Enhanced crisis planning for serious mental illness
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
The main objective of this review is to evaluate the effectiveness of crisis planning in reducing/preventing relapse and readmission to psychiatric hospital services.
Background
Description of the condition
In recent years a consensus has emerged in various areas, including the UK, that mental health services should be especially targeted to those suffering from severe mental illness. However, there is no internationally agreed definition of severe mental illness. This is a term used commonly by healthcare professionals but which is remarkably inconsistent in how it is defined (Slade 1996). The definition of severe mental illness with the widest consensus is that of the National Institute of Mental Health (NIMH) (Schinnar 1990). To bring about a degree of consistency, NIMH made an attempt and defined individuals as having severe mental illness if they met three criteria: a diagnosis of non‐organic psychosis or personality disorder; duration characterised as involving "prolonged illness and long‐term treatment" and operationalised as a two‐year or longer history of mental illness or treatment; and disability, which was described as including at least three of the eight specified criteria (NIMH 1987).
A European survey put the total population‐based annual prevalence of severe mental illness at approximately two per thousand individuals (Ruggeri 2000). Severe mental illnesses, especially the schizophrenia spectrum and affective psychotic disorders, present with a wide variety of clinical signs and symptoms. A distressing feature for most people with these disorders is the loss of contact with reality and people of importance to them. In turn this leads to difficulties in social, occupational and emotional well being resulting in this subset of patients requiring special services (Oud 2009). Often, the prognosis for those enduring mental health problems can be guarded. For individuals suffering with schizophrenia, it is often a life‐long illness with frequent relapses and remissions (Bridge 2004). Whilst bipolar disorder may have a slightly better prognosis, up to 70% of patients with one episode of mania are still likely to develop another episode of mania or depression over a four‐year period (Gitlin 1995). These illnesses can afflict people in their formative years and each episode of illness can be sufficiently severe to require inpatient admission, causing considerable erosion in self confidence and deterioration in functioning. Inpatient hospital admissions are punctuated by negative associations, stigma and perception of loss of role.
Description of the intervention
An enhanced or joint crisis plan is a form of advance planning where a document is drawn up by the recipient of care along with professionals who are involved in their care with a view to accessing it if the patient is displaying early warning signs of relapse, such that a clear pathway is described as to what would help the patient in crisis (Flood 2006). The main aim of crisis planning is for the individual and their family to be aware of actions to be undertaken when the patient is becoming unwell, so as to prevent further deterioration and possible rehospitalisation. If a crisis plan is prepared and used adequately, it should help reduce the need for hospitalisation or prevent relapses. Joint crisis plans (advanced agreements between the service user and care providers concerning what will happen when a crisis unfolds) are thought to empower individuals and help them feel more 'in control' (Henderson 2009), and to facilitate detection and treatment of relapse (Sutherby 1999).
Enhanced crisis planning interventions may be a cost‐effective method of reducing relapse and readmissions for people with severe mental illness and may be a more effective alternative to standardised service information. Enhanced crisis planning may have the potential to reduce both compulsion and costs (Flood 2006). Whether crisis planning is cost‐effective must be considered with evidence of the probable cost‐effectiveness of any savings made by reducing admissions.
How the intervention might work
Many people with long‐term severe mental illness rely on community‐based facilities as well as hospital facilities (Sutherby 1999). With this in mind, it is important to find and establish effective methods of crisis planning that can be used to reduce the likelihood of people with severe mental illness from relapsing and being re‐hospitalised, and to provide care in the community that is service‐effective, meets the needs of the individual and recognises choices they make about their care.
Similar to making a lasting power of attorney, a joint or enhanced crisis plan is to be used when people with severe mental illness become so ill that they need others to make decisions about their care. This should pay large attention to patients' wishes and how healthcare professionals and family should play a part in making sure that early signs of illness are detected well in time and further deterioration is prevented (Henderson 2009). Encouraging individuals to develop a crisis plan with the help and support of their family and healthcare professionals could provide an effective method of intervention during a crisis. A joint or enhanced crisis care plan recognises the opinions of those involved in the person's care whilst also meeting the needs of the individual.
A recent Cochrane Review found that home care crisis treatment, combined with an ongoing home care package, is a viable alternative to hospital admission for crisis intervention for people with severe mental illness (Joy 2004). For a crisis plan intervention to be effective, it is important that the patient has a care plan that is up to date and has been thoroughly reviewed by healthcare professionals, family and the individual collectively. It is also crucial that the care plan is tailored specifically to the views and needs of the individual, and is fully understood by the patient. It should designate directive actions to be taken in a crisis by the patient, their carer/family and care co‐ordinator. This could include contact details for all relevant support agencies, including out of hours, as well as clear guidelines for the patient to follow in order to prevent further crises.
Why it is important to do this review
With the emergence of new specialist teams like Crisis Teams, Assertive Outreach Teams, early intervention etc, there is a need to establish good quality evidence that the interventions offered do work and also to argue the case that if evidence is lacking there is a need for more trials in this area. Use of joint crisis plans has been shown to reduce compulsory admissions and treatment in patients with severe mental illness. Theoverall admission rate was less. This is the first structured clinical intervention that seems to reduce compulsory admission and treatment in mental health services (Henderson 2004). There have been no systematic reviews to date which have critically reviewed the available evidence for the effectiveness of crisis planning in preventing readmissions to hospital. There is an urgent need to review this intervention, given that it is beginning to be widely used, at least in the UK and probably elsewhere in the world.
Objectives
The main objective of this review is to evaluate the effectiveness of crisis planning in reducing/preventing relapse and readmission to psychiatric hospital services.
Methods
Criteria for considering studies for this review
Types of studies
We will include all relevant randomised controlled trials. We will not include pseudo‐randomised trials.
Types of participants
We will include people diagnosed with schizophrenia, bipolar disorder, depressive disorder and people with schizophrenia‐like illness symptoms using any criteria. We will include people who are treated with antipsychotic medication for severe mental illness, with any length of illness and in any treatment setting. We will include trials where it is implied that the majority of the participants had a severe mental illness which was likely to be schizophrenia. We will include trials with participants aged between 18 and 65 years. We will not exclude trials due to ethnicity or gender of participants.
Types of interventions
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Crisis planning intervention: any type of crisis planning intervention, used alone or in conjunction with others, where preventing relapse and readmission to hospital services is considered to be the main or active element. This will include interventions which include joint crisis planning, advance crisis planning, adverse crisis planning and any type of crisis intervention used for individuals with enduring severe mental health illness.
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Standard care: any type of standard care that an individual would normally receive as treatment for severe mental health illness to stabilise and maintain symptomology and condition of their mental health. This will include interventions such as medication, community psychiatric nursing input and day hospital. We will exclude any type of in‐patient psychiatric hospital crisis intervention.
For a study to be included, the experimental and comparison interventions have to have had a similar duration.
Types of outcome measures
We have selected outcome measures that provide global estimations of functioning. Outcomes are grouped according to time preceding relapse and readmission to acute mental health services, and according to health care utilisation and cost. We grouped the outcomes into short‐term (up to 12 weeks), medium‐term (13 to 26 weeks) and long‐term (over 26 weeks).
Primary outcomes
1. Relapse of mental illness, readmission to hospital or both.
Secondary outcomes
1. Mental state
1.1 Clinically important change in general mental state
1.2 Average endpoint and change in general mental state score
1.3 Clinically important change in specific symptoms (positive symptom of schizophrenia, negative symptoms of schizophrenia, depression, mania)
1.4 Average endpoint and change in specific symptom score
2. General functioning
2.1 Clinically important change in general functioning
2.2 Average endpoint and change in general functioning score
2.3 Clinically important change in specific aspects of functioning, such as social or life skills
2.4 Average endpoint and change in specific aspects of functioning, such as social or life skills
3. Global state
3.1 Clinically important change in global state (as defined by individual studies)
3.2 Average endpoint and change in global state score
4. Behaviour
4.1 Clinically important change in general behaviour
4.2 Average endpoint and change in general behaviour score
4.3 Clinically important change in specific aspects of behaviour
4.4 Average endpoint and change in specific aspects of behaviour
5. Adverse effects
5.1 Suicide and all causes of mortality
5.2 Clinically important general adverse effects
5.3 Average endpoint and change in general adverse effect score
5.4 Average endpoint and change in clinical specific adverse effects
6. Satisfaction with treatment
6.1 Leaving the study early
6.2 Recipient of care satisfied with treatment
6.3 Recipient of care average endpoint and change in satisfaction score
6.4 Carer satisfied with treatment
6.5 Carer average endpoint and change in satisfaction score
7. Service use
7.1 Number of participants hospitalised
7.2 Mean days in hospital
8. Quality of life
8.1 Clinically important change in quality of life
8.2 Average endpoint and change in quality of life score
8.3 Clinically important change in specific aspects of quality of life
8.4 Average endpoint and change in specific aspects of quality of life
9. Economic outcomes
9.1 Direct costs
9.2 Indirect costs
10. Engagement with services
Search methods for identification of studies
We will apply no language restriction within the limitations of the search.
Electronic searches
We will search the Cochrane Schizophrenia Group Register using the phrase:
[((*Advance* AND * Care* And * Plan*) OR (*Joint* AND *Cris?s* AND * plan*) OR (*Adverse* AND *cris?s* AND * Plan*) OR *advance directives* in Title, Abstract and indexing terms of REFERENCE)) OR (*Crisis plan* or *advance directives* in interventions of STUDY)]
This register is compiled by systematic searches of major databases, handsearches and conference proceedings (see Group Module).
Searching other resources
Reference lists
We will examine the reference lists of all retrieved articles, previous reviews and major text books mentioning severe mental illnesses for additional trials.
Authors of studies
We will identify the authors of significant papers from authorship of trials and review articles found in the search. We will contact them, as well as other experts in the field, to ask for their knowledge of other studies, published or unpublished, relevant to the review.
Data collection and analysis
Selection of studies
RS, JS and SB will independently review the abstracts of the studies identified in the search as being of relevance. Where there are disagreements or the abstract is unclear, we will review the full report and repeat the assessment process. If a dispute still exists we will discuss this with MJ and if there is insufficient information to assess the study, we will contact the main author.
Data extraction and management
1. Extraction
RS, JS and SB will extract data from each study independently. We will resolve any disagreements by discussion. Where disagreements are not resolved, we will discuss with the third author (MJ). If further information is required, we will list the study under the awaiting assessment section whilst we contact the authors of studies. We will discuss and report any disagreement. Data does not need to be published to be included in this review.
2. Management
2.1 Forms
We will extract data onto standard, simple forms.
2.2 Scale‐derived data
We will include continuous data from rating scales only if:
a. the psychometric properties of the measuring instrument have been described in a peer‐reviewed journal (Marshall 2000); and
b. the measuring instrument has not been written or modified by one of the trialists for that particular trial.
Ideally the measuring instrument should either be i. a self report or ii. completed by an independent rater or relative (not the therapist). We realise that this is not often reported clearly; in 'Description of studies' we will note if this was the case or not.
2.3 Endpoint versus change data
There are advantages of both endpoint and change data. Change data can remove a component of between‐person variability from the analysis. On the other hand, calculation of change needs two assessments (baseline and endpoint) which can be difficult in unstable and difficult to measure conditions such as schizophrenia. We have decided to primarily use endpoint data and will only use change data if the former are not available. We will combine endpoint and change data in the analysis as we will use mean differences (MD) rather than standardised mean differences (SMD) throughout (Higgins 2011).
2.4 Skewed data
Continuous data on clinical and social outcomes are often not normally distributed. To avoid the pitfall of applying parametric tests to non‐parametric data, we will aim to apply the following standards to all data before inclusion:
a) standard deviations and means are reported in the paper or obtainable from the authors;
b) when a scale starts from the finite number zero, the standard deviation, when multiplied by two, is less than the mean (as otherwise the mean is unlikely to be an appropriate measure of the centre of the distribution (Altman 1996);
c) if a scale started from a positive value (such as Positive and Negative Syndrome Scale (PANSS) which can have values from 30 to 210), the calculation described above was modified to take the scale starting point into account. In these cases skew is present if 2SD > (S‐S min), where S is the mean score and S min is the minimum score. Endpoint scores on scales often have a finite start and endpoint and these rules can be applied. When continuous data are presented on a scale that includes a possibility of negative values (such as change data), it is difficult to tell whether data are skewed or not.
We will enter skewed data from studies of fewer than 200 participants in additional tables rather than into an analysis. Skewed data pose less of a problem when looking at means if the sample size is large and we will enter these into syntheses.
2.5 Common measure
To facilitate comparison between trials, we intend to convert variables that can be reported in different metrics, such as days in hospital (mean days per year, per week or per month) to a common metric (e.g. mean days per month).
2.6 Conversion of continuous to binary
Where possible, we will make efforts to convert outcome measures to dichotomous data. This can be done by identifying cut‐off points on rating scales and dividing participants accordingly into 'clinically improved' or 'not clinically improved'. It is generally assumed that if there is a 50% reduction in a scale‐derived score, such as the Brief Psychiatric Rating Scale (BPRS, Overall 1962) or the PANSS(Kay 1986), this could be considered as a clinically significant response (Leucht 2005; Leucht 2005a). If data based on these thresholds are not available, we will use the primary cut‐off presented by the original authors.
2.7 Direction of graphs
Where possible, we will enter data in such a way that the area to the left of the line of no effect indicates a favourable outcome for crisis planning. Where keeping to this makes it impossible to avoid outcome titles with clumsy double‐negatives (e.g. 'Not improved') we will report data where the left of the line indicates an unfavourable outcome. We will note this in the relevant graphs.
2.8 'Summary of findings' table
We will use the GRADE approach to interpret findings (Schünemann 2008) and use GRADE Profiler (GRADE PRO) to import data from RevMan 5.1 (Review Manager) to create a 'Summary of findings' table. These tables provide outcome‐specific information concerning the overall quality of evidence from each included study in the comparison, the magnitude of effect of the interventions examined, and the sum of available data on all outcomes we rate as important to patient care and decision making. We have selected the following main outcomes for inclusion in the 'Summary of findings' table:
1. Relapse
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Relapse
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Admission to hospital
2. Mental state
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Clinically important change in mental state
3. General functioning
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Clinically important change in general functioning
4. Quality of life
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Clinically important change in quality of life
5. Satisfaction with treatment
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Leaving the study early
Assessment of risk of bias in included studies
Again RS, JS and SB will work independently to assess risk of bias by using the criteria described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) to assess trial quality. This set of criteria is based on evidence of associations between overestimate of effect and high risk of bias of the article, such as sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting.
If the raters disagree, we will make the final rating by consensus, with the involvement of another member of the review group. Where inadequate details of randomisation and other characteristics of trials are provided, we will contact authors of the studies in order to obtain further information. We will report non‐concurrence in quality assessment, but if disputes arise as to which category a trial is to be allocated to, again we will resolve by discussion.
We will note the level of risk of bias in both the text of the review and in the 'Summary of findings' table.
Measures of treatment effect
1. Dichotomous data
Where possible, we will make efforts to convert outcome measures to dichotomous data. This could be done by identifying cut‐off points on rating scales and dividing participants accordingly into 'clinically improved' or 'not clinically improved'. We will generally assume that if there has been a 50% reduction in a scale‐derived score, such as the Brief Psychiatric Rating Scale (Overall 1962) or the Positive and Negative Syndrome Scale (PANSS) (Kay 1987), this could be considered as a clinically significant response (Leucht 2005). If data based on these thresholds are not available, we will use the primary cut‐off presented by the original authors.
We will calculate the risk ratio (RR) and its 95% confidence interval (CI) based on the random‐effects model, as this takes into account any differences between studies even if there is no statistically significant heterogeneity. It has been shown that RR is more intuitive (Boissel 1999) than odds ratios and that odds ratios tend to be interpreted as RRs by clinicians (Deeks 2000). This misinterpretation then leads to an overestimate of the impression of the effect. When the overall results are significant we will calculate the number needed to treat for an additional beneficial outcome (NNTB) and the number needed to treat for an additional harmful outcome (NNTH) as the inverse of the risk difference.
2. Continuous data
2.1 Summary statistic
For continuous outcomes we will estimate a mean difference (MD) between groups. We will base MDs on the random‐effects model as this takes into account any differences between studies, even if there is no statistically significant heterogeneity. We will not calculate standardised mean difference measures.
2.2 Endpoint versus change data
Since there is no principal statistical reason why endpoint and change data should measure different effects (Higgins 2008), we will use scale endpoint data which are easier to interpret from a clinical point of view. If endpoint data are not available, we will use change data.
2.3 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 aim to apply the following standards to all data before inclusion:
(a) standard deviations and means are reported in the paper or obtainable from the authors;
(b) when a scale starts from the finite number zero, the standard deviation, when multiplied by two, is less than the mean (as otherwise the mean is unlikely to be an appropriate measure of the centre of the distribution (Altman 1996);
(c) if a scale starts from a positive value (such as PANSS which can have values from 30 to 210) the calculation described above was modified to take the scale starting point into account. In these cases skew is present if 2SD > (S‐S min), where S is the mean score and S min is the minimum score. Endpoint scores on scales often have a finite start and endpoint and these rules can be applied. When continuous data are presented on a scale which includes a possibility of negative values (such as change data), it is difficult to tell whether data are skewed or not.
We will enter skewed data from studies of fewer than 200 participants in additional tables rather than into an analysis. Skewed data pose less of a problem when looking at means if the sample size is large and we will enter these into syntheses.
2.4 Data synthesis
When standard errors instead of standard deviations are presented, we will convert the former to standard deviations. If standard deviations are not reported and cannot be calculated from the available data, we will ask the authors to supply the data. In the absence of data from authors, we will use the mean standard deviation from other studies.
Unit of analysis issues
1. Cluster trials
Studies increasingly employ 'cluster‐randomisation' (such as randomisation by clinician or practice) but analysis and pooling of clustered data poses problems. Firstly, authors often fail to account for intraclass correlation in clustered studies, leading to a 'unit of analysis' error (Divine 1992) whereby P values are spuriously low, confidence intervals unduly narrow and statistical significance overestimated. This can lead to a type I error or false positive (Bland 1997; Gulliford 1999). Where clustering is not accounted for in primary studies, we will present the data in a table with a (*) symbol to indicate the presence of a probable unit of analysis error. In subsequent versions of this review we will seek to contact first authors of studies to obtain intraclass correlation coefficients of their clustered data and to adjust for this using accepted methods (Gulliford 1999). Where clustering has been incorporated into the analysis of primary studies, we will also present these data as if from a non cluster‐randomised study, but adjust for the clustering effect.
We will divide binary data as presented in a report by a 'design effect'. We will calculate this using the mean number of participants per cluster (m) and the intraclass correlation coefficient (ICC) [Design effect=1+(m‐1)*ICC] (Donner 2002). If the ICC is not reported, we will assume it to be 0.1 (Ukoumunne 1999). This assumption may be too high and, should this instance occur, we plan to see if taking an ICC of 0.01 will make any substantive difference for the primary outcome. If not we will use 0.01 in preference across outcomes.
If cluster studies have been appropriately analysed, taking into account intraclass correlation coefficients and relevant data documented in the report, we will synthesise these with other studies using the generic inverse variance technique.
2. Cross‐over trials
A major concern of cross‐over trials is the carry‐over effect. It occurs if an effect (e.g. pharmacological, physiological or psychological) of the treatment in the first phase is carried over to the second phase. As a consequence, on entry to the second phase the participants can differ systematically from their initial state despite a wash‐out phase. For the same reason cross‐over trials are not appropriate if the condition of interest is unstable (Elbourne 2002). As both effects are very likely in schizophrenia, we will only use data from the first phase of cross‐over studies.
3. Studies with multiple treatment groups
Where a study involves more than two treatment arms, if relevant, we will present the additional treatment arms in additional relevant comparisons. We will not double‐count data. Where the additional treatment arms are not relevant, we will not reproduce these data.
Dealing with missing data
1. Overall loss of credibility
At some degree of loss of follow‐up, data must lose credibility (Xia 2009). We are forced to make a judgement as to where this is for the trials likely to be included in this review. Should more than 40% of data be unaccounted for we will not reproduce these data or use them within analyses, except for the outcome 'leaving the study early'.
2. Binary
If attrition for a binary outcome is between 0% and 40% and outcomes of these people are described, we will include these data as reported. Where these data are not clearly described, we will present data on a 'once‐randomised‐always‐analyse' basis, assuming an intention‐to‐treat analysis. We will assume those lost to follow‐up all to have a negative outcome, with the exception of the outcome of death. For example, for the outcome of relapse, those who were lost to follow‐up all relapsed. We will undertake a final sensitivity analysis, testing how prone the primary outcomes are to change when 'completed' data only are compared to the intention‐to‐treat analysis using the negative assumption.
3. Continuous
If attrition for a continuous outcome is between 0% and 40% and completer‐only data are reported, we will reproduce these.
4. Intention‐to‐treat (ITT)
We will use intention‐to‐treat (ITT) when available. We anticipate that in some studies, in order to carry out an ITT analysis, the method of last observation carried forward (LOCF) will be employed within the study report. As with all methods of imputation to deal with missing data, LOCF introduces uncertainty about the reliability of the results. Therefore, where LOCF data have been used in the analysis, we will indicate this in the review.
Assessment of heterogeneity
1. Clinical heterogeneity
We will consider all included studies, hoping to use all studies together. Should unforeseen issues be apparent that may add obvious clinical heterogeneity, we will note these issues, consider them in analyses and undertake sensitivity analyses for the primary outcome.
2. Statistical
2.1 Visual inspection
We will visually inspect graphs to investigate the possibility of statistical heterogeneity.
2.2 Employing the I2 statistic
We will investigate heterogeneity between studies by using the I2 statistic (Higgins 2003) and the Chi2 test P value. The former provides an estimate of the percentage of variation in observed results thought unlikely to be due to chance. We will take a value equal to or greater than 50% to indicate heterogeneity and explore reasons for heterogeneity. If the inconsistency is high and clear reasons are found, we will present the data separately.
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 Systematic Reviews of Interventions (Higgins 2003). 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 enter data from all identified and selected trials into a funnel graph (trial effect versus trial size) in an attempt to investigate the likelihood of overt publication bias. We will not undertake a formal test for funnel plot asymmetry
Data synthesis
Where possible we will employ a fixed‐effect model for analyses. We understand that there is no closed argument for preferential use of fixed or random‐effects models. The random‐effects method incorporates an assumption that the different studies are estimating different, yet related, intervention effects. This does seem true to us, however, random‐effects does put added weight onto the smaller of the studies ‐ those trials that are most vulnerable to bias. For this reason we favour using the fixed‐effect model.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analysis
We will undertake no subgroup analyses in this review.
2. Investigation of heterogeneity
If data are clearly heterogeneous we will check that the data are correctly extracted and entered and that we made no unit of analysis errors. We will then visually inspect the graphs to investigate the possibility of statistical heterogeneity. We will supplement this by employing, primarily, the I2 statistic. This provides an estimate of the percentage of inconsistency thought to be due to chance. Where the I2 statistic is greater than or equal to 50% we will interpret this as evidence of high levels of heterogeneity (Higgins 2003). If heterogeneity is found, we will reanalyse the data using a random‐effects model to see if this makes a substantial difference. If it does, we will not add the studies responsible for heterogeneity to the main body of homogeneous trials, but summate and present them separately, and investigate reasons for heterogeneity.
Sensitivity analysis
We plansensitivity analyses for examining the change in the robustness of the results due to including studies with implied randomisation (see Criteria for considering studies for this review), skewed and non‐skewed data, inappropriate comparator doses of drug and different clinical groups ‐ the latter being defined post hoc. If inclusion of studies with implied randomisation makes no substantive difference to the primary outcome we will leave them in the final analyses. For outcomes with both skewed data and non‐skewed data, we will investigate the effect of combining all data together and if no substantive difference is noted then we will leave the potentially skewed data in the analyses. If necessary, we will analyse the effect of including studies with high attrition rates in a sensitivity analysis. We recognise that we may not have considered some clinical causes of heterogeneity that become more obvious after seeing the data. We are fully aware that these are weak investigations and only generate and do not prove hypotheses. We will leave the potential for investigating any omission we may have made in consideration of studies at the stage of writing the protocol.
