The number of people who are compulsorily admitted to psychiatric hospitals is rising each year in England,1 as well as several other European countries.2,3 Although compulsory admissions may help to reduce short-term risks, there are negative repercussions for both the individual and healthcare services.4–8 The reasons for these rising rates are complex and debated, and are likely to include socioeconomic, legal and service-related factors.9 Reducing compulsory admissions has been identified as a priority for mental health services,9 but we lack a strong evidence base on the most effective interventions to achieve this.

Crisis-planning interventions may help to prevent relapse, for example by promoting better self-management, or may reduce the need for hospital admissions by encouraging prompt help-seeking or improved community service responses. The presence of crisis plans may also make patients and clinicians more willing to accept voluntary hospital admissions when a crisis occurs, because of greater awareness of indicators of relapse and increased confidence on the part of the patient that their treatment preferences will be respected once admitted, even if capacity is lost.

Crisis-planning interventions are one of the few that have been identified as potentially beneficial in reducing the risk of compulsory admissions. 10 , 11 In this review, we use ‘crisis planning’ as an overall descriptive term for interventions that focus on involving patients in identifying preferences and planning for their care in the event of a future mental health crisis. Multiple types of crisis plan exist that vary in terminology, content and legal enforceability between jurisdictions. In England, advance decisions are legally binding and document a person's instructions for healthcare they want to refuse in the future, if they lose capacity for making treatment decisions at that time. 12 However, if patients have been admitted under the Mental Health Act 2007, doctors' statutory authority to provide treatment overrides advance decisions. 13 In contrast to advance decisions, advance statements can be used to describe a person's preferences for the care they would like to receive, as well as treatments they want to refuse, but are not legal documents. 14 Joint crisis plans are a type of advance statement developed collaboratively between the patient and mental health professionals, which are also not legally enforceable. In Scotland, advance decisions (which indicate which treatments a person wants to refuse) are known as advance directives, but are not legally binding. 15 In the USA, psychiatric advance directives provide documentation of people's preferences for future mental health treatment during a crisis, with legislation varying by state ( https://www.nrc-pad.org/ ).

A previous review of interventions to reduce compulsory psychiatric admissions found that crisis plans were the only intervention that appeared to be effective, 16 with pooled estimates for community treatment orders (three randomised controlled trials (RCTs)), adherence enhancement (two RCTs) and integrated treatment (four RCTs) showing no significant effects. However, this review gave little information on the core components of the crisis-planning interventions and did not examine important secondary outcomes, including voluntary admissions, length of stay and therapeutic alliance. We therefore conducted a thorough up-to-date systematic review of RCTs examining crisis-planning interventions for people with psychotic illness or bipolar disorder. The primary review question examines whether crisis-planning interventions are effective for reducing compulsory admissions among people with psychotic illness or bipolar disorder, compared with treatment as usual. Secondary review questions examine the impact of crisis-planning interventions on other outcomes of interest including voluntary admissions, duration of in-patient treatment, psychiatric functioning, quality of life, therapeutic alliance, patient engagement, perceived coercion, adverse effects and cost-effectiveness.

Random-effects meta-analysis was also used to pool data for each of the secondary outcomes, if three or more comparable studies were identified. Risk ratios were pooled for dichotomous outcomes and standardised mean differences were calculated and combined for continuous outcomes. If insufficient comparable studies were identified for any planned analyses, narrative synthesis was used. Key components of crisis-planning interventions from the included studies were also described and compared.

The main meta-analyses were conducted including only participants for whom outcome data was available (i.e. complete case analysis). Such analysis assumes that data are missing at random. Sensitivity analyses were performed to investigate the robustness of findings to changing assumptions regarding the mechanism of missing data, as recommended in the Cochrane Handbook for Systematic Reviews of Interventions . 19 Four different assumptions were made to complete the missing data: first, that participants lost to follow-up had no compulsory admissions; second, that they had the same rate of compulsory readmissions as other participants in the same arm of the same trial; third, that the proportion of readmissions was 10 percentage points lower among those lost to follow-up; and finally, that the proportion of readmissions was 10 percentage points higher among those lost to follow-up. An additional sensitivity analysis excluded studies with high risk of bias in any domain from the meta-analysis. Finally, an influence analysis was conducted in which each study was removed in turn from the meta-analysis. If sufficient (ten or more) studies were included in any meta-analysis, a funnel plot would be used to investigate potential publication bias. 20

The number of participants with and without the primary outcome of compulsory psychiatric admission was extracted from all studies for the intervention and control groups separately. A pooled risk ratio (RR) with 95% CI was calculated through random-effects meta-analysis using the Mantel–Haenszel method. Heterogeneity between trials included in the meta-analyses was investigated by visual inspection of the forest plots and calculation of the I 2 statistic. Where there was indication of heterogeneity (for example I 2 statistic higher than 50%), the study quality, clinical population and intervention content were considered as possible explanatory factors. If any studies eligible for the meta-analysis included more than one crisis-planning intervention condition, we combined the active treatment groups into a single arm for comparison against the control group, in line with the recommendations in the Cochrane Handbook for Systematic Reviews of Interventions . 19 A subgroup analysis was planned to pool studies or treatment conditions in which the crisis-planning intervention was facilitated by a healthcare professional, and those where it was not facilitated by a healthcare professional (for example by a patient advocate).

Risk of bias was assessed for each study using the Cochrane Collaboration Risk of Bias Tool 18 , 19 for the following domains: sequence generation, allocation concealment, masking of outcome assessors, incomplete outcome data and selective reporting. Two reviewers conducted risk of bias assessments for all papers independently and any discrepancies were resolved through discussion, including a third author if necessary.

Title and abstract screening and full-text screening were conducted by two reviewers independently. Following title and abstract screening, the full texts of all articles identified as potentially relevant by either reviewer were obtained. Any discrepancies following full-text screening were resolved through discussion with a third author when necessary. Relevant data for the review (relating to the participants, setting, method, intervention, comparison and outcomes) were extracted into a data extraction table and checked by a second reviewer. Authors of the papers were contacted to request additional information if needed, if this related to the primary outcome of compulsory hospital admission.

The following databases were searched from inception to 16 October 2018: Cochrane Central Register of Controlled Trials (CENTRAL), CINAHL, Medline, EMBASE, PsycINFO and the International Standard Randomised Controlled Trial Number (ISRCTN) registry. The search strategy was based around terms for crisis plans or advance directives, mental disorders and RCTs. The full search strategy is available in Supplementary Appendix 1 available at https://doi.org/10.1192/bjo.2019.28 . Conference proceedings from the European Psychiatric Association, World Psychiatric Association, the European Network for Mental Health Service Evaluation and the American Psychiatric Association from 2011 onwards were hand-searched for relevant RCTs. Forward and backward citation tracking were conducted for all eligible studies and for two relevant systematic reviews, 16 , 17 to identify any additional relevant studies.

The primary review outcome was compulsory hospital admission for psychiatric care. The secondary outcomes of interest were: (a) voluntary hospital admission for psychiatric care; (b) any hospital admission for psychiatric care; (c) duration of in-patient psychiatric treatment; (d) global and specific psychiatric symptoms; (e) psychiatric functioning; (f) quality of life; (g) therapeutic alliance; (h) service engagement; (i) perceived coercion; (j) adverse effects; and (k) cost-effectiveness. These outcomes could be assessed at any time point.

Cost-effectiveness was not reported in any of the main trial papers. However, economic evaluations were published separately for two of the included trials. 10 , 21 For the Henderson et al 10 trial, cost-effectiveness acceptability curves suggested that there was over 78% probability that joint crisis plans were more cost-effectiveness than usual care. 26 The economic evaluation of the Thornicroft et al 21 trial found a similar overall probability (80%) that joint crisis plans were more cost-effective than usual care. 27

Thornicroft et al 21 reported no evidence of a difference in perceived coercion, service engagement or clinician-rated therapeutic alliance between groups. However, there was evidence for a slight improvement in patient-rated therapeutic relationship, assessed by the Working Alliance Inventory Client (WAIC), in the intervention group compared with controls after adjusting for variables associated with trial design and loss to follow-up (mean difference −1.28, P = 0.049, adjusted for baseline WAIC score, site, number of previous admissions and diagnosis). 21 Ruchlewska et al 11 reported no difference in service engagement or working alliance (either patient or clinician rated) between the intervention arms and the control group. Lay et al 22 did not report these outcomes at 24 months, but found no group differences in perceived coercion at 12 months post-randomisation. 25 Two trials did not report any outcomes related to therapeutic alliance, service engagement or perceived coercion. 10 , 23

One study reported on psychiatric symptoms and functioning at 12 months’ follow-up, 23 and found no difference between the intervention and control groups. Lay et al 22 did not report psychiatric functioning at 24 months, but found no difference in functioning in an interim analysis at 12 months post-randomisation. 22 , 25 Finally, one study examined patients' insight into their psychiatric symptoms, 11 again reporting no difference between the intervention and control groups. None of the trials included in this review reported quality of life.

Only two studies reported data on duration of admissions among those who had received an admission during the study period. One of these studies (Henderson et al 10 ) reported that there was no difference in length of compulsory admissions between the intervention and control groups, and the other (Ruchlewska et al 11 ) reported no difference in overall length of admissions (compulsory and voluntary combined). Four of the studies compared duration of admissions in the intervention and control groups for their entire samples (i.e. also including those who had not received an admission during the study period as having zero days of admission), using means, medians or counts. Of these four studies, two found no difference between the intervention and control groups for the duration of compulsory or voluntary admissions. 21 , 23 In contrast, two studies reported that the mean length of compulsory admissions was lower for the intervention than the control group, but there was no difference in the length of any admissions 10 or voluntary admissions. 22

Three studies reported the prevalence of voluntary hospital admissions 11 , 22 , 23 and three reported the overall prevalence of admissions to psychiatric care (i.e. including both compulsory and voluntary admissions). 10 , 11 , 21 Pooled estimates for these secondary outcomes showed no evidence that crisis-planning interventions reduced the risk of voluntary admissions (RR = 1.17; 95% CI 0.91–1.50; see Fig. 5 ) or any psychiatric admissions (RR = 0.90, 95% CI 0.74–1.09; see Fig. 6 ).

An additional sensitivity analysis was conducted to exclude studies with high risk of bias from the meta-analysis. Only one study (Lay et al 22 ) had high risk of bias in any domain relating to the primary outcome. After excluding this study, the pooled effect was slightly attenuated (RR = 0.78, 95% CI 0.60–1.01). Finally, influence analyses were conducted to remove each study in turn from the pooled estimate. As described previously, excluding Lay et al 22 slightly attenuated the relationship, but other influence analyses did not alter conclusions (see Supplementary Appendix 3 for full details).

Sensitivity analyses were conducted to investigate the robustness of the findings (see Supplementary Appendix 3). First, the proportion of compulsory admissions was calculated under four different assumptions for missing outcome data. All four analyses gave comparable findings to the main results. The pooled estimate was RR = 0.70 (95% CI 0.54–0.90) under the assumption that there were no compulsory admissions among participants with missing follow-up data and RR = 0.74 (95% CI 0.61–0.91) under the assumption that participants with missing follow-up data had the same rate of compulsory admissions as participants with follow-up data in the same arm of that trial. Assuming that the rate of compulsory readmissions was either 10 percentage points lower or higher among participants with missing data, the pooled estimates were RR = 0.72 (95% CI 0.57–0.92) and RR = 0.77 (95% CI 0.63–0.94), respectively.

There were only two studies that examined crisis-planning interventions that were not facilitated by a healthcare professional, so these results were not pooled using meta-analysis. There was no evidence that the crisis-planning intervention facilitated by researchers in Papageorgiou et al 's 23 trial was effective in reducing compulsory hospital admissions. In Ruchlewska et al 's 11 trial, 16% of participants receiving patient-advocate-facilitated crisis plans were admitted under court order in the follow-up period, compared with 10% in the clinician-facilitated crisis plan group and 26% in the control group.

The results of all five studies were pooled using random-effects meta-analysis, as shown in Fig. 3 . The pooled estimate showed a 25% reduction in compulsory admissions among those receiving crisis-planning interventions compared with those who did not receive the intervention (RR = 0.75, 95% CI 0.61–0.93, P = 0.008). There was no evidence of moderate or substantial heterogeneity 24 ( I 2 = 0%, χ 2 = 3.94, d.f. = 4, P = 0.41). A subgroup analysis was conducted to pool studies 10 , 21 , 22 or treatment conditions 11 in which the crisis-planning intervention was facilitated by a healthcare professional, which gave a similar estimate (RR = 0.67, 95% CI 0.49–0.92; based on four studies; see Fig. 4 ).

All five trials reported the number of participants who had a compulsory admission or readmission to hospital during the follow-up period, which ranged from 12 to 24 months. Based on complete case analysis, the proportion of participants experiencing compulsory admissions in each study ranged from 13% to 28% in the intervention groups and 20% to 43% in the control groups.

In four studies, the risk of attrition bias was low. The primary outcome of compulsory admissions was largely collected from hospital records meaning that missing data for the primary outcome was less than 4% in four studies. 10 , 11 , 21 , 23 However, in one study, 22 readmission data was only reported for participants who completed the outcome assessments. This study was rated as having high risk of attrition bias as loss to follow-up was unbalanced between groups (32.8% from the intervention group and 14.3% from the control group).

Figure 2 summarises the risk of bias in the included trials, assessed using the Cochrane collaboration tool. 18 Three trials had low risk of bias for sequence generation 10 , 21 , 23 and two had low risk of bias for allocation concealment. 10 , 21 The remaining studies had unclear risk of bias in these domains, with insufficient detail provided in trial reports. None of the trials were able to mask the participants or staff, because of the nature of the intervention, so this was not included in the risk of bias assessment. However, masking of outcome assessors was examined. Three of the five trials did not mask outcome assessors to group allocation, 11 , 22 , 23 which could lead to risk of detection bias. However, the impact of detection bias on the primary outcome of this review (compulsory hospital admissions) should be limited, as this was assessed or cross-checked with hospital records in all included studies. Risk of bias was therefore assessed separately for the primary and secondary outcomes, and studies in which no masking was performed were rated as having unclear risk of bias for the primary outcome, and high risk of bias for the secondary outcomes.

A summary of the intended components of the interventions are given in Table 2 , and a detailed description of the content of each intervention and control condition is reported in Supplementary Appendix 2. None of the crisis plans examined in the included RCTs were legally enforceable.

Finally, one trial examined a crisis-planning intervention that was facilitated by a healthcare professional (psychologist) without involvement from the patient's clinical team. 22 This trial implemented a higher intensity crisis-planning intervention, in which participants in the intervention group attended a varying number of individualised psychoeducation sessions focused on identifying behaviours prior to crisis and developed crisis cards consisting of future treatment preferences. In addition, they received 4-weekly telephone monitoring, to review the crisis cards and facilitate the detection of early signs of crisis identified in the previous psychoeducation sessions.

There was some variation in the components of the crisis-planning interventions across the included trials. In two trials, the intervention commenced while participants were psychiatric in-patients; 22 , 23 the other three trials recruited out-patients with previous psychiatric admissions. 10 , 11 , 21 One trial 23 examined the effectiveness of a type of advance statement, in which participants completed a booklet consisting of seven statements on future treatment preferences, with support from researchers. Three trials examined joint crisis-planning interventions. 10 , 11 , 21 One of these included two intervention groups; participants could be randomised to a clinician-facilitated crisis plan (i.e. joint crisis plan) or a patient-advocate facilitated crisis plan. 11 In the other two trials of joint crisis plans, 10 , 21 the crisis plan was facilitated by a healthcare professional who was part of the research team, and discussed at one or more meetings with members of the patient's clinical team, and a family member or friend if they wished.

Key characteristics of the five included studies are given in Table 1 . Three trials only included participants with psychotic disorders or bipolar disorder, 10 , 11 , 21 whereas the other two trials included mixed populations from secondary care mental health services. 22 , 23 All of the trials reported a majority diagnosis of schizophrenia or schizophrenia-like disorders. Follow-up periods for the trials ranged from 12 to 24 months. In all five trials, the crisis-planning intervention was compared with treatment as usual, however, in one trial the control group also received an information leaflet about local mental health services and the Mental Health Act. 10

The search strategy identified 1428 studies, of which 1023 remained after duplicates were removed. Through title and abstract screening, 964 records were excluded. Full texts for the remaining 59 studies were obtained and assessed for eligibility. Five studies met the inclusion criteria and were included in the review. The study selection process is shown in Fig. 1 .

Discussion

This systematic review identified five RCTs that examined the effectiveness of crisis-planning interventions for adults with psychotic illness or bipolar disorder. A meta-analysis of these studies showed a 25% reduction in risk of compulsory hospital admissions among those receiving crisis-planning interventions compared with usual care, a finding that was found to be robust in multiple sensitivity analyses. In contrast, there was no evidence for a reduction in voluntary admissions or total psychiatric admissions, and the pooled estimate for voluntary admissions showed a trend towards increased risk following crisis-planning interventions. It may be that crisis-planning interventions do not prevent admissions entirely but can reduce compulsory admissions rates by shifting some of these to voluntary admissions.

Our findings are in keeping with a previous systematic review that examined interventions to reduce compulsory psychiatric admissions.16 That review identified four RCTs investigating the effectiveness of crisis-planning interventions (including advance statements and joint crisis plans), with searches conducted in April 2015. Our review updates this previous review, including one additional trial of an intensive crisis-planning intervention22 and provides further details on the characteristics of the interventions and the secondary outcomes of these trials. These details are important for clinicians considering implementing crisis-planning interventions or for researchers planning future studies in this area. Implications for research and clinical practice are described in the final section of this discussion.

Although the pooled estimate shows that crisis-planning interventions were effective in reducing compulsory admissions, there was variation between individual studies both in the characteristics and the effectiveness of the crisis-planning interventions. All of the included RCTs found a trend for a positive effect of crisis-planning interventions but this was not statistically significant in three of the five original studies. The meta-analysis is therefore an important contribution to the evidence base as consideration of the trials individually might have led to more cautious conclusions about the effectiveness of crisis-planning interventions.

Thornicroft et al21 found no evidence that their intervention was effective in reducing compulsory admissions. This is the largest included study and was assessed to have low risk of bias in all domains, so the null finding could reduce confidence in the overall positive conclusion from our meta-analysis. Thornicroft et al themselves considered potential explanations for their null finding, which was in contrast with the Henderson et al10 trial that followed a highly similar protocol in a smaller sample. In the Thornicroft et al trial, it was found that almost 50% of the crisis plans were developed during usual clinical review meetings as staff had not made themselves available to discuss the crisis plan at a specific time. Qualitative interviews conducted with participants in Thornicroft et al's trial suggested that this had an impact on the patients' experiences, as many could not remember the crisis-planning meeting as being distinct from other routine meetings, and also commented that the content of their plans was not followed during subsequent crises. Problems with implementation of the crisis-planning intervention were also reported in other studies, for example, Ruchlewska et al reported that only 57% of the clinician-facilitated crisis plans were completed.11 It is notable that the pooled estimate showed a positive impact of crisis-planning interventions given these implementation challenges.

Methodological strengths and limitations This review provides an updated account of the effects of crisis-planning interventions for people with psychotic illness or bipolar disorder, and highlights that these interventions may be effective in reducing risk of compulsory hospital admissions. However, the conclusions of this review are limited by the small number of studies included, particularly in some subgroup analyses, and the fact that all included trials were conducted in Europe. The review was limited to RCTs because these represent the gold standard when evaluating interventions.19 Observational studies and studies using routine hospital data may also generate valuable evidence about the effectiveness and implementation of these interventions outside experimental conditions and could be included in future reviews. A strength of this review was the inclusion of secondary outcomes such as quality of life, psychiatric functioning, perceived coercion and therapeutic alliance, which were not examined in the earlier systematic review of interventions to reduce compulsory admissions.16 However, these were not widely assessed in the included trials, thus limiting our ability to draw conclusions about the effectiveness of crisis-planning interventions for these outcomes. Several trials included in this review reported that a high proportion of the patients approached were either ineligible or declined to participate. Low rates of recruitment are common for trials on psychotic illness or bipolar disorder, where there is often a multitude of factors that can prevent a person from taking part in research.28 Nevertheless, recruitment rates can be an important indicator of the acceptability of an intervention, and low recruitment rates may also suggest that participants are not representative of the target population. Three out of the five trials included in this review reported a lower number of compulsory admissions in the control arm than was initially predicted from local routine data, which may be the result of systematic differences between those who agreed to participate in the trials and those who did not. Only studies conducted in Europe were identified so our findings may have limited generalisability to other settings. In addition, changes in clinical practice and service funding over time may limit the applicability of studies such as Henderson et al's (published in 2004)10 to the current context. Our review focused on crisis-planning interventions for individuals with psychotic disorders and bipolar disorder, meaning that we are unable to draw conclusions about the effectiveness of crisis-planning interventions for other groups at risk of compulsory admission. However, there is very little evidence for other disorders. One previous pilot RCT examined crisis-planning interventions for individuals with a diagnosis of personality disorder29 but did not include compulsory admissions as an outcome. In addition, none of the RCTs included in this review examined advance decisions that were legally binding, so it is not clear what impact the legal basis would have on risk of compulsory hospital admissions. Loss to follow-up is also a common problem for RCTs; however, this had limited impact on the primary outcome of this review that was collected from routine records for the majority of the trials. The exception to this is Lay et al,22 who only had readmission data for participants who completed the follow-up interviews. This study was rated as having high risk of attrition bias as there was substantial loss to follow-up that was unbalanced between study groups. However, we examined multiple different assumptions for imputing missing data in sensitivity analyses and these did not alter the overall conclusions, so we believe our findings are robust to the missing data in this study. All studies had low or unclear risk of bias in the other domains assessed, with the exception of masking of outcome assessors. In addition, no studies included masking of participants or study personnel, because of the nature of the intervention. Lack of masking is unlikely to lead to bias for the primary outcome, for which data on compulsory admissions was extracted from medical records but may have led to bias in the secondary outcomes.