting individual treatments to a group format, self-help materials, biblio-therapy and eMedia-assisted therapy programs. The most common approach for enhancing efficiency, however, is to abbreviate existing CBT treatments by reducing the number of treatment sessions.
Brevity has many clear advantages. Increased cost-effectiveness could make treatment accessible to more individuals in need of assistance. Patients enjoy rapid treatment gains, and this may also improve the credibility of the treatment and increase the motivation for further change (Hazlett-Stevens 2002). However, this approach may be disadvantageous in some circumstances. An abbreviated CBT approach assumes that the target for change is clearly defined and circumscribed. Patients presenting with more diffuse symptoms or with particular comorbid conditions that interfere with directly targeted programs may need more lengthy treatment. Brief CBT puts a greater burden on the patient to engage actively in treatment both during and between sessions. It can be argued that in psychotic disorders, especially with symptoms such as severe auditory hallucinations, brief therapy may not work as engaging patients and overcoming psychotic phenomenon need a prolonged and intensive treatment approach. It is also possible that brief therapy may leave patients more confused, and could prove harmful. However, the literature on the use of brief CBT for non-psychotic disorders does not seem to substantiate these apprehensions.
There is some evidence to suggest that brief therapies work in psychosis, but the research in this area needs to address the fundamental issue of the dose-effect relationship in CBT. This is especially important to provide information to the service providers, funders, researchers, reviewers and the user groups. The dose of therapy not only depends upon duration (brief versus long) but also on number of sessions, time for each session (for example number of hours), and intensity of therapy. Other factors that should be taken into consideration in this regard should be description of therapy (for example use of a manual), therapist’s training, fidelity to CBT model (for example use of CBT Scale) and expertise. In a recent Cochrane review (Jones 2012) which included 30 studies describing 20 trials, it was found that only 11 trials met the criteria for well-defined CBT, and 13 trials met the criteria for qualified therapists. In the future, trials of CBT for psychosis (or, for that matter, any psychological treatment) need to include some measure of the 'effective dose' of a specific therapy. This will add to further standardisation of measures of effect and dose of therapy required to bring about change.
There is a need for randomised trials to compare brief CBTp with standard CBTp. These trials should further focus on evaluating cost. This comparison is very important as brief CBTp might provide a solution for patients with schizophrenia in areas where resources and training are limited. There is also a need for clearer definitions of standard and brief CBTp. Finally, this review also highlights one very important issue that needs further research, that of 'effective dose of CBT', as currently there is no research on measurement of 'dose' (quantity of therapy and time period as well as therapy and therapist factors) of CBTp and effect on psychotic symptoms.
We offer a draft design for a trial in this area, in Table 3
We thank the editorial staff of the Cochrane Schizophrenia Group for their support in preparing this review.
We also thank Emily Beetschen for peer reviewing the protocol and for her helpful comments and Chris Jones for peer reviewing the finished review.
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.
Data and analyses
This review has no analyses.
Contributions of authors
Farooq Naeem - completion of protocol, trial selection, data extraction of excluded studies, write up of report.
Saeed Farooq - completion of protocol, trial selection, data extraction of sample of excluded studies, write up of report.
David Kingdon - completion of protocol, help with trial selection, advice with completion of report
Declarations of interest
Farooq Naeem - has published on CBT for psychosis and other disorders and has developed a model of adaptation of CBT in non-Western cultures, adapting CBT for psychosis and depression.
Saeed Farooq - has experience of conducting literature reviews on psychosis-related topics. SF has published a Cochrane systematic review and also systematic reviews and meta-analyses in peer-reviewed scientific journals.
David Kingdon - has pioneered the use of CBT for psychosis and has published widely on this issue.
Sources of support
- Department of Psychiatry, Queens University, Kingston, ON, Canada, UK.Employer of author
- Staffordshire University & Black Country Social Partnership NHS Foundation Trust, Wolverhampton, UK.Employer of author
- University of Southampton, Southampton, UK.Employer of author
- NIHR Grant 2011, Reference number: 10/4001/15, UK.Funding provided by the NIHR to enable completion of this review.
Differences between protocol and review
As a result of a literature review, we further clarified the difference between standard and brief CBT for psychosis, as "standard CBT for psychosis tends to involve around 16 sessions (12 to 20 session) over 4 to 6 months, while brief CBT involves around 6 to 10 sessions, in less than 4 months".