Cognitive behavioural therapy without medication for schizophrenia

Objectives

This is a protocol for a Cochrane Review (intervention). The objectives are as follows:

To investigate the effects of CBT for schizophrenia when administered without a concomitant pharmacological treatment with antipsychotics.

Background

Schizophrenia is a chronic and severe psychiatric disorder that is seen in approximately 1% of the population and which causes significant functional loss (McGrath 2008).

Antipsychotic drugs are effective for the acute treatment and relapse prevention of the disorder (Huhn 2019, Schneider‐Thoma 2022), but are associated with burdensome side effects which are likely to contribute to excess mortality associated with the disorder (Hjorthøj 2017).

Psychotherapeutic interventions for schizophrenia have been developed to address the various aspects of the disorder and are widely recommended in accordance with the guidelines of the National Institute of Clinical Excellence (NICE) (NICE 2014). These interventions are usually offered in combination with antipsychotic medications, so that the separate roles of psychological and of pharmacological treatment could not be ascertained so far (Bighelli 2020).

There have been attempts to provide psychotherapy with cognitive behavioural therapy (CBT) to participants that were not receiving antipsychotic medication (Morrison 2012, Morrison 2014). These studies could be an opportunity to determine the role of psychotherapy alone in improving the symptoms of schizophrenia.

In the current Cochrane Review, we will summarise all randomised controlled trials (RCTs) that investigated CBT provided without concomitant antipsychotic medication compared to the combination of CBT and medication, medication alone, or placebo.

Description of the condition

Schizophrenia is a chronic and severe psychiatric disorder affecting approximately 1% of the population worldwide (McGrath 2008). The onset typically occurs in the second decade of life (Kirkbride 2017), and usually has a significant impact in terms of quality of life, functioning, social inclusion and disability. According to the Global Burden of Disease Study 2019, schizophrenia is ranked 9th in terms of years lived with disability (YLDs) in the age range 15‐49 years (http://www.healthdata.org/gbd/gbd-2019-resources).

The typical symptom manifestations of the condition include severe thought disturbances, which may lead to delusions (beliefs that are not based on reality) and hallucinations, for example, hearing or seeing things that are not there. These manifestations are usually defined as 'positive' symptoms, because they are unusual by their presence. By contrast, 'negative' symptoms are unusual by their absence, and can include a restricted range and intensity of emotional expression and a reduced ability to experience pleasure.

Difficulties with concentration, attention and motivation may also lead to reduced participation or abandoning education activities, and to reduced employment; it is estimated that up to 80% of patients with schizophrenia are not employed (Marwaha 2004).

In the course of the disease, different stages can be identified. In the onset or prodromal phase, subtle modifications in the person's behaviour, cognition and feelings can be identified, which then develop into clear psychotic symptoms during the acute phase. After the acute episode, florid symptoms recede during the remission phase (Andreasen 2005). In this stage, most individuals still require maintenance treatment, in order to prevent symptoms recrudescence (relapse).

Description of the intervention

Antipsychotic medication is the current first‐line treatment for schizophrenia. Due to the chronic nature of the disease, long‐term treatment with antipsychotics is usually needed to prevent the risk of relapse (Ceraso 2020, Schneider‐Thoma 2022). Unfortunately, these medications have many adverse events that make their use complicated, including movement disorders, weight gain, metabolic problems and sexual dysfunction (Leucht 2013, Schneider‐Thoma 2019). Also, for this reason, people with schizophrenia are often ambivalent about taking medications, and rates of medication non‐compliance are high (Lacro 2002, Moncrieff 2009). Moreover, recent guidelines tend to shift their recommendations from not recommending to partially recommending antipsychotic discontinuation, both for schizophrenia in general and for first‐episode schizophrenia (Shimomura 2020).

Some authors argued that the efficacy of antipsychotics may have been overestimated, and their adverse effects underestimated, suggesting that clinicians reconsider “whether everyone who meets the criteria for a schizophrenia spectrum diagnosis requires antipsychotics in order to recover" (Morrison 2012).

Cognitive behavioural therapy (CBT) is a psychological intervention which was developed by Aaron Beck in 1979 to be used in the treatment of depression (Beck 1979). Aims of the therapy are to establish links between the person's thoughts, feelings or actions with respect to the current or past symptoms and/or functioning; persons are encouraged to re‐evaluate their perceptions, beliefs or reasoning in relation to the target symptoms. Alternative ways of coping with the target symptom can be promoted, with the aim of reducing stress and improving functioning (NICE 2014).

CBT began to be used for schizophrenia in the late 1980s and early 1990s (Kingdon 1998). CBT for psychosis (CBTp) is a problem‐centred, structured type of therapy that is based on patient‐clinician collaboration. It was developed with the primary aim of reducing symptom severity, and there is evidence that it may be effective in this regard when used in addition to antipsychotic medication (Bighelli 2018; Jauhar 2014; Jones 2018a; Jones 2018b; Wykes 2008; Zimmermann 2005). There is evidence that CBT could also be beneficial for improving other outcomes in patients with schizophrenia, such as insight, well‐being and functioning (Jones 2018a, Laws 2018). Based on this literature, current guidelines recommend offering CBT in addition to pharmacological treatment with antipsychotics (NICE 2014).

However, in all the existing meta‐analyses, CBT was investigated as provided in combination with antipsychotics (Jauhar 2014; Jones 2018a; Jones 2018b; Wykes 2008; Zimmermann 2005). As a result, the role of CBT without a concomitant treatment with antipsychotics is unclear. In recent years, there have been attempts to deliver CBT alone to patients with schizophrenia (Morrison 2012, Morrison 2014). These attempts have raised criticism and ethical concerns (Mustafa 2018), but also opened the way to new research and clinical perspectives.

How the intervention might work

CBT encourages the person to establish links between their thoughts, feelings or behaviours with respect to their symptoms. The aim of creating these connections is changing the way in which the individuals interpret and evaluate their experiences and attribute meanings to them.

By helping patients recognise their basic feelings, thoughts, and behaviours about the disease, CBT can improve the ability of schizophrenic patients to cope with their psychotic symptoms and can be an important helpful tool (Morrison 2010). Being able to recognise inappropriate thoughts, feelings, and behaviours can reduce the stress burden of patients, improve their quality of life, and help recovery (Morrison 2010).

Individuals are stimulated to identify and challenge biased interpretations of their experiences, that may have a role in the continuation of symptoms.

Why it is important to do this review

A few attempts and clinical trials have been conducted on the administration of CBT without concomitant antipsychotic medication (Morrison 2012, Morrison 2014). However, this literature has never been systematically appraised, nor the results synthesised with a meta‐analysis.

As a result, no evidence in the form of a systematic review exists on the effects of CBT when administered alone.

Evidence on this issue would be highly relevant for clinical practice.

On the one side, antipsychotics have burdensome side effects so, if it was proven that CBT is effective also without pharmacological treatment, this may reduce the burden for patients and the costs related to the intervention. Nevertheless, the feasibility of such option should be carefully examined, because not offering an antipsychotic medication goes against current clinical guidelines, and may be considered a critical ethical issue (Mustafa 2018). On the other side, the combination of the two interventions together may increase the efficacy of the treatment, in comparison to their use as stand‐alone.

The present Cochrane review will provide a comprehensive examination of the existing evidence on the feasibility and effectiveness of CBT offered without concomitant pharmacological therapy, and help shed light on this challenging matter.

Objectives

To investigate the effects of CBT for schizophrenia when administered without a concomitant pharmacological treatment with antipsychotics.

Methods

Criteria for considering studies for this review

Types of studies

We will consider all relevant randomised controlled trials (RCTs). We will include RCTs meeting our inclusion criteria and reporting useable data either for the qualitative or quantitative synthesis. We will consider eligible for inclusion both open‐label and rater‐blind studies. We will exclude quasi‐randomised studies, such as those that allocate intervention by alternate days of the week. Where people are given additional treatments as well as CBT, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the CBT that is randomised.

Types of participants

People with schizophrenia, however defined, or related disorders such as schizophreniform disorder, schizoaffective disorder and delusional disorder, by any means of diagnosis. We will not include trials where the majority of patients have disorders such as bipolar affective disorder or substance‐induced psychosis.

In case a study includes participants with other diagnoses, the study will be included only if participants with a diagnosis of schizophrenia or related disorders constituted at least 50% of the participants. 

Trials where participants have organic psychoses will be excluded, and also studies that recruited participants with prodromal symptoms or at risk mental states.

We are interested in making sure that information is as relevant as possible to the current care of people with schizophrenia, so aim to highlight the current clinical state clearly (acute, early post‐acute, partial remission, remission), as well as the stage (first episode, early illness, chronic), and whether the studies primarily focussed on people with particular problems (for example, negative symptoms, treatment‐resistant illnesses). The effect of the intervention on chronic patients and on patients with a first episode of psychosis will be investigated in a subgroup analysis (see Subgroup analysis and investigation of heterogeneity).

In case a study recruits participants from early intervention services without providing additional details about inclusion criteria, we will evaluate on a case‐by‐case basis if the participants match the characteristics of the population of the present review described above and, if necessary, ask for additional details from the authors.

Types of interventions

1. CBT without concomitant medication for schizophrenia

Cognitive behavioural therapy (CBT) has been used as a broad label that can include a variety of interventions. It normally includes elements of cognitive restructuring or cognitive therapy (CT) and elements of behavioural therapy (BT) that are delivered together. However, CT and BT elements could also be approached separately in the therapeutic process. For the aim of this review, we will consider any intervention that includes CT or BT elements alone, as well as CBT interventions that include both components, as an eligible intervention under the term 'CBT'. In this review, CBT will be evaluated in patients with schizophrenia who are not taking concurrent medication.

The group that received structured CBT and did not receive antipsychotic treatment will be used as the intervention group.

2. Control

Any control condition applied in studies that aimed to investigate the effects of CBT without concomitant medication will be considered for inclusion.

We plan to classify the control condition as follows and be open to include more, if found in the included studies:

2.1 CBT in combination with antipsychotics

Patients are randomised to receive CBT in addition to standard care, that usually includes antipsychotics. No distinction will be made between antipsychotics (e.g. first or second generation), doses or administration forms (oral, injection) and all will be included.

2.2 Standard care or treatment‐as‐usual (TAU)

This normally includes antipsychotics; participants in this group may receive some form of psychosocial support, but not CBT.

2.3 Standard care without antipsychotics

Patients are randomised to received standard care, explicitly excluding the prescription of an antipsychotic medication. The possibility of receiving rescue medication, if needed, is not excluded.

Types of outcome measures

We aim to divide all outcomes into short term (up to six months since the onset of therapy), medium term (up to 12 months) and long term (over 12 months). This grouping reflects the recommendations of the National Institute for Health and Care Excellence (NICE), according to which CBT should be delivered for at least 16 sessions (NICE 2014).

For outcomes such as 'clinically important change', 'any change', and 'relapse', we will use the definition used by each of the trials.

For valid scales, please see (Data extraction and management).

Primary outcomes

1. Mental state

1.1 General

1.1.1 Average endpoint or change score on a general mental state scale (e.g. Positive and Negative Syndrome Scale (PANSS), Brief Psychiatric Rating Scale (BPRS))

Secondary outcomes

1. Mental state

1.1 General

1.1.1 Clinically important change in general mental state (study defined)

1.2 Specific

1.2.1 Clinically important change in positive symptoms (delusions, hallucinations, disordered thinking), as defined by individual studies

1.2.2 Average endpoint or change score on a published scale/subscale addressing positive symptoms (e.g. PANSS positive, PANSS positive factor, Scale for the Assessment of Positive Symptoms (SAPS))

1.2.3 Clinically important change in negative symptoms (avolition, poor self‐care, blunted affect), as defined by individual studies

1.2.4 Average endpoint or change score on a published scale/subscale addressing negative symptoms (e.g. PANSS negative, PANSS negative factor, Scale for the Assessment of Negative Symptoms (SANS))

1.2.5 Clinically important change in depressive symptoms, as defined by individual studies

1.2.6 Average endpoint or change score on a published scale/subscale addressing depressive symptoms (e.g. Montgomery‐Asberg Depression Rating Scale (MADRS), Beck Depression Inventory (BDI)).

1.2.7 Clinically important change in anxiety symptoms, as defined by individual studies

1.2.8 Average endpoint or change score on a published scale/subscale addressing anxiety (e.g. Hamilton Anxiety Rating scale (HAM‐A) or Beck Anxiety Inventory (BAI)). 

2. Global state

2.1 Relapse

In case more measures of relapse are reported, we will give priority to: (i) relapse defined with operationalised criteria (e.g. worsening on a symptom scale); (ii) clinical judgement.

2.2 Recovery

Recovery is intended as "the ability to function in the community, socially and vocationally, as well as being relatively free of disease‐related psychopathology" (Andreasen 2005). We will extract the number of participants in recovery, based on this definition or on similar definitions provided in the studies. 

2.3 Remission 

Symptomatic remission according to Andreasen criteria (Andreasen 2005)

2.4 Clinically important change in global state (e.g. global impression of much improved, or more than 50% improvement on a rating scale such as Clinical Global Impression (CGI))

2.5 Average endpoint or change score on a global state scale

3. Service use

3.1 Admission to hospital

3.2 Number of days in hospital

4. Leaving the study early

4.1 For any reason

4.2 Due to inefficacy

4.3 Due to adverse effect

5. Functioning

5.1 Clinically important change in functioning

Number of participants with a clinically important change in functioning, as defined in each study

5.2 Average endpoint or change score on functioning scale

We will accept any published rating scales such as the Global Assessment of Functioning (GAF) or the Psychosocial Performance Scale (PSP).

6. Cognitive functioning

6.1 Clinically important change in cognitive functioning

6.2 Average endpoint or change score on cognitive functioning scale

We will accept any published cognitive functioning scale (e.g. the MATRICS consensus cognitive battery or the Neuropsychological Assessment Battery).

7. Quality of life

7.1 Clinically important change in quality of life

7.2 Average endpoint or change score on quality of life scale

We will accept any published quality of life scale (e.g. Heinrich‐Carpenter Quality of Life Scale).

8. Satisfaction with care

8.1 Recipient

8.1.1 Recipient satisfied with care

8.1.2 Average endpoint or change score on satisfaction with care scale

We will accept any published rating scale measuring satisfaction with care.

8.2 Carers

8.2.1 Carers satisfied with care

8.2.2 Average endpoint or change score on satisfaction with care scale

9. Behaviour

9.1 Occurrence of violent incidents (to self, others or property)

9.2 Self‐injury

9.3 Suicide attempt

10. Adverse events/effects

10.1 At least one adverse event/effect

10.2 Specific adverse events

We will use the classification proposed by Linden and colleagues (Linden 2014) to record adverse events potentially connected with CBT.

10.3 Incidence of various specific adverse effects

11. Mortality

11.1 Overall mortality

11.2 Mortality due to natural causes

11.3 Mortality due to suicide

12. Economic outcomes

12.1 Costs due to treatment

12.2 Total direct and indirect costs

12.3 Average change in total cost of medical and mental health care

Search methods for identification of studies

Electronic searches

The Information Specialist will search the register of the Cochrane Schizophrenia Group using the following search strategy:

*Cognit* in Intervention Field of STUDY

In such a study‐based register, searching the major concept retrieves all the synonyms and relevant studies. This is because the studies have already been organised, based on their interventions, and linked to the relevant topics (Shokraneh 2017). This allows rapid and accurate searches that reduce waste in the next steps of systematic reviewing (Shokraneh 2019).

Following the methods from Cochrane (Lefebvre 2021), the Information Specialist will compile this register from systematic searches of major resources and their monthly updates (unless otherwise specified).

• Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library

• MEDLINE

• Embase

• Allied and Complementary Medicine (AMED)

• BIOSIS

• Cumulative Index to Nursing and Allied Health Literature (CINAHL)

• PsycINFO

• PubMed

• US National Institute of Health Ongoing Trials Register (ClinicalTrials.gov)

• World Health Organization International Clinical Trials Registry Platform (www.who.int/ictrp)

• ProQuest Dissertations and Theses A&I and its quarterly update

The register of the Schizophrenia Group also includes handsearches and conference proceedings (see Group's website). It does not place any limitations on language, date, document type or publication status.

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. We will note the outcome of this contact in the 'Included studies' or 'Studies awaiting classification' tables.

Data collection and analysis

Selection of studies

At least two review authors (OC and IB) will independently inspect citations from the searches and identify relevant abstracts. Where disputes arise, we will acquire the full report for more detailed scrutiny. At least two review authors (OC and IB) will then obtain and independently inspect full reports of the abstracts or reports meeting the review criteria. Where it is not possible to resolve disagreement by discussion, we will discuss with the senior author of the team to resolve it. If, following discussion with the third author disagreement exists, we will attempt to contact the authors of the study concerned for clarification. All decisions will be documented.

Data extraction and management

1. Extraction

At least two review authors (OC and IB) will independently extract data from all included studies. We will attempt to extract data presented only in graphs and figures whenever possible, but will include only if two reviewers independently obtain the same result. We will discuss any disagreement. Where it is not possible to resolve disagreements by discussion, we will discuss with the senior author. All decisions will be documented. If necessary, we will attempt to contact authors through an open‐ended request in order to obtain missing information or for clarification. SL will help clarify issues regarding any remaining problems and we will document these final decisions.

2. Management

2.1 Forms

Data will be extracted using simple, pre‐designed forms, developed specifically for this review.

2.2 Scale‐derived data

We will include continuous data from rating scales only if:

• the psychometric properties of the measuring instrument have been described in a peer‐reviewed journal (Marshall 2000);

• the measuring instrument has not been written or modified by one of the trialists for that particular trial; and

• the instrument should be a global assessment of an area of functioning and not subscores which are not, in themselves, validated or shown to be reliable. However, we will include subscores of scales if these were validated or if these were predefined in a scale such as the positive symptom, negative symptom and general symptom scores of the Positive and Negative Syndrome Scale (PANSS, Kay 1986).

Ideally, the measurement instrument should either be a self‐report, or be completed by an independent rater or relative (not the therapist). We realise that this is not often reported clearly. 

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; however, calculation of change needs two assessments (baseline and endpoint) that can be difficult to obtain 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. If necessary, we will combine endpoint and change data in the analysis. This procedure is possible when using mean differences (MDs) (Deeks 2011) and also when using standardised mean differences (SMDs). Although, theoretically, the combination of change and endpoint data when SMDs are used can be problematic, meta‐epidemiological research has shown that on average no major over‐ or underestimations can be expected (Da Costa 2013). Endpoint and change data will be analysed separately in a Sensitivity analysis for the primary outcome mental state.

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 will apply the following checks to relevant continuous data before inclusion.

For endpoint data from studies including fewer than 200 participants, we will calculate the observed mean minus the lowest possible value of the scale and divide this by the standard deviation (Higgins 2020).

For example, in a scale that has possible lowest values higher than 0 (such as the Positive and Negative Syndrome Scale (PANSS), which can have values from 30 to 210 (Kay 1986)), we will subtract the minimum score (in this case 30) from the observed mean, and then divide by the standard deviation. In a scale that has 0 as minimum possible score, we will divide the observed mean by the standard deviation.

For this calculation, we will check the original publication of the scales referenced in the studies, in order to understand if they can have a lowest possible score different from 0, and the adjustment described above is needed or not.

If the ratio obtained is lower than one, it strongly suggests that the data are skewed. If it is higher than one but less than two, there is a suggestion that the data are skewed; if the ratio is larger than two we will include these data, because it is less likely that they are skewed (Altman 1996).

Where there is suggestion of skewedness (ratio < 2), we will exclude the relevant studies in a sensitivity analysis to check if they have an impact on the results (see Sensitivity analysis for further details).

These skewed results will nevertheless be reported in 'other data tables'.

We will enter all relevant data from studies of more than 200 participants in the analysis irrespective of the above rules, because skewed data pose less of a problem in large studies. We will also enter all relevant change data as, 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 or not data are skewed.

2.5 Common measurement

To facilitate comparison between trials, we aim, where relevant, 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 will make efforts 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) which corresponds to 'much improved' according to the clinical global impressions (CGI, Guy 1976) of raters, this could be considered a clinically significant response (Leucht 2005a; Leucht 2005b), in particular, for acutely ill participants. If data based on these thresholds are not available, we will use the primary cut‐off presented by the original authors, because the exact cut‐off is not so important in a meta‐analysis using risk ratios or odds ratios as effect sizes (Furukawa 2010).

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 CBT. Where keeping to this makes it impossible to avoid outcome titles with clumsy double‐negatives (e.g. 'not un‐improved'), we will report data where the left of the line indicates an unfavourable outcome and note this in the relevant graphs.

Assessment of risk of bias in included studies

Review authors OC and IB will work independently to assess risk of bias by using the RoB 2 tool and referring to the criteria described in the Cochrane Handbook for Systematic Reviews of Interventions, version 6.1 to assess trial quality (Sterne 2019, Higgins 2020, Chapter 8).

This set of criteria is based on the judgement of the following domains:

●      bias arising from the randomisation process;

●      bias due to deviations from intended interventions;

●      bias due to missing outcome data;

●      bias in measurement of the outcome; and

●      bias in selection of the reported result.

For each domain, we will rate the available 'signalling questions' in order to reach a judgement (high, some concerns, low) following the tool algorithms implemented in the RoB 2 Excel tool (available on the riskofbiasinfo website).

RoB 2 generally allows assessors to address studies from two angles: 1. the effect of assignment to the interventions at baseline, regardless of whether the interventions were received as intended ‐ the 'intention‐to‐treat effect'. 2. the adherence to the interventions ‐ the 'per‐protocol effect' (Chapter 8.2.2, Higgins 2020). For the purpose of this review, we will aim to assess the 'intention‐to‐treat effect'.

An evaluation with the RoB 2 tool will be performed for the following outcomes:

1. Mental state: Average endpoint or change score on a general mental state scale (e.g. PANSS, BPRS) (primary outcome) ‐ medium term

2. Global state: relapse ‐ long term

3. Leaving the study early: Leaving the study early for any reason ‐ medium term

4. Functioning: Average endpoint or change score on functioning scale ‐ medium term

5. At least one adverse event ‐ long term

For cluster‐randomised trials, we will use the specific version of the RoB 2 tool, provided at https://sites.google.com/site/riskofbiastool/welcome/rob-2-0-tool.

For cross‐over trials, since we intend to only use data from the first phase (see Measures of treatment effect), we will use the standard version of the RoB 2.

If the raters disagree, we will make the final rating by consensus. Where inadequate details of randomisation and other characteristics of trials are provided, we will attempt to contact authors of the studies in order to obtain further information. We will report non‐concurrence in quality assessment, but if disputes arise regarding the category to which a trial is to be allocated, we will resolve this by discussion.

We will note the level of risk of bias in both the text of the review, the relevant forest plots, and the Summary of findings table/s.

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), as it has been shown that RR is more intuitive than odds ratios (Boissel 1999) and that odds ratios tend to be interpreted as RR by clinicians (Deeks 2000). Although the number needed to treat for an additional beneficial outcome (NNTB) and the number needed to treat for an additional harmful outcome (NNTH), with their CIs, are intuitively attractive to clinicians, they are problematic to calculate and interpret in meta‐analyses (Hutton 2009). For binary data presented in the Summary of findings table/s, we will, where possible, calculate illustrative comparative risks.

2. Continuous data

For continuous outcomes, we will estimate MD between groups, in particular, when natural measures (such as days, kilograms, etc.) are used. We prefer not to calculate standardised 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 SMD. It should be noted that SMD can be transformed to MD by using the formula MD = SMD x standard deviation of the scale of interest (Higgins 2020).

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. Authors often fail to account for intra‐class correlation in clustered studies, leading to a unit‐of‐analysis error whereby P values are spuriously low, CIs unduly narrow and statistical significance overestimated (Divine 1992). This causes type I errors (Bland 1997; 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.

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. We will seek to contact first authors of studies to obtain intra‐class correlation coefficients for their clustered data and to adjust for this by using accepted methods (Gulliford 1999).

We have sought statistical advice and have been advised that the binary data from cluster trials 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 intra‐class correlation coefficient (ICC): thus design effect = 1 + (m − 1) * ICC (Donner 2002). If the ICC is not reported, we will assume it to be 0.1 (Ukoumunne 1999).

If cluster studies have been appropriately analysed and have taken intra‐class correlation coefficients and relevant data documented in the report into account, 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. This 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, participants can differ significantly from their initial state at entry to the second phase, 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 carry‐over and unstable conditions are very likely in severe mental illness, we will only use data from the first phase of cross‐over studies.

3. Studies with multiple treatment groups

Where a study involves more than two treatment arms, if relevant, we will present the additional treatment arms in comparisons. If data are binary, we will simply add these arms and combine within the two‐by‐two table. If data are continuous, we will combine data following the formula in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2020). Where additional treatment arms are not relevant, we will not use data from these arms.

Dealing with missing data

1. Overall loss of credibility

Although at some degree of loss of follow‐up data lose credibility (Xia 2009), we will not exclude studies based on this.

However, if more than 50% of data are unaccounted for (lost to follow‐up), we will exclude these studies in a Sensitivity analysis. If 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 (and not exclude the study in the sensitivity analysis). Finally, we will also downgrade quality within the Summary of findings table/s should the loss be 25% to 50% in total.

2. Binary

We will present data using an intention‐to‐treat analysis (ITT). In case studies present data only on completers, we will still use these studies. We will undertake a Sensitivity analysis excluding studies using completer analyses.

3. Continuous

3.1 Standard deviations

If standard deviations (SDs) are not reported, we will try to obtain the missing values from the authors. If these are not available, where there are missing measures of variance for continuous data, but an exact standard error (SE) and CIs are available for group means, and either P value or t value available for differences in the mean, we can calculate SDs according to the rules described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2020). When only the SE is reported, SDs are calculated by the formula SD = SE * √(n). The Cochrane Handbook for Systematic Reviews of Interventions presents detailed formulae for estimating SDs from P, t or F values, CIs, ranges or other statistics (Higgins 2020). 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. Nevertheless, we will examine the validity of the imputations in a sensitivity analysis that excludes imputed values.

3.2 Assumptions about participants who left the trials early or were lost to follow‐up

Various methods are available to account for participants who left the trials early or were lost to follow‐up. Some trials just present the results of study completers; others use the method of last‐observation‐carried‐forward (LOCF); while more recently, methods such as multiple imputation or mixed‐effects models for repeated measurements (MMRM) have become more of a standard. While the latter methods seem to be somewhat better than LOCF (Leon 2006), we feel that the high percentage of participants leaving the studies early and differences between groups in their reasons for doing so is often the core problem in randomised schizophrenia trials. We will, therefore, not exclude studies based on the statistical approach used. However, by preference, we will use the more sophisticated approaches, i.e. we will prefer to use MMRM or multiple‐imputation to LOCF, and we will only present completer analyses if some kind of ITT data are not available at all. Moreover, we will address this issue in the item 'Missing outcome data' of the RoB 2.

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 participants who are clearly outliers or situations that we had not predicted would arise and, where found, discuss with other authors such situations or participant groups.

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 and discuss with other authors any such methodological outliers.

3. Statistical heterogeneity

3.1 Visual inspection

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

3.2 Using the I² statistic

We will investigate heterogeneity between studies by considering the I² statistic alongside the Chi² P value. The I² statistic provides an estimate of the percentage of inconsistency thought to be due to chance (Higgins 2003). The importance of the observed value of I² depends on the magnitude and direction of effects as well as the strength of evidence for heterogeneity (e.g. P value from Chi² test, or a confidence interval for I²). We will interpret the I² estimate as follows (Chapter 10, Higgins 2020):

• 0% to 40%: might not be important;

• 30% to 60%: may represent moderate heterogeneity;

• 50% to 90%: may represent substantial heterogeneity;

• 75% to 100%: considerable heterogeneity.

When substantial levels of heterogeneity are found in the primary outcome, we will explore reasons for heterogeneity (Subgroup analysis and investigation of heterogeneity).

Assessment of reporting biases

Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997). These are described in Chapter 13 of the Cochrane Handbook for Systematic reviews of Interventions (Higgins 2020).

1. Protocol versus full study

We will try to locate protocols of included randomised trials. If the protocol is available, we will compare outcomes in the protocol and in the published report. If the protocol is not available, we will compare outcomes listed in the methods section of the trial report with actually reported results. If details from Clinicaltrials.gov and WHO registry (ICTRP) are available, they will be included in the search results and these can be used to compare the differences between planned methods and published results.

2. Funnel plot

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 fewer than ten studies, or where all studies are of similar size. In other cases, where funnel plots are possible, we will seek statistical advice in their interpretation. We will additionally apply the Egger's test for funnel plot asymmetry, in order to support the visual inspection of the forest plot with a statistical test. Egger's test will be performed with R.

Data synthesis

We understand that there is no closed argument regarding 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 a random‐effects model for analyses. In a sensitivity analysis of the primary outcome, we will apply the fixed‐effect model.

Subgroup analysis and investigation of heterogeneity

1. Subgroup analyses

The following subgroup analysis will be conducted for the primary outcome, if at least 10 studies are included in the analysis (Higgins 2020).

1.1 Stage of the illness

We will investigate separately studies that enrolled chronic participants and studies that enrolled participants at their first episode of psychosis.

1.2 Special populations

We will investigate the effect of the intervention in different subpopulations, if data are provided separately (e.g. participants with schizophrenia versus participants with other psychotic disorders such as schizophreniform disorder, schizoaffective disorder and delusional disorder).

1.3 Individual vs group 

We will investigate separately studies that provided CBT in an individual vs in a group setting.

1.4 Clinical staff training

We will investigate separately studies in which CBT was delivered by different professionals (e.g. therapists expert in CBT, therapists in training, nurses).

2. Investigation of heterogeneity

We will report if inconsistency is substantial. Firstly, we will investigate whether data have been entered correctly. If this is the case, the following strategies will be considered: a) pool the data despite the heterogeneity. An example where this strategy may be appropriate is when the effects of all studies are in the same direction. In other words, the heterogeneity reflects the degree of an effect rather than its direction which is less problematic. Another example is when heterogeneity can be explained by appropriate subgroup analyses. b) exclude outlying studies. This strategy may apply, if reinspection of such studies reveal methodological or clinical differences that were previously overlooked. c) not pool the studies. All decisions in this regard will be described and discussed.

Sensitivity analysis

Where possible, we will perform sensitivity analyses for the primary outcome in order to explore the influence of the following factors on effect size. If there are substantial differences in the direction or precision of effect estimates in any of the sensitivity analyses listed below, we will discuss them in the discussion section.

1. Blinding of outcome assessor

We will exclude trials that did not apply a blind outcome assessor.

2. Assumptions for missing data

We will exclude studies using completer analyses only (see Dealing with missing data).

3. Loss to follow‐up

We will exclude studies where the overall loss of data was greater than 50%.

4. Risk of bias

We will analyse the effects of excluding trials that are at overall high risk of bias (see Assessment of risk of bias in included studies) for the meta‐analysis of the primary outcome.

5. Imputed values

We will also undertake a sensitivity analysis excluding trials where we use imputed values for ICC in calculating the design effect in cluster‐randomised trials or where SDs were imputed.

6. Fixed‐effect

We will synthesise data using the 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.

7. Separating endpoint and change data

We will analyse studies providing data in the form of endpoint scores and change scores separately for the continuous primary outcome, mental state.

8. Skewed data

We will perform a sensitivity analysis excluding studies for which there is suggestion of skewedness (mean/SD ratio lower than 2 ‐ see Data extraction and management). If this changes the results in comparison with the main analysis (from significantly favouring the intervention to significantly favouring the control, or vice‐versa), we will exclude these studies also from the main analysis, and present their data in 'Other data' tables.

Summary of findings and assessment of the certainty of the evidence

Summary of findings table(s)

We will use the GRADE approach to interpret findings (Schünemann 2017); and will use GRADEpro GDT (GRADEpro GDT) to export data from our review to create a Summary of findings table(s) (RevMan Web 2020). These tables provide outcome‐specific information concerning the overall certainty 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. The overall RoB 2 judgements will be used to feed into the GRADE assessment. We aim to select the following main outcomes for inclusion in the Summary of findings table:

1. Mental state: Average endpoint or change score on a general mental state scale (e.g. PANSS, BPRS) (primary outcome) ‐ medium term

2. Global state: relapse ‐ long term

3. Leaving the study early: Leaving the study early for any reason ‐ medium term

4. Functioning: Average endpoint or change score on functioning scale ‐ medium term

5. At least one adverse event ‐ long term

If data are not available for these prespecified outcomes but are available for ones that are similar, we will present the closest outcome to the prespecified one in the table but take this into account when grading the finding.

Contributions of authors

OC: Protocol development

IB: Protocol development

SL: Protocol development

Sources of support

Internal sources

• Freistaat Bayern, Germany

  The employer of Irene Bighelli and Stefan Leucht

• National Institute for Health and Care Research (NIHR), UK

  Provided funding for Cochrane Schizophrenia Group

External sources

• None, Other

  None

Declarations of interest

OC: None

IB: IB is the Deputy Co‐ordinating editor of Schizophrenia Group. She was not involved in the editorial process of the present review (see Acknowledgements for details about editorial process).

SL: In the past 3 years, SL has received honoraria for service as a consultant or adviser and/or for lectures from Angelini, Böhringer Ingelheim, Geodon&Richter, Janssen, Johnson&Johnson, Lundbeck, LTS Lohmann, MSD, Otsuka, Recordati, SanofiAventis, Sandoz, Sunovion, TEVA, ROVI and EISAI. He has no declaration of interest related to CBT. SL is an editor of Schizophrenia Group. He was not involved in the editorial process of the present review (see Acknowledgements for details about editorial process).

These authors contributed equally to this work.

These authors contributed equally to this work.

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