Post‐incident debriefing for people with schizophrenia after coercive measures

Objectives

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

To investigate the effects of post‐incident debriefing after coercive measures for people with schizophrenia or schizophrenia‐type psychosis.

Background

Description of the condition

Schizophrenia

Schizophrenia and schizophrenia‐type psychosis are severe mental illnesses (WHO 2022). They are classified in the International Classification of Diseases (ICD)‐11 as F20 to F29, schizophrenia, schizotypal, delusional, and other non‐mood psychotic disorders (WHO 2019); and in the Diagnostic and Statistical Manual of Mental Disorders (DSM)‐5 as schizophrenia and other psychotic disorders (APA 2013). Schizophrenia alone affects almost 21 million people globally (Charlson 2018). About 71% (14.8 million) of cases occur among people between 25 and 54 years of age (Charlson 2018). It has been estimated that the incidence of schizophrenia per year is 15.2 cases per 100,000 population, while the lifetime prevalence is 7.2 cases per 1000 (McGrath 2008). The disorder usually onsets in late adolescence or early adulthood (Gogtay 2011).

Schizophrenia is characterised by positive and negative symptoms (Tandon 2013). Positive symptoms may include hallucinations, delusions, disorganised speech, and catatonic or grossly disorganised behaviour, while negative symptoms include diminished emotional expression and avolition (Tandon 2013). For a person to be diagnosed with schizophrenia, symptoms must be present for at least one month within the last six months, and be accompanied by social or occupational dysfunction (APA 2013; Tandon 2013). The illness may also cause cognitive impairments (Keefe 2008).

Not only does schizophrenia cause a high economic burden (Chong 2016), it also has a significant negative impact on those who suffer from the illness. Schizophrenia accounts for 13.4 million YLDs (years lived with disease) globally, equivalent to 1.7% of total YLDs in 2016 (Charlson 2018). People suffering from schizophrenia also have a higher risk of developing certain somatic illnesses, such as type 2 diabetes (Vancampfort 2015), and metabolic syndrome (Ward 2015). High mortality rates have been found in all age groups, and the life expectancy of people with schizophrenia is approximately 20 years lower than that of the general population (Laursen 2014). The illness may also negatively impact one’s quality of life (Savilla 2008).

Coercive measures

In its acute stage, especially when positive symptoms are present (Rund 2018), violent behaviour may occur in people with schizophrenia (Iozzino 2015). In psychiatric hospitals, coercive measures may be used to manage violent or aggressive behaviour, to ensure the safety of people with schizophrenia and others (Thibaut 2019). However, the use of coercive measures is a controversial issue, as it may violate a person's human rights and freedom of movement (Montaguti 2019). According to the National Institute for Health and Care Excellence (NICE), coercive measures include: 1) close observation, during which a staff member observes and maintains contact with the person; 2) a seclusion room is a specific, locked room in which a person is put for supervised confinement; 3) manual restraint is a hands‐on method of physical restraint used by staff; mechanical restraint is a physical intervention, during which staff uses authorised equipment to restrain the individual (e.g. handcuffs or restraining belts); 4) rapid tranquillisation is the use of parenteral medication for urgent sedation, if oral medication is not possible (NICE 2015).

The use of coercive measures varies across countries. A nationwide cohort study, following 112,233 people in Denmark between 1999 and 2014, found that 22% of people treated in inpatient psychiatric services were exposed to different types of coercion (Thomsen 2017). In Finland between 1995 and 2014 (N = 226,948 participants), the overall prevalence of coercive treatment for inpatients was 9.8% (Välimäki 2019). A study in Norway found that from the 19,283 people admitted to hospitals between 2004 and 2011, 324 were exposed to restraint, which included a total of 1458 cases (mean 4.5 cases per exposed person); 9% were mechanical restraints, and 41% were pharmacological restraints (Reitan 2018). In 2011, in the Netherlands, 11% of all people admitted to psychiatric hospitals (N = 42,960) experienced seclusion (Noorthoorn 2015).

Researchers have found a number of characteristics associated with the use of coercive measures. Personal characteristics associated with higher odds for experiencing coercive measures are: being male (Reitan 2018; Thomsen 2017), younger than 50 years old, having a history of substance abuse, and a diagnosis of schizophrenia spectrum disorder or mood disorder (Reitan 2018). Researchers also found that lower socioeconomic class, unemployment, and being an immigrant from a low‐ or middle‐income country increased the odds for experiencing coercion. However, having social relations, such as being a parent or being married, seems to protect people from being coerced (Thomsen 2017). Other factors related to being coerced include the treatment culture on the ward (Husum 2010), and the characteristics of the direct‐care staff (Beghi 2013).

Coercive measures have an impact on people and their well‐being. The psychological impact may include significant distress (Frueh 2005), humiliation (Robins 2005), or a depressed or powerless state of mind (Fugger 2016). Re‐traumatisation (Strout 2010), and post‐traumatic stress disorder have also been reported as outcomes of coercive methods (Fugger 2016). Physical impacts may include injuries, and even death (Kersting 2019). Associations between coercion and treatment outcomes, such as longer inpatient stays and a person's disapproval of treatment, have also been found (McLaughlin 2016). Overall, a person's experiences of being subjected to coercion are negative (Askew 2019). Still, some contrary results have been found. For example, Soininen and colleagues reported that neither seclusion nor restraints were significantly associated with a person's quality of life (Soininen 2013).

Description of the intervention

Post‐incident debriefing is an intervention that could support efforts to reduce use (Huckshorn 2014; Whitecross 2013), and duration (Goulet 2018), of coercive measures, aggressive incidents (NICE 2015), and post‐traumatic symptoms following the use of coercive measures (Abdelghaffar 2018). Incident refers here to both the use of coercive measure itself, and the situation (e.g. violent behaviour) that led to the use of coercive measures. 

Based in psychology, debriefing can be defined as a set of procedures, including counselling, that give information to prevent psychological morbidity and aid in recovery after a traumatic event (Kenardy 2000). According to the literature, post‐incident debriefing related to use of coercive measures is defined in numerous ways, and may include a number of different elements. Post‐incident debriefing can be defined as an intervention, conducted immediately after coercive measures, when those involved have recovered their composure, and when the risk of harm related to the event has been contained (NICE 2015). Debriefing has also been described as a form of talking therapy, during which the involved parties recount the incident (Needham 2010). The Restraint Reduction Network defines this intervention as a post‐incident review, which has two main components: post‐incident support, i.e. attention to the physical and emotional well‐being of the individuals involved, and a post‐incident reflection and learning review (RRN 2019). The Six Core Strategies for reducing and preventing the use of seclusion and restraint include the use of rigorous debriefing techniques, which is defined as systematically analysing seclusion and restraint incidents, and the use of acquired knowledge to inform policy, procedures, and practices to avoid future incidents (Huckshorn 2014). 

The aim of debriefing is to provide the staff and people with schizophrenia with the opportunity to jointly learn why incidents leading to the coercion happened (Petti 2001). It usually takes place within the first few days after a traumatic event, and may last one to three hours (Kenardy 2000). It may include a discussion about the factors that contributed to the incident that led to the use of coercive measures, and typically acknowledges the emotional responses to the incident, assesses the need for emotional support or possible trauma experienced, supports feelings of safety and relaxation, and encourages a return to normal activities (NICE 2015). It offers the person the opportunity to make sense of the experience (Needham 2010), and share the emotional experience (Zech 2005). The intervention may include counselling, ventilation, support and reassurance, physical intervention, and psychoeducation (Needham 2010; Whitecross 2013). The intervention may be led by a nurse (Needham 2010; Whitecross 2013), psychologist, social educator, or a doctor (Hammervold 2020), who was not involved in the incident (NASMHPD 2006).

For the purpose of this review, we will define post‐incident debriefing as a structured or unstructured discussion related to the use of a coercive measure, involving staff and the person with schizophrenia, with or without their families (Scanlan 2010).

How the intervention might work

There are no standardised procedures or techniques for post‐incident debriefing after coercive measures. Essential components of the debriefing intervention are inconsistently described in related literature (Mangaoil 2018). Thus, interventions used to describe debriefing vary from study to study (Hammervold 2019). Kaplan has argued that debriefing could assist in preventing permanent emotional injury, by allowing time for emotional processing, cognitive appraisal, and normalisation of reactions to a traumatic experience (Kaplan 2001). The mechanism behind a debriefing intervention is learning together about why the event that led to the use of coercion by staff occurred, and any other useful information about that specific event (Petti 2001). Therefore, in a debriefing session, it is possible to identify risk factors that can be addressed to reduce the likelihood of a future event, and amend the risk and care plans accordingly (Hirsch 2019; NICE 2015). It has also been assumed that analysing past incidents can reduce the future use of seclusion and restraint (Huckshorn 2014).

Why it is important to do this review

Post‐incident debriefing is recommended as an intervention to be used after coercive measures (NICE 2015). It has been reported to have several benefits: for example it reduces the emotional impact of coercive measures (Aguilera‐Serrano 2018), helps to restore the therapeutic relationship between the person with schizophrenia and staff (Goulet 2018; Wullschleger 2019), allows participants to find individual alternatives for coercion (Huckshorn 2014), assists in changing the culture of psychiatric settings (Petti 2001), increases ethical awareness for the staff (Hammervold 2020), and leads to better care for people with schizophrenia and schizophrenia‐type psychosis.

Based on published research results, post‐incident debriefing is in place in the United Kingdom, Canada, the United States, Norway, Sweden, Finland, and Germany (Hammervold 2019; Hammervold 2020; Putkonen 2013; Steinert 2020; Wullschleger 2019). However, evidence behind the recommendations in the NICE guideline for the use of post‐incident debriefing intervention is based on qualitative studies, which lack information about actual effectiveness of the intervention (NICE 2019). There has been debate over whether debriefing should be used in inpatient care, due to its possible harmful psychological effects on people (NICE 2019). The effectiveness of debriefing has also been questioned, especially in preventing post‐traumatic stress disorder after traumatic events (Rose 2002). To address these controversies, there is a need to conduct a systematic review of all available evidence evaluating the effectiveness of post‐incident debriefing after the use of coercive measures.

Objectives

To investigate the effects of post‐incident debriefing after coercive measures for people with schizophrenia or schizophrenia‐type psychosis.

Methods

Criteria for considering studies for this review

Types of studies

We will consider all relevant randomised controlled trials (RCT). We will include RCT meeting our inclusion criteria. We will consider trials that are described as double‐blind, in which randomisation is implied. We will also consider cluster‐randomised, and the first phase data of cross‐over trials.

We will exclude quasi‐randomised studies, such as those that allocate intervention by alternate days of the week. When people are given treatments additional to post‐incident debriefing, we will only include data if the adjunct treatment is evenly distributed between groups, and it is only the post‐incident debriefing that is randomised.

Types of participants

In this review, we will include adult participants, who have been diagnosed with a wide spectrum of schizophrenia or schizophrenia‐type psychosis (F20 to F29, schizophrenia, schizotypal, delusional, and other non‐mood psychotic disorders (ICD‐11 (WHO 2019); Schizophrenia and Other Psychotic Disorders, DSM‐5 (APA 2013)).

We will include trials in which the majority (> 50%) of the participants had a severe mental illness, which is likely to be schizophrenia or schizophrenia‐type psychosis, including those with multiple diagnoses, and those who have already been subjected to coercive measures. Adult participants will not be excluded due to age, nationality, gender, duration of illness, or treatment setting.

We want to make sure that information is as relevant as possible to the current care of people with schizophrenia or schizophrenia‐type psychosis, so aim to clearly highlight the current clinical state (acute, early post‐acute, partial remission, remission), 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

1. Post‐incident debriefing plus standard professional care

For the purpose of this review, we will define post‐incident debriefing as either a structured or unstructured discussion about the use of coercive measure, involving staff and the person with schizophrenia, with or without their families (Scanlan 2010). We will also consider interventions labelled as post‐incident review as a synonym for post‐incident debriefing. For our main comparison, we will consider only post‐incident debriefing as an intervention. 

2. Standard professional care

Standard professional care to people with schizophrenia for whom no post‐incident debriefing is used after coercive measures.

Types of outcome measures

We aim to divide all outcomes into immediate (less than one day), short‐term (one to seven days), medium‐term (up to two months), and long‐term (longer than two months).

We will endeavour to report binary outcomes that record clear and clinically meaningful degrees of change first (e.g. global impression of much improved, or more than 50% improvement on a rating scale, as defined within the trials). Thereafter, we will list other binary outcomes, and then continuous outcomes.

Primary outcomes

1. Further seclusion and restraint

1.1 Further use of a seclusion room (placing the person in a locked room from which free exit is denied; involves isolation with or without the reduction of sensory stimuli)

1.2 Further use of mechanical/physical restriction (devices are used to restrict a person's free movement, such as belts/physical holding)

Secondary outcomes

1. Mental state (specific symptoms)

1.1 Clinically important change in specific symptoms, as defined by each of the studies (positive, negative, affective, cognitive symptoms of schizophrenia or schizophrenia‐type psychosis)

1.2 Any change in specific symptoms, as defined by each of the studies (positive, negative, affective, cognitive symptoms of schizophrenia or schizophrenia‐type psychosis)

1.3 Average end point or change score on specific symptom scale (e.g. post‐traumatic stress disorder (PTSD), measured by Clinician‐Administered PTSD Scale (CAPS (Weathers 2013)) 

1.4 Mental state (general symptoms, e.g. overall symptoms of schizophrenia, measured by Positive and Negative Syndrome Scale (PANSS) total (Kay 1986))

2. Satisfaction with care (recipients of care or carers; including subjective well‐being and family burden)

2.1 Recipient

2.1.1 Clinically important change in satisfaction, as defined by each of the studies

2.1.2 Recipient of care satisfied/not satisfied with treatment

2.1.3 Recipient of care average end point or change score on satisfaction scale (e.g. patient satisfaction measured by a scale, such as Mental Health Care Thermometer for Appreciation of Clients (GGZ (Kok 2003))

2.2 Carers (including health professionals)

2.2.1 Clinically important change in satisfaction, as defined by each of the studies

2.2.2 Carer satisfied/not satisfied with treatment (general impression of carer/other)

2.2.3 Carer average end point or change score on satisfaction scale (e.g. caregiver satisfaction measured by a published scale, such as Client Satisfaction Questionnaire (CSQ (Attkisson 2012))

3. Behaviour

3.1 General

3.1.1 Clinically important change in general behaviour, as defined by each of the studies

3.1.2 Any change in general behaviour, as defined by each of the studies

3.1.3 Average end point or change score on general behaviour scale (e.g. patient behaviour measure by Brief Psychiatric Rating Scale (BPRS (Overall 1962))

3.2 Specific

3.2.1 Clinically important change in specific aspects of behaviour, as defined by each of the studies, e.g. aggression, violence

3.2.2 Any change in specific aspects of behaviour, as defined by each of the studies, e.g. aggression, violence

3.2.3 Average end point or change on specific aspects of behaviour scale (e.g. patient aggression measured by a published scale, such as Staff Observation Aggression Scale – Revised (SOAS‐R (Nijman 1999)) 

4. Additional medication

4.1 Use of rapid tranquillisation/increased medication (medication administered by parenteral route, if oral medication is not possible or appropriate, and urgent sedation with medication is needed)

4.2 Use of rapid tranquillisation/increased medication (oral medication for rapid tranquillisation)

5. Use of compulsion 

5.1 Other treatment or detainment against a person's will, besides seclusion or restraints

6. Quality of life (recipient of care)

6.1 Overall

6.1.1 Clinically important change in quality of life, as defined by each of the studies
6.1.2 Any change in quality of life, as defined by each of the studies
6.1.3 Average end point or change score on quality of life scale (e.g. quality of life measured by a rating scale, such as World Health Organization Quality of Life (WHOQOL (WHO 2004))

6.2 Specific

6.2.1 Clinically important change in specific aspects of quality of life, as defined by each of the studies
6.2.2 Any change in specific aspects of quality of life, as defined by each of the studies
6.2.3 Average end point or change score on specific aspects of quality of life scale (e.g. health‐related quality of life measured by Health‐Related Quality of Life scale (HRQOL‐14 (Moriarty 2003)) 

7. Adverse events and safety

7.1 Suicide attempts

7.2 Death (all causes)

7.3 Injuries

7.4 Occupational injuries

8. Adverse effects

8.1 General adverse effects

8.1.1 At least one adverse effect

8.1.2 Clinically important adverse effects

8.1.3 Average end point or change scores on adverse‐effect scales (e.g. unwanted events, measured by a scale, such as Unwanted Event to Adverse Treatment Reaction (UE–ATR) checklist (Linden 2013))

8.2 Specific adverse effects 

8.2 Clinically important, as defined by each of the studies

9. Acceptability of intervention 

Number of participants leaving the study early:

9.1 For any reason
9.2 Due to inefficacy
9.3 Due to adverse effect

10. Economic outcomes

10.1 Costs due to treatment, as defined by each study
10.2 Total direct and indirect costs
10.3 Average change in total cost of medical and mental health care

Search methods for identification of studies

Electronic searches

The Information Specialist (IS) will search the Schizophrenia Group's Specialised Register using the following search strategy: [(*seclusion*) AND (*post*)] OR [(*incident*) AND (*post*)] [(*restraint*) AND (*review*)] in abstract terms of REFERENCE)]

The Schizophrenia Group's Specialised Register is a study‐based register, which allows the information specialist (IS) to search the major concept and retrieve 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 Cochrane methods, the IS compiles this register from systematic searches of major resources and their monthly updates (unless otherwise specified (Lefebvre 2022)).

• CENTRAL (Cochrane Central Register of Controlled Trials)

• MEDLINE

• Embase

• PubMed

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

• PsycINFO

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

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

• ISRCTN registry

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

The Specialised Register also includes the results of handsearches and conference proceedings (see schizophrenia.cochrane.org/resources). 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 corresponding 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

Review authors TL and JV will independently inspect citations from the searches and identify relevant abstracts. When disputes arise, we will acquire the full report for more detailed scrutiny; when necessary, a third reviewer will be consulted. TL and JV will then obtain and inspect full reports of the abstracts or reports meeting the review criteria. MV will re‐inspect a random 20% of these full reports, in order to ensure reliability of selection. When it is not possible to resolve disagreement by discussion, we will attempt to contact the authors of the study concerned, for clarification.

Data extraction and management

1. Extraction

Review authors TL and JV will independently extract data from all included studies. We will attempt to extract data that is only presented in graphs and figures whenever possible, but will only include them if two reviewers independently obtain the same result. We will discuss any disagreement and document our decisions. If necessary, we will attempt to contact trial authors with an open‐ended request, to obtain missing information, or for clarification. MV will help clarify issues regarding any remaining problems, and we will document these final decisions.

2. Management

2.1 Forms

We will extract data onto standard, predesigned, simple forms.

2.2 Scale‐derived data

We will include continuous data from rating scales only if:

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

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

3. the instrument is a global assessment of an area of functioning and not sub‐scores, which are not, in themselves, validated or shown to be reliable. However, there are exceptions, we will include sub‐scores from mental state scales measuring positive and negative symptoms of schizophrenia or schizophrenia‐type psychosis. Ideally, the measuring instrument should be either a self‐report, or completed by an independent rater or relative (not the therapist). We realise that this is not often reported clearly; in the description of studies table, we will note if this was the case.

2.3 End point versus change data

There are advantages to both end point 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 end point), which can be difficult to obtain in unstable and difficult‐to‐measure conditions, such as schizophrenia. We decided to primarily use end point data, and only use change data if the former are not available. If necessary, we will combine end point and change data in the analysis, as we prefer to use mean differences (MDs) rather than standardised mean differences (SMDs) throughout (Deeks 2022).

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 standards to relevant continuous data before inclusion.

For end point 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 (Deeks 2022).

For example, for a scale that has a possible lowest value higher than 0, such as the 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. For 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 have a lowest possible score different from 0, and whether the described adjustment is needed. 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). When there is suggestion of skewedness (ratio < 2), we will exclude the relevant studies in a sensitivity analysis to check if they had an impact on the results (see Sensitivity analysis for further details). These skewed results will 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, since it is difficult to tell whether data are skewed, when continuous data are presented on a scale that includes a possibility of negative values (such as change data).

2.5 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 week, or per month) to a common metric (e.g. mean days per month).

2.6 Conversion of continuous to binary

We will make all efforts to convert outcome measures to dichotomous data. This can be done by identifying cutoff 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 BPRS (Overall 1962), or the PANSS (Kay 1986), this could be considered a clinically significant response (Leucht 2005a; Leucht 2005b). If data based on these thresholds are not available, we will use the primary cutoff presented by the trial authors.

2.7 Direction of graphs

Where possible, we will enter data so that the area to the left of the line of no effect indicates a favourable outcome for post‐incident debriefing. When keeping to this makes it impossible to avoid outcome titles with clumsy double‐negatives (e.g. not un‐improved), we will report data for which 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 TL and MV will independently assess risk of bias by using the RoB 1 criteria described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017). This set of criteria is based on evidence of associations between potential overestimation of effect and the level of risk of bias in the report that may be due to aspects of sequence generation; allocation concealment; blinding of personnel, participants, and outcome assessment; incomplete outcome data, and selective reporting, or the way in which these domains are reported.

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 trial authors to obtain further information. We will report non‐concurrence in the risk of bias 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 (high, low, unclear) in both the text of the review, a summary of the risk of bias graph, 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 clinicians tend to interpret odds ratios as RR (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 calculate illustrative comparative risks, when possible.

2. Continuous data

For continuous outcomes, we will estimate the mean difference (MD) between groups. We prefer not to calculate effect size measures (standardised mean difference (SMD)). However, if similar but different scales are used, we will presume there is little difference in measurement, and we will calculate SMD. 

Unit of analysis issues

1. Cluster trials

Studies increasingly use cluster‐randomisation (such as randomisation by clinician or practice), but analysis and pooling of clustered data pose problems. Trial 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 try to contact trial authors to obtain intra‐class correlation coefficients for their clustered data, and to adjust for this by using accepted methods (Gulliford 1999).

We 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 intra‐class correlation coefficients and relevant data documented in the report have been taken 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

When a study involves more than two treatment arms, we will present the additional treatment arms in comparisons, if relevant. If data are binary, we will simply add these and combine them 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 (McKenzie 2022). When additional treatment arms are not relevant, we will not reproduce these data.

Dealing with missing data

1. Overall loss of credibility

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

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% are lost in one arm of a study, but the total loss is less than 50%, we will address this in the summary of findings table/s by downgrading the certainty of the evidence, but not exclude the study in the sensitivity analysis. Finally, we will also downgrade the certainty of the evidence in the summary of findings table/s should the loss be between 25% and 50% in total.

2. Binary

We will analyse data in an intention‐to‐treat analysis (ITT), in the groups to which they were randomised. When studies present data only on completers, we will still use these studies, but 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 trial authors. If they are not available, and there are missing measures of variance for continuous data, but a standard error (SE) and CI available for group means, and either a P value or t value available for differences in mean, we can calculate the SD, according to the rules described in the Cochrane Handbook for Systematic Reviews of Interventions (McKenzie 2022). When only the SE is reported, the SD will be calculated by the formula SD = SE * √(n). The Cochrane Handbook for Systematic Reviews of Interventions presents detailed formulae for estimating the SD from P, t, or F values, CI, ranges, or other statistics (McKenzie 2022). If these formulae do not apply, we will calculate the SD according to a validated imputation method, which is based on the SD 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 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, are often the core problems in randomised schizophrenia trials. Therefore, we will not exclude studies based on the statistical approach used. However, by preference, we will use the more sophisticated approaches, i.e. we prefer to use MMRM or multiple‐imputation to LOCF, and we will only present completer analyses if ITT data are not available at all. Moreover, we will address this issue when assessing incomplete outcome data in RoB 1.

Assessment of heterogeneity

1. Clinical heterogeneity

We will consider all included studies initially, without seeing comparison data, to judge clinical heterogeneity. We will inspect all studies for participants who are clearly outliers, or situations that we had not predicted would arise, and when found, will discuss 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 inspect all studies for clearly outlying methods that we had not predicted would arise, and discuss any such methodological outliers.

3. Statistical heterogeneity

3.1 Visual inspection

We will inspect forest plots 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 and 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, and the strength of evidence for heterogeneity (e.g. P value from Chi² test, or a confidence interval for I²). We will interpret an I² estimate of 50% or higher, accompanied by a statistically significant Chi² statistic, as evidence of substantial heterogeneity (Chapter 10. Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2022)). When substantial levels of heterogeneity (I² = 50% to 90%) are found for the primary outcome, we will explore reasons for heterogeneity with 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 section 10.1 of the Cochrane Handbook for Systemic reviews of Interventions (Deeks 2022).

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.

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 when there are ten or fewer studies, or when all studies are of similar size. In other cases, when funnel plots are possible, we will seek statistical advice for their interpretation.

Data synthesis

We understand that there is no closed argument for prefered 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. The random‐effects model takes into account differences between studies, even if there is no statistically significant heterogeneity. However, there is 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. Therefore, we will use a fixed‐effect model for all analyses.

Subgroup analysis and investigation of heterogeneity

Subgroup analyses

We do not anticipate subgroup analyses due to the known low number of relevant trials in this research area.

Sensitivity analysis

When possible, we will perform sensitivity analyses for the primary outcomes, 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. Implication of randomisation

We will exclude trials that are described as double‐blind, but where randomisation is not explicitly mentioned.

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 in which the overall loss of data was greater than 50%.

4. Risk of bias

We will exclude trials that are at high risk of bias across one or more of the domains (see Assessment of risk of bias in included studies).

5. Imputed values

We will exclude trials in which we use imputed values for ICC to calculate the design effect in cluster‐randomised trials, or in which we imputed SDs.

6. Fixed‐ and random‐effects

We will re‐synthesise data for the primary outcome using a random‐effects model, to evaluate whether this alters the significance of the results.

7. Skewed data

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

Summary of findings and assessment of the certainty of the evidence

We will use the GRADE approach to interpret findings (Schünemann 2022), and GRADEpro GDT software to export data from our review and create a summary of findings table. For each main comparison, these tables provide outcome‐specific information concerning the overall certainty of evidence from the included studies 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 the person receiving care, and clinical decision‐making. We will include the following main outcomes in the summary of findings table.

1. Further use of a seclusion room

2. Any change in specific symptoms, as defined by each of the studies 

3. Recipient of care satisfied/not satisfied with treatment

4. Any change in specific aspects of behaviour, as defined by each of the studies, e.g. aggression, violence

5. At least one adverse effect

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

MV ‐ initiation of the protocol, development and writing the protocol

JV ‐ writing the protocol

TL ‐ development and writing the protocol

Sources of support

Internal sources

• University of Turku, Finland

  Internal fund 26003424 (Maritta Välimäki); Department of Nursing Science (Maritta Välimäki); and the Doctoral Programme in Nursing Science (Jaakko Varpula).

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

  provided funding for Cochrane Schizophrenia Group

External sources

• Academy of Finland, Finland

  Grants 294298 and 307367 (Maritta Välimäki); and 316206 (Tella Lantta)

Declarations of interest

MV ‐ has completed studies and interventions about patient coercion practices (not including post‐incident debriefing)

JV ‐ has joined studies about patient coercion practices (not including post‐incident debriefing)

TL ‐ has completed studies and interventions about patient coercion practices (not including post‐incident debriefing)

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