Cannabidiol for people with schizophrenia

Objectives

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

To assess the effectiveness and safety of CBD in the treatment of people with schizophrenia.

Background

Description of the condition

Schizophrenia is a severe mental disorder characterised by psychotic symptoms and a range of behavioural, cognitive, and social deficits (Millan 2016). The typical age of onset is late adolescence or early adulthood, with a second peak of incidence in midlife, especially in women (Lopez‐Castroman 2019). The female to male ratio amongst people with schizophrenia is 1:1.4, and males tend to have an earlier age of illness onset, worse premorbid functioning, more negative symptoms, fewer affective symptoms, and a higher rate of comorbid alcohol or substance use (Giordano 2021). Schizophrenia is considered to evolve in four stages: a period of asymptomatic risk, the prodromal phase with cognitive and behavioural changes, the progressive phase with characteristic symptoms of psychosis, and the residual phase with fewer and less severe symptoms (Kahn 2015). Schizophrenia affects more than 20 million people worldwide, approximately one percent of the global population (Spencer 2018). It makes a significant contribution to the global burden of disease, and is amongst the most prominent causes of disability around the world (Spencer 2018). Due to the complexity of the condition, the impact on healthcare systems' budgets is considerable, not only due to the direct costs associated with medical treatment, but also due to the nonmedical costs such as caregiving and loss of productivity (Tajima‐Pozo 2015). In countries like the USA, direct healthcare costs attributed to schizophrenia are 24% higher than for individuals without schizophrenia, and indirect costs are 76% higher (Cloutier 2016). Schizophrenia presents with characteristic symptoms that can be grouped into positive, negative, and cognitive categories (Kahn 2015). The Diagnostic and Statistical Manual of Mental Disorders, Fifth Edition (DSM‐5) and the International Classification of Diseases and Related Health Problems (ICD) organise these characteristic symptoms into criteria that define symptom duration, the impact on everyday functioning, and certain exclusion criteria (Kahn 2015). According to DSM‐5, a schizophrenia diagnosis is based on the presence of specific positive psychotic symptoms (delusions, hallucinations, disorganised speech and behaviour) and negative symptoms (e.g. affective flattening, emotional and social isolation) for at least one month, a substantial decrease in social and occupational functioning, an overall symptom duration of six months or longer, and the exclusion of other conditions that might contribute to or explain the symptoms (APA 2013).

Antipsychotic agents are the first line of treatment for people with schizophrenia, usually combined with non‐pharmacological treatments such as psychotherapy. The main objective of treatment is to improve psychiatric symptoms, functioning in social life, and quality of life, with minimal adverse effects (Patel 2014). However, between 30% and 60% of individuals do not respond to pharmacological therapy (Gillespie 2017). Consequently, new therapeutic options have been developed to improve psychotic symptoms, negative symptoms, cognitive impairment, and social outcomes in people with schizophrenia. (Kennedy 2014)

Description of the intervention

Cannabis is a botanical product with origins tracing back to the ancient world (Bridgeman 2017). It is mainly derived from two types of plants: Cannabis indica and Cannabis sativa. Humans have used the products derived from Cannabis sativa for more than two millennia for medicinal purposes (Cohen 2019). Products containing cannabis are also used recreationally; research has shown that 4% of the global adult population have used cannabis at some time in their lives (Hall 2015; Cohen 2019). The cannabis plant contains a total of 483 compounds, more than 120 of which are bioactive components, collectively known as phytocannabinoids (Brenneisen 2007). The component of cannabis with the greatest psychoactive potency is delta‐9‐tetrahydrocannabinol (THC; Cooper 2009). Although studies have associated cannabis use with the development of psychopathology, cannabidiol (CBD), a natural component found in cannabis plants that can be synthetically manufactured, does not have the negative effects that are commonly seen with cannabinoids like THC (WHO 2017). CBD is generally administered orally as a capsule or in an oil solution. There is evidence for its efficacy in the treatment of pain, dementia, Parkinson's disease, and schizophrenia (Cohen 2019). CBD is well tolerated and has relatively few serious adverse effects, although not all potential toxic effects have been studied (WHO 2017; Chesney 2020).

How the intervention might work

Cannabinoids target the brain’s endocannabinoid system, which is involved in many neuromodulation processes. The endocannabinoid system is negatively impacted in people with schizophrenia (An 2020). In healthy and non‐healthy populations, THC can have psychoactive effects, including psychotic symptoms, due to its partial affinity for the cannabinoid receptor CB₁ (Leweke 1999; D'Souza 2009; An 2020). CBD has shown a lower affinity than THC for the cannabinoid receptors CB₁ and CB₂ (Pisanti 2017). CBD appears to moderately inhibit the degradation of the endocannabinoid anandamide; in this way, it may exert an antipsychotic effect and improve cognitive processes in people with schizophrenia (Beltramo 2000; Leweke 2012; Patel 2014; Schoevers 2020). In addition, CBD can interact with multiple receptor systems and is a negative allosteric modulator of the CB₁ receptor; thus, it can produce  an antipsychotic effect and prevent adverse effects (Laprairie 2015). 

The first findings on the effect of CBD in people with schizophrenia were presented in a 1995 case report. It described the case of a 19‐year‐old woman diagnosed with schizophrenia who showed improvement on the Brief Psychiatric Rating Scale (BPRS), especially psychotic symptoms, after receiving CBD treatment (Zuardi 1995). One study in mice compared CBD with haloperidol and clozapine (drugs used in the treatment of schizophrenia) for preventing the hyperlocomotion induced by amphetamine or ketamine, and found that both CBD and clozapine were efficacious. (Moreira 2005). In one human study, ketamine was used to induce a psychotic state in healthy volunteers who had previously received placebo or CBD. The CBD group showed attenuated effects of ketamine on the Clinician‐Administered Dissociative States Scale, which supports the hypothesis that CBD could serve as an antipsychotic agent (Hallak 2011). Similarly, neuroimaging and behavioural studies have demonstrated the contrasting effects of THC and CBD (induction of versus protection against psychosis; Bhattacharyya 2010; Bhattacharyya 2012; Bhattacharyya 2015). Clinical trials on CBD have found that it may decrease positive symptoms and improve cognitive functioning in people with schizophrenia when used as an add‐on to antipsychotic therapy (Boggs 2018; McGuire 2018), or as monotherapy (Leweke 2012).

Why it is important to do this review

Schizophrenia is a severe mental health condition that often leads to disability; has direct implications on level of functioning, autonomy and well‐being; and decreases quality of life (Solanki 2008). Because of the complex nature of this disorder, finding safe and effective treatments is a challenge (Rogers 2009). Available treatments for schizophrenia are ineffective in many people and are associated with serious adverse effects (Patel 2014). The discovery of the endocannabinoid system in relation to the psychotic components of mental illness has motivated research into the use of CBD as an alternative or add‐on for treating schizophrenia (Leweke 2012; Cohen 2019).

Three previous systematic reviews have assessed the effects of CBD in people with schizophrenia. McLoughlin 2014 identified only one eligible study, but reports of other relevant studies have been published since. Ahmed 2021 aimed to summarise the results of controlled trials using defined doses of THC and CBD in schizophrenia; it included evidence from clinical trials and one case series. Finally, McKee 2021 aimed to aggregate the high‐level evidence on the effectiveness of cannabinoid products for treating psychiatric disorders (including schizophrenia) in adults. In Ahmed 2021 and McKee 2021, the available evidence was limited and heterogeneity was substantial.

This review aims to identify the available evidence on the effectiveness and safety of CBD for treating people with schizophrenia.

Objectives

To assess the effectiveness and safety of CBD in the treatment of people with schizophrenia.

Methods

Criteria for considering studies for this review

Types of studies

We will consider open‐label, single‐blind, and double‐blind randomised control trials (RCTs). We will consider trials that are described as 'double‐blind' in which randomisation is implied, deciding on whether to include or exclude them after performing the sensitivity analysis. If the sensitivity analysis reveals substantive differences, we will only include clearly randomised trials and describe the findings in the sensitivity analysis section (see Sensitivity analysis). We will exclude quasi‐randomised studies (e.g. studies allocating the intervention by alternation).

Types of participants

Adults aged 18 to 65 years with schizophrenia and schizophrenia‐like psychoses (schizophreniform and schizoaffective disorder) defined by any diagnostic criteria. We will include people with first‐episode and multiple‐episode schizophrenia, as well as people with acute exacerbation and people in the stable phase. We will exclude people with comorbid substance use.

Types of interventions

Intervention

• CBD at any dose, administered by any route. CBD is generally administered orally, either as a capsule or dissolved in an oil solution. It can also be administered through sublingual or intranasal routes (Fasinu 2016). We will include both CBD as monotherapy and CBD as add‐on therapy to other pharmacological treatments.

Control

• Active comparator (e.g. antipsychotic treatment)

• Placebo

Types of outcome measures

We will group outcomes into short‐term (up to 12 weeks), medium‐term (13 to 26 weeks), and long‐term outcomes (more than 26 weeks).

Primary outcomes

• Global state (short term): clinically important response in the global state as defined by individual studies (e.g. global impression of much improved, or more than 50% improvement on a rating scale)

• Mental state (short term): clinically important response in specific symptoms (e.g. positive, negative, affective, cognitive symptoms) as defined by the individual studies

• Adverse effects (short‐, medium‐, and long‐term): clinically important adverse effects

Secondary outcomes

• Global state

  • Relapse as defined by the individual studies

  • Average endpoint or change score on a global state scale

  • Use of other medications

• Mental state

  • Clinically important response in general mental state as defined by the individual studies

  • Average endpoint or change score on a general mental state scale

  • Average endpoint or change score on a specific symptom scale (e.g. positive, negative, affective, cognitive symptoms)

•  Service use

  • Number of participants hospitalised

  • Number of days in hospital

• Behaviour

  • Clinically important change in general behaviour

  • Average endpoint or change score on a general behaviour scale

  • Clinically important change in specific aspects of behaviour (e.g. aggression, violence)

  • Average endpoint or change on specific aspects of a behaviour scale

• Adverse effects/events

  • Number of participants with at least one adverse effect

  • Average endpoint of change score on an adverse effect scale

  • Specific adverse effects

    • Anticholinergic

    • Cardiovascular

    • Central nervous system

    • Gastrointestinal

    • Endocrine (e.g. amenorrhoea, galactorrhoea, hyperlipidaemia, hyperglycaemia, hyperinsulinaemia)

    • Haematology (e.g. haemogram, leukopenia, agranulocytosis/neutropenia)

    • Hepatitic (e.g. abnormal transaminase, abnormal liver function, abnormal liver function tests)

    • Metabolic

    • Movement disorders

    • Other

  • Average endpoint or change score on a specific adverse effect scale

• Leaving the study early

  • For any reason

  • Due to inefficacy

  • Due to adverse events

• Quality of life (for recipient, informal carers, or professional carers)

  • Clinically important change in quality of life as defined by the individual studies

  • Average endpoint or change score on a quality‐of‐life scale

• General functioning

  • Clinically important changes in general functioning as defined by the individual studies

  • Average endpoint or change score on a general functioning scale

  • Clinically important change in specific aspects of functioning as defined by the studies

  • Average endpoint or change score on specific aspects of a functioning scale

• Social functioning

  • Clinically important change in social functioning

  • Average endpoint or change score on a social functioning scale

Search methods for identification of studies

Electronic searches

The Information Specialist will search the Cochrane Schizophrenia Trials Register using the following search strategy:

*cannabidiol* OR *CBD* in Intervention Field of STUDY 

In such a study‐based register, searching the major concept retrieves all the synonyms and relevant studies, as 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 Cochrane methods, the Information Specialist compiles this register from systematic searches of the following major resources and their monthly updates, unless otherwise specified (Lefebvre 2022):

• 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); and

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

As explained on the Schizophrenia Group website (schizophrenia.cochrane.org/register-trials), the register also includes handsearches and conference proceedings. It does not place any limitations on language, date, document type, or publication status.

Searching other resources

Other electronic resources

We will search for grey literature in the System for Information on Grey Literature in Europe (www.opengrey.eu)

We will also search the proceedings and repositories of worldwide congresses and conferences of psychiatry since 2014 by consulting the following websites:

• World Psychiatric Association (www.wpanet.org);

• European Psychiatric Association (www.europsy.net);

• Royal College of Psychiatrists (www.rcpsych.ac.uk);

• American Psychiatric Association (www.psychiatry.org);

• Canadian Psychiatric Association (www.cpa-apc.org);

• Psychiatric Association of Latin America (Asociación Psiquiatrica de America Latina; www.webapal.org);

• Argentine Association of Psychiatrists (Asociación Argentina de Psiquiatras; www.aap.org.ar);

• World Congress of Mental Health Psychiatry and Wellbeing (annualmentalhealth.psychiatryconferences.com); and

• International Association of Cannabinoid Medicines (cannabis-med.org).

Reference searching

We will check the reference lists of all included studies for further relevant trials.

Personal contact

We will contact the first author of each included study for information regarding unpublished trials.

Data collection and analysis

Selection of studies

Two review authors (SG, PS) will independently screen the titles and abstracts of the recovered records to eliminate those that are clearly ineligible; one review author (SB or DB) will independently reinspect a random 20% sample of the recovered records to ensure reliability of selection. We will resolve any disagreements by consulting a third review author (GSV or LB). If we still cannot reach consensus, we will contact the trial authors for clarification. Where studies have multiple publications, we will collate all the publications for each study under a single identifier.

Data extraction and management

Extraction

Two review authors (SG, PS) will extract data from all included studies in duplicate. To ensure reliability, another review author (SB or DB) will independently extract data from a random 10% sample of these studies. We will attempt to extract data from graphs and figures whenever possible. For multicentre studies, where possible we will extract data relevant to each site. We resolve any disagreements by discussion or by consulting a third review author (LB), and document our decisions. If necessary, we will also contact the corresponding trial authors for further details.

Management

Data extraction forms

We will develop and pilot standardised data extraction forms, including the following variables:

• study location and setting;

• trial design;

• inclusion and exclusion criteria;

• baseline characteristics of trial participants;

• intervention;

• comparison;

• primary and secondary outcomes; and

• methodological characteristics.

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 provides a global assessment of an area of functioning and not unvalidated subscores. However, we will include subscores from mental state scales that measure positive and negative symptoms of schizophrenia.

Ideally, the participant, an independent rater, or a relative of the participant (rather than the therapist) should apply the measuring instrument. We will note whether this is the case in the 'Characteristics of studies' section.

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 requires two measurements (baseline and endpoint), which can be difficult to obtain in unstable and difficult‐to‐measure conditions such as schizophrenia. We have decided to use endpoint data primarily, and use change data only where endpoint data are unavailable. If necessary, we will combine endpoint and change data in the analysis, as we prefer to use mean differences (MDs) rather than standardised mean differences (SMDs) throughout (Deeks 2022).

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 standards to relevant continuous data before inclusion.

For endpoint data from studies including fewer than 200 participants:

• when a scale starts from the finite number zero, we will subtract the lowest possible value from the mean, and divide this by the standard deviation (SD). If this value is lower than one, it strongly suggests that the data are skewed, and we will exclude these data. If this ratio is higher than one but less than two, it suggests that the data are skewed. We will enter these data and test whether their inclusion changes the results substantially; if it does, we will enter the data as 'other data'. Finally, if the ratio is larger than two, we will include the data, as they are less likely to be skewed (Altman 1996); and

• if a scale starts from a positive value (e.g. Positive and Negative Syndrome Scale (PANSS), which ranges from 30 to 210 (Kay 1986)), we will modify the calculation described above to factor in the starting point. In these cases, skewed data are present if 2 × SD > (S − S_min), where S is the mean score and S_min is the minimum score.

Note: 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 it is difficult to determine whether continuous data are skewed when they are presented on a scale that includes a possibility of negative values.

Common measurement

To facilitate comparison between trials, we will convert variables that can be reported in different metrics, such as days in hospital (mean days per year, per month, or per week) to a common metric (e.g. mean days per month).

Conversion of continuous to binary

Where possible, we will convert continuous outcome measures to dichotomous data by identifying cut‐off points on rating scales and dividing participants accordingly into 'clinically improved' or 'not clinically improved'. It is generally assumed that a 50% reduction in a scale‐derived score, such as the BPRS (Overall 1962), or the PANSS (Kay 1986), represents a clinically significant response (Leucht 2005a; Leucht 2005b). If data based on these thresholds are unavailable, we will use the primary cut‐off presented by the study authors.

Direction of graphs

Whenever possible, we will enter the data in such a way that the area to the left of the line of no effect in the forest plots indicates a favourable outcome for CBD interventions. Where this results in outcome titles with clumsy double‐negatives (e.g. 'not un‐improved') we will switch the graph labels.

Assessment of risk of bias in included studies

Two review authors (DB, SG) will independently assess risk of bias in each trial using a simple form and applying the criteria described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022a). This set of criteria is based on evidence of associations between overestimate of effect and high risk of bias related to sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting. We will resolve any discrepancies through discussion or by involving a third review author (LB or GS). Where study authors have not provided details of randomisation or other relevant characteristics, we will contact the study authors to request further information. We will use the Cochrane risk of bias tool (RoB 2; Sterne 2019) and generate risk of bias tables.

Measures of treatment effect

Binary data

For binary or dichotomous data, we will use risk ratios (RRs) with their respective 95% confidence intervals (CIs). The RR is considered a more intuitive effect measure than the odds ratio (Boissel 1999). Moreover, clinicians often interpret odds ratios as RRs (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 difficult to calculate and interpret in meta‐analyses (Hutton 2009). For binary data presented in the summary of findings table(s), we will calculate illustrative comparative risks where possible.

Continuous data

For continuous outcomes, we will estimate MDs between groups, especially for data with natural units (e.g. days, kilograms). We prefer not to calculate SMDs, but will consider doing so for scales that are not identical but are very similar..

Unit of analysis issues

Cluster trials

Studies increasingly employ cluster randomisation (e.g. randomisation by clinician or practice), but analysis and pooling of clustered data poses some problems. Study authors often fail to account for intraclass 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 the data as we would data from an individually 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 an asterisk to indicate the presence of a probable unit‐of‐analysis error. We will attempt to contact study authors to obtain intraclass correlation coefficients (ICCs) for their clustered data and adjust for clustering using accepted methods (Gulliford 1999). We have sought statistical support and have been advised that the binary data from cluster trials presented in a report should be divided by a design effect, calculated using the mean number of participants per cluster (m) and the 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).

Where the authors of cluster studies have performed appropriate analyses and taken ICCs and relevant data into account, we will synthesise these studies with other studies using the generic inverse variance method.

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 period. 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.

Studies with multiple treatment groups

Where a study involves more than two relevant treatment arms, we will present the additional treatment arms in comparisons. If data are binary, we will simply combine them and enter the totals in a 2 × 2 table. If data are continuous, we will combine data following the formula presented in Chapter 6, section 6.5.2.10 (Combining groups) of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022b). We will not include data from additional treatment arms that are irrelevant to our review. We will list all treatment arms in the 'Characteristics of included studies' tables, including those we do not use in the review.

Dealing with missing data

Overall loss of credibility

At some degree of loss to follow‐up, data must lose credibility (Xia 2009). For any particular outcome, should more than 50% of data be unaccounted for, we will not reproduce these data or use them in the analyses. However, if more than 50% of the data in one arm of a study are lost, but the total loss is 50% or less, we will address this by downgrading the certainty of the evidence. We will also downgrade the certainty of the evidence if total loss is between 25% and 50%.

Binary data

Where attrition for a binary outcome is 50% or less, and where these data are not clearly described, we will analyse data on a 'once‐randomised‐always‐analysed' basis (intention‐to‐treat (ITT)). We will assume that participants leaving the study early had negative outcomes. We will undertake a sensitivity analysis testing how prone the primary outcomes are to change when we compare the data only from people who complete the study to the intention‐to‐treat analysis using the above assumptions.

Continuous data

Attrition

We will use data where attrition for a continuous outcome is 50% or less. We will use the data only from participants who complete the study.

Standard deviations

If studies do not report SDs, we will try to obtain the missing values from the study authors. If these data are unavailable, 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 the P value or t value is available for differences in mean, we can calculate SDs according to the formula provided in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022c). When only the SE is reported, SDs are calculated by multiplying the SE by the square root of the sample size. The Cochrane Handbook for Systematic Reviews of Interventions presents detailed formulae for estimating SDs from P, t or F values; CIs; ranges; and other statistics (Higgins 2022c). If these formulae do not apply, we will calculate the SDs according to a validated imputation method 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 an outcome from a given study and thus to lose information. Nevertheless, we will examine the validity of the imputations in a sensitivity analysis that excludes imputed values.

Assumptions about participants who leave trials early or are lost to follow‐up

Various methods are available to account for participants who leave trials early or are lost to follow‐up. Some trials only present the results of study completers; others use the method of last observation carried forward (LOCF). Since 2006, methods such as multiple imputation or mixed‐effects models for repeated measurements (MMRM) have become more of a standard. While these two newer methods seem to perform better than LOCF (Leon 2006), we consider that the core problem in randomised trials on schizophrenia relates to the high percentage of participants who leave early and the differences between groups in reasons for dropout. Therefore, we will not exclude studies based on the statistical approach used for accounting for dropouts. However, by preference, we will use the more sophisticated approaches (i.e. MMRM or multiple‐imputation over LOCF), and we will only present completer analyses if no ITT data are available. Moreover, we will address this issue in the 'Incomplete outcome data' domain of the risk of bias tool.

Assessment of heterogeneity

Clinical heterogeneity

We will judge clinical heterogeneity initially by inspecting all studies to identify and discuss any participants who are clearly outliers, or situations we had not predicted.

Methodological heterogeneity

We will judge methodological heterogeneity by inspecting all studies to identify and discuss any methodological outliers.

Statistical heterogeneity

Visual inspection

We will assess forest plots visually to investigate the possibility of statistical heterogeneity.

Employing 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 the I² statistic depends on the magnitude and direction of effects as well as the strength of evidence for heterogeneity (e.g. Chi² P value or I² statistic CI). We will interpret an I² estimate of 50% or more accompanied by a statistically significant Chi² value as evidence of substantial heterogeneity (Deeks 2022). Where we find substantial levels of heterogeneity in the primary outcomes, we will explore the potential sources (see Subgroup analysis and investigation of heterogeneity).

Assessment of reporting biases

Reporting biases occur 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 Systemic reviews of Interventions (Page 2022).

Protocol versus full study

We will try to identify protocols of included randomised trials. Where a protocol is available, we will compare outcomes in the protocol and in the published study. For studies without a protocol, we will compare outcomes listed in the methods section of the trial report with the reported outcomes in the results section.

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 reported in 10 or fewer studies, or where all studies are of similar size. In other cases, where funnel plots are possible, we will seek statistical advice on their interpretation.

Data synthesis

We understand that the fixed‐effect model and the random‐effects model each has advantages and limitations. In fixed‐effect meta‐analysis, the true effect of intervention (in both magnitude and direction) is assumed to be the same in every study (i.e. is fixed across studies). This assumption implies that the observed differences between study results are due entirely to chance (i.e. that there is no statistical heterogeneity). When there is heterogeneity that cannot readily be explained, one analytical approach is to incorporate it into a random‐effects model. The random‐effects method assumes that the different studies are estimating different (though related) intervention effects. It takes into account differences between studies, even if there is no statistically significant heterogeneity. However, the random‐effects method attributes added weight to small studies, which are often the most prone to bias. Depending on the direction of effect, these studies can either inflate or deflate the effect size. We will use a random‐effects model for the analyses.

Subgroup analysis and investigation of heterogeneity

Subgroup analyses

If data are available, we will conduct the following subgroup analyses:

• clinical stage: first‐episode acute versus multiple‐episode participants;

• dosage of CBD administered: low dose (less than 600 mg per day) versus high dose; and

• treatment regimen (CBD as monotherapy versus add‐on therapy).

Investigation of heterogeneity

If we find substantial statistical heterogeneity, first we will check whether data have been entered correctly. If they have, we will then inspect the forest plot visually and remove outlying studies successively until homogeneity is restored. For this review, we have decided that if we can restore homogeneity by removing data contributing to no more than 10% of the total weighting, we will pool the data. Otherwise, we will not pool these data and will present these issues in the discussion. Although there is no supporting evidence for this 10% cut‐off, we will use prediction intervals as an alternative to present these results. When there is unanticipated clinical or methodological heterogeneity, we will state hypotheses regarding the observations for future reviews or updates of this review.

Sensitivity analysis

Where possible, we will perform sensitivity analyses to explore the influence of the following factors on effect size.

Implication of randomisation

If we identify trials that imply randomisation for the primary outcomes, we will pool data from trials with implied and true randomisation.

Assumptions for lost binary data

Where we have to make assumptions regarding participants lost to follow‐up (see Dealing with missing data), we will compare the primary outcome findings when we assume all participants lost to follow‐up had a negative outcome (worst‐case scenario) to the findings for study completers only. If there is a substantial difference, we will report results and discuss them but continue to employ our assumption.

Where we have to make assumptions regarding missing SDs (see Dealing with missing data), we will undertake a sensitivity analysis testing how prone results are to change when complete data only are compared to the imputed data using the above assumption. If there is a substantial difference, we will report results and discuss them but continue to employ our assumption.

Risk of bias

We will evaluate the effects of excluding trials that are at high risk of bias across one or more domains (see Assessment of risk of bias in included studies) for the meta‐analysis of the primary outcomes.

Imputed values

We will undertake a sensitivity analysis to assess the effects of including data from cluster‐randomised trials where we use imputed values for ICC in calculating the design effect.

Fixed‐effect and random‐effects

We will synthesise data using a random‐effects model; however, we will also synthesise data for the primary outcomes using a fixed‐effect model to evaluate whether this alters the results.

We aim to carry out these sensitivity analyses for primary outcomes only. If there are substantial differences in the direction or precision of effect estimates in any of the sensitivity analyses listed above, we will not add data from studies at high risk of bias to the results of the studies at low risk of bias, but will present them separately. If including data from high‐risk studies does not result in a substantive difference, they will remain in the analyses.

Summary of findings and assessment of the certainty of the evidence

We will use the GRADE approach to assess the certainty of the evidence (Schünemann 2022); and will use GRADEpro GDT to export data from our review (RevMan Web 2022) and create one or more summary of findings tables. These tables provide outcome‐specific information concerning the overall certainty of evidence from each included study in the comparison, the magnitude of the effect of the interventions examined, and the sum of available data on all outcomes we rated as important to patient care and decision‐making. The summary of findings table will include the outcomes (at endpoint) of:

• global state

• mental state; and

• adverse effects.

Contributions of authors

Wrote protocol: DB, PS, SB, SG
Reviewed and drafted parts of the protocol: GS, LB 

Sources of support

Internal sources

• Fundacion Universitaria de Ciencias de la Salud‐FUCS, Colombia

  Provides funding for the Cochrane Associate Centre 

• Diana Buitrago‐Garcia receives grants from the Swiss Government Excellence Scholarship and The Swiss School of Public Health Global P3HS, Switzerland

  Doctoral studies 

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

  provided funding for Cochrane Schizophrenia Group

External sources

• NA, Other

  No external sources of support for this review have been obtained

Declarations of interest

DB: none 
GS: none 
PS: is a resident in psychiatry. No other conflict of interest declared.
SB: none 
SG: works as a general practitioner. No other conflict of interest declared.
LB: works as head of clinic at Mental Health Centre Copenhagen (Denmark). LB is the principal investigator of a randomised controlled trial investigating cannabidiol versus risperidone in people with dual diagnosis. LB is an editor of the Cochrane Schizophrenia Group and was completely excluded from the editorial process of this protocol.

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