Pharmacological interventions for acute and transient psychotic disorder (ATPD)
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To evaluate the effects of pharmacological interventions, including cost‐effectiveness, when compared to placebo or between different pharmacological agents in controlling psychotic symptoms and other relevant outcome measures in people suffering from ATPD or brief psychotic disorder (BPD).
Background
Description of the condition
Acute and transient psychotic disorders (ATPD) first appeared in the 10th revision of the International Classification of Diseases (ICD‐10) (WHO 1992), but classification of acute psychosis has a long historical tradition. Different nomenclatures exist for acute psychosis; a few examples from European countries are cycloid disorders, bouffeé délirante, psychogenic, reactive psychoses, non‐affective acute remitting psychosis, and emotional psychoses (Marneros 2006). The related concept in the Diagnostic and Statistical Manual of Mental Disorders, 4th Edition (DSM‐IV), which has been retained in DSM‐V, is brief psychotic disorder. This review will cover the interventions for both diagnostic categories.
ATPD are distinct forms of psychoses with acute and florid onset, polymorphous symptomatology, and are usually short lived. Many studies report high recurrence rates (Jorgensen 1996; Jorgensen 1997;Singh 2004). Whether ATPD is a subtype of schizophrenia remains controversial. An overview of the epidemiology of ATPD provided by Marneros suggests that several features distinguish ATPD from schizophrenia (Marneros 2003). These include preponderance of females, with female to male ratio of almost 2:1, and an acute or abrupt onset (Marneros 2006; Singh 2004; Varma 1996). The age of onset, which can be throughout adult life, is usually between the 30th and the 50th year, which is different from the age of onset for schizophrenia. There is very brief psychotic period and with very good response to antipsychotic treatment, and the outcome is much favourable compared to that of schizophrenia (Marneros 2006). The premorbid levels of functioning and social interactions are much better in people suffering from ATPD than those reported for people suffering from schizophrenia (Jacob 2013).
ATPD is included as a separate nosological entity in ICD‐10, listed under the heading of F20‐29, which is the group for schizophrenia, schizotypal, and delusional disorders. The key features of ATPD include the following:
-
an acute onset, within two weeks;
-
the presence of typical syndrome of polymorphic and rapidly changing psychotic symptoms; and
-
the presence of associated acute stress.
The characteristic symptoms of ATPD include varied delusions, perplexity, hallucinations, confusion, disorganisation of thought processes, less intense and few negative symptoms, and mood instability (Marneros 2002; Marneros 2003). The disorder has acute onset of psychotic symptoms within two weeks without a prodrome. The symptoms are markedly variable, changing from day to day or even from hour to hour. The duration of symptoms usually does not exceed more than three months, and the course is characterised by recovery within a few weeks, and longer periods of remission.
According to ICD‐10, the ATPD group (F23) consists of six disorders including acute schizophrenia‐like psychotic disorder (Table 1). The first two disorders have polymorphic features, which mean a rapidly changing and variable state. The rest have no polymorphic features, or are characterised by a more stable state (WHO 1992).
| F23.0 | Acute polymorphic psychotic disorder without symptoms of schizophrenia |
| F23.1 | Acute polymorphic psychotic disorder with symptoms of schizophrenia |
| F23.2 | Acute schizophrenia‐like psychotic disorder |
| F23.3 | Other acute predominantly delusional psychotic disorders |
| F23.8 | Other acute and transient psychotic disorders |
| F23.9 | Acute and transient psychotic disorders, unspecified |
DSM‐IV diagnostic category of brief psychotic disorder is a closely related diagnostic concept. The DSM‐IV category of brief psychotic disorder requires the presence of at least one of four symptoms of delusions, hallucinations, disorganised speech, or grossly disorganised or catatonic behaviour for at least one day but less than one month, with eventual return to premorbid functioning. Culturally sanctioned responses to severe stress are excluded. The presence or absence of marked stressor(s) and postpartum onset are specifiers. The draft of DSM–V retains the category with only minor changes. Although the literature regarding the concordance of the two diagnostic concepts is sparse, available evidence suggests that the two are closely related and have significant concordance (Pillmann 2002a; Pillmann 2002b). Another related concept in DSM‐IV is schizophreniform disorder, but this disorder has symptoms duration criteria of more than one month and less than six months, therefore this is substantially different from ATPD and will not be considered in this review.
Description of the intervention
We will investigate pharmacological interventions specifically aimed at ATPD. Such interventions include antipsychotics, anxiolytics, mood stabilisers, and antidepressants. These can be used individually or in combination. We will include trials that compare one pharmacological agent with another or with a placebo.
How the intervention might work
The characteristic symptoms of ATPD include delusions, perplexity, hallucinations, confusion, disorganisation of thought processes, agitation, and mood instability. These symptoms can respond to antipsychotics, mood stabilisers, or benzodiazepines. Several reports suggest that antipsychotics can be effective in a variety of conditions in which delusions, hallucinations, or agitation is present. Excessive dopaminergic activity in the mesolimbic pathway of the brain has been linked to positive psychotic symptoms. Most antipsychotic medications act as dopamine antagonists by preferential blockade of D2 receptors, thereby reducing psychotic symptoms. They are particularly effective in relation to positive symptoms, which are the most common manifestations of ATPD.
As described above, a significant feature of ATPD is mood instability, and the central feature of the disorder is that the symptoms are markedly variable, changing from day to day or even from hour to hour. It is therefore possible that mood stabilisers could be effective in this condition. This is achieved by either potentiation of gamma‐aminobutyric acid (GABA), blocking sodium channels or reducing neurotransmission mediated activation of second messenger system, depending on the type of medication used (Stahl 1998). Mood stabilisers may also help to control agitation and other psychotic symptoms. Similarly, the presence of significant mood symptoms in the form of depression and irritability, usually precipitated by a stressful life event, indicate that an antidepressant or anxiolytic could also be used in the treatment of ATPD. Antidepressants will exert their therapeutic effect by increasing noradrenergic or serotoninergic transmission, or both. Anxiolytics, on the other hand, will enhance the effect of neurotransmission GABA at the GABA a‐receptor, resulting in sedative, hypnotic, and antianxiety action (Stahl 1998).
Why it is important to do this review
The prevalence of ATPD varies from 3.9 to 9.6 per 100,000 population (Castagnini 2008; Singh 2004), and have greater frequency in low and middle income countries, in an analysis of the data from the World Health Organization (WHO) Ten‐Country Study, the prevalence of non‐affective acute remitting psychosis was 10 times more common in low and middle income countries than in high income countries (Susser 1994). In India, 40% to 52% of people presenting with psychosis could not be classified as having schizophrenia or manic depressive psychosis and were considered to be suffering from acute psychosis (Malhotra 2007). The estimates for the burden of ATPD‐caused disease are not available, but these disorders may be responsible for huge burden of disease in view of the high prevalence estimates and younger age of onset. ATPD therefore poses a significant public health problem.
It is not currently known which is the most suitable therapeutic agent for the treatment of ATPD. Major guidelines such as National Institute of Health and Clinical Excellence (NICE) do not even mention acute psychosis as a separate diagnostic category requiring different management. We searched the guidelines using the term acute psychosis, instead of ATPD, as it could be argued that the latter is a controversial diagnostic entity. The word ‘psychosis’ appears in 41‐page guidelines only four times, and only in relation to first episode and substance abuse (NICE 2010). Currently there are no systematic reviews looking at the effectiveness of pharmacological interventions for ATPD.
In the absence of any guidance and evidence, the impression is that the ATPD is mostly treated with antipsychotics. One authority on the subject suggested that "patients with ATPD have a favourable response to drug treatment, but are usually prescribed antipsychotic medications for long periods to prevent recurrences" (Castagnini 2008; Castagnini 2009). This reinforces the impression from clinical practice that ATPD is perhaps being treated as a form of ‘mini schizophrenia’, as if the disorder is an attenuated form of schizophrenia (Farooq 2012).
As mentioned above, characteristic features of ATPD include confusion and mood instability and marked variation in intensity and duration of symptoms and a course characterised by recovery within a few weeks, with longer periods of remission. Considering that most ATPD occur at a young age, and the fact that the definition of ATPD includes ‘transient’ duration, the treatment with atypical antipsychotics may produce serious long‐term effects over a longer period. Castagnini 2013 conducted a record linkage study to the official register of causes of death of all cases aged 15 to 64 years who were listed for the first time in the Danish Psychiatric Register between 1995 and 2008 with an ICD‐10 diagnosis of ‘acute and transient psychotic disorders’ (ATPD). This study showed that ATPD is associated with increased mortality from both natural causes and suicide and is roughly similar to that observed for schizophrenia. It is therefore vitally important that the evidence about the optimum treatment for these psychotic disorders is systematically reviewed and evaluated (Jager 2003).
Objectives
To evaluate the effects of pharmacological interventions, including cost‐effectiveness, when compared to placebo or between different pharmacological agents in controlling psychotic symptoms and other relevant outcome measures in people suffering from ATPD or brief psychotic disorder (BPD).
Methods
Criteria for considering studies for this review
Types of studies
All relevant randomised controlled trials. If a trial is described as 'double blind' but implies randomisation, we will include such trials in a sensitivity analysis (see Sensitivity analysis). If their inclusion does not result in a substantive difference, they will remain in the analyses. If their inclusion does result in important clinically significant but not necessarily statistically significant differences, we will not add the data from these lower‐quality studies to the results of the better trials, but will present such data within a subcategory. We will exclude quasi‐randomised studies, such as those allocating by alternate days of the week. Where participants are given additional treatments with antipsychotic drugs or any other drug, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the pharmacological intervention that is randomised.
Types of participants
Adults (over the age of 18 years) with either a formal diagnosis of ATPD as described by ICD‐10 or suffering from BPD according to DSM‐IV. We will exclude studies in which interventions are evaluated for acute psychotic symptoms or acutely disturbed/aggressive/agitated behaviour on their own or secondary to other psychotic illnesses such as schizophrenia, schizoaffective disorder, substance abuse, organic disorder, mixed affective disorders, or manic phase of bipolar disorder.
Types of interventions
1. Any pharmacological intervention
We will include trials that use a pharmacological intervention for one of the outcome measures described below in the diagnostic category of ATPD. These will primarily include antipsychotics but may also also include other agents such as antidepressants or anxiolytic drugs. The treatment for ATPD may not necessarily include antipsychotics in view of the diverse nature of ATPD symptoms (see How the intervention might work section). We will describe these trials separately, specifying the pharmacological intervention being used.
1.1 Antipsychotics: any individual antipsychotic (any dose, means of administration)
1.2 Antidepressants: any individual antidepressant (any dose, means of administration)
1.3 Anxiolytic drugs: any individual anxiolytic drug (any dose, means of administration)
2. Comparisons
2.1 Placebo (dummy or active)
2.2 Treatment as usual
2.3 Individual pharmacological interventions
2.4 Psychological interventions (as defined by studies)
Types of outcome measures
We will, if possible, divide all outcomes into short term (less than 6 months), medium term (7 to 12 months), and long term (over 1 year).
Primary outcomes
1. Global state
1.1 Any clinically significant response in global state, as defined by each study
1.2 Relapse
1.3 Any improvement, as defined by each study
1.4 Average endpoint/change score on global state scales
2. Social functioning
2.1 Clinically significant response, as defined by each study
2.2 Any improvement, as defined by each study
2.3 Average endpoint/change score on social functioning scales
Secondary outcomes
3. Mental state
3.1 Clinically significant change, as defined by each study
3.2 Any improvement, as defined by each study
3.3 Average total endpoint/change score on mental state scales
3.4 Average endpoint/change scores in negative symptoms
3.5 Average endpoint/change score in positive symptoms
3.6 Average endpoint/change score in affective symptoms
3.7 Use of additional medication (other than anticholinergics)
4. Behaviour
4.1 Clinically significant change, as defined by each study
4.2 Average endpoint/change score on behaviour scales
4.3 Incidence aggression/violence
5. General functioning
5.1 Clinically significant improvement, as defined by each study
5.2 Average endpoint/change score on general functioning scales
6. Compliance with treatment
6.1 Compulsory/voluntary administration of treatment
7. Leaving the study early
7.1 Any reason
7.2 Due to adverse events
7.3 Due to relapse
8. Death
8.1 Due to suicide
8.1 Due to other causes
9. Adverse effects
9.1 At least one adverse effect
9.2 Incidence of serious adverse effect
9.3 Use of additional medication to control side effects
9.4 Any other specific adverse effects
9.5 Average endpoint/change score on adverse effect scales
10. Substance use
10.1 Substance abuse during the course of study
11. Economic outcome
11.1 Direct costs
11.2 Indirect costs
12. Quality of life
12.1 Clinically significant change, as defined by each study
12.2 Average endpoint/change score on quality of life/satisfaction scale
12.3 Any change in employment status, as defined by each study
13. Service use
13.1 As per service/services available
13.2 Hospital admission
13.3 Days in hospital
Summary of findings table
We will use the GRADE approach to interpret findings, Schünemann 2008, and will use GRADE profiler (GRADEPRO) to import data from RevMan 5 (Review Manager) to create 'Summary of findings' tables. 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 rated as important to patient care and decision making. We aim to select the following main [medium term] outcomes for inclusion in the 'Summary of findings' table:
-
Global state: clinically significant response
-
Social functioning
-
Behaviour: incidence of violence/aggressive behaviour
-
Compliance with treatment: compulsory administration of treatment
-
Leaving the study early
-
Adverse effects
-
Quality of life
Search methods for identification of studies
Electronic searches
1. Cochrane Schizophrenia Group Trials Register
The Trials Search Co‐ordinator will search the Cochrane Schizophrenia Group’s Registry of Trials using the following phrase:
(ATPD or ((*Acute or Transient), brief psychotic disorder NEAR3 (Psychosis or Psychoses or Psychotic)) or "Cycloid Disorder?" or "Bouffee Delirante" or "Bouffée Délirante" or "Psychogenic Psycho*" or "Reactive Psycho*" or "Emotional Psycho*"):ti,ab in REFERENCE or (*Acute and Psycho*):sco in STUDY
The Cochrane Schizophrenia Group’s Registry of Trials is compiled by systematic searches of major resources (including MEDLINE, EMBASE, CENTRAL, CINAHL, AMED, BIOSIS, PsycINFO, PubMed, and registries of clinical trials) and their monthly updates, handsearches, grey literature, and conference proceedings (for more detail see Group Module).
Searching other resources
1. Reference searching
We will inspect references of all included studies for further relevant studies.
2. Personal contact
We will contact the first author of each included study for information regarding unpublished trials.
Data collection and analysis
Selection of studies
Review authors SF and MR will independently inspect citations from the searches and identify relevant abstracts. FN will independently inspect a random 20% sample to ensure reliability. Where disputes arise, we will acquire the full report for more detailed scrutiny. SF and MR will obtain full reports of the abstracts meeting the review criteria and inspect. FN will re‐inspect a random 20% of reports to ensure reliable selection. Where it is not possible to resolve disagreement by discussion, we will attempt to contact the authors of the study for clarification.
Data extraction and management
1. Extraction
Review authors SF and MR, will extract data from all included studies. In addition, to ensure reliability, FN will independently extract data from a random sample of these studies comprising 10% of the total. Again, we will discuss any disagreement, document decisions, and, if necessary, contact authors of studies for clarification. SF will help clarify any remaining issues, and we will document these final decisions. We will attempt to extract data presented only in graphs and figures whenever possible, but include only if two review authors independently have the same result. We will attempt to contact authors through an open‐ended request in order to obtain missing information or for clarification whenever necessary. If studies are multi‐centre, where possible, we will extract data relevant to each component centre separately.
2. Management
2.1 Forms
We will extract data onto standard, pre‐designed 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, we will note whether or not this is the case in Description of studies.
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 ATPD. We have decided to primarily use endpoint data, and only use change data if the former are not available. We will combine endpoint and change data in the analysis, as we prefer to use mean differences rather than standardised mean differences 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 aim to apply the following standards to data before inclusion:
a) standard deviations (SDs) and means are reported in the paper or obtainable from the authors;
b) when a scale starts from the finite number zero, the SD, 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 the Positive and Negative Syndrome Scale, which can have values from 30 to 210, Kay 1986), we will modify the calculation described above to take the scale starting point into account. In these cases skew is present if 2 SD > (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 end point, and these rules can be applied. Skewed data pose less of a problem when looking at means if the sample size is large (greater than 200), and we will enter these into the syntheses. We will present skewed endpoint data from studies of less than 200 participants as 'other data' within the Data and analyses section but will not enter these data into statistical analysis.
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 present and enter change data into analyses.
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 (for example 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, Overall 1962, or the Positive and Negative Syndrome Scale, Kay 1986, this could be considered to be a clinically significant response (Leucht 2005a; Leucht 2005b). 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 pharmacological interventions. Where keeping to this makes it impossible to avoid outcome titles with clumsy double‐negatives (for example 'Not un‐improved'), we will report data where the left of the line indicates an unfavourable outcome. We will note this in the relevant graphs.
Assessment of risk of bias in included studies
Again, review authors SF and MR will work independently to assess risk of bias using criteria described in the Cochrane Handbook for Systematic Reviews of Interventions to assess trial quality (Higgins 2011). 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.
In case of disagreement, 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, again, we will resolve by discussion.
We will note the level of risk of bias in both the text of the review and the 'Summary of findings' table.
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. It has been shown that RR is more intuitive than odds ratios, and that odds ratios tend to be interpreted as RR by clinicians (Boissel 1999; Deeks 2000). The number needed to treat for an additional beneficial outcome/harmful outcome (NNTB/H) statistic with its confidence intervals is intuitively attractive to clinicians but is problematic both in its accurate calculation in meta‐analyses and interpretation (Hutton 2009). For binary data presented in the 'Summary of findings' table/s, where possible, we will calculate illustrative comparative risks.
2. Continuous data
For continuous outcomes we will estimate mean difference between groups. We prefer not to calculate effect size measures (standardised mean difference). However, if scales of very considerable similarity are used, we will presume there is a small difference in measurement, and we will calculate effect size and transform the effect back to the units of one or more of the specific instruments.
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 pose 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 causes type I errors (Bland 1997; Gulliford 1999).
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. In subsequent versions of this review, we will seek to contact first authors of studies to obtain intraclass correlation coefficients (ICCs) for their clustered data and to adjust for this by using accepted methods (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.
We have sought statistical advice and have been advised that the binary data as 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 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).
If cluster studies have been appropriately analysed taking into account ICCs and relevant data documented in the report, 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. It occurs if an effect (for example 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 severe mental illness, we will only use data of the first phase of cross‐over studies.
3. Studies with multiple treatment groups
Where a study involves more than two treatment arms, if relevant, we will present the additional treatment arms in comparisons. If data are binary, we will simply add these and combine within the two‐by‐two table. If data are continuous, we will combine data following the formula in Section 7.7.3.8 (Combining groups) of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Where the additional treatment arms are not relevant, we will not use 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 choose that, for any particular outcome, should more than 50% of data be unaccounted for, we will not reproduce these data or use them within analyses. If, however, more than 50% of data in one arm of a study are lost, but the total loss is less than 50%, we will address this within the 'Summary of findings' table/s by down‐rating quality. Finally, we will also downgrade quality within the 'Summary of findings' table/s should loss be 25% to 50% in total.
2. Binary
In the case where attrition for a binary outcome is between 0 and 50% and where these data are not clearly described, we will present data on a 'once‐randomised‐always‐analyse' basis (an intention‐to‐treat analysis). Those leaving the study early are all assumed to have the same rates of negative outcome as those who completed, with the exception of the outcome of death and adverse effects. For these outcomes we will use the rate of those who stay in the study ‐ in that particular arm of the trial ‐ for those who did not. We will undertake a sensitivity analysis testing how prone the primary outcomes are to change when data only from people who complete the study to that point are compared to the intention‐to‐treat analysis using the above assumptions.
3. Continuous
3.1 Attrition
In the case where attrition for a continuous outcome is between 0 and 50%, and data only from people who complete the study to that point are reported, we will reproduce these.
3.2 Standard deviations
If standard deviations (SDs) are not reported, we will first try to obtain the missing values from the authors. If these are not available, where measures of variance for continuous data are missing, but an exact standard error and confidence intervals available for group means, and either 'P' value or 't' value available for differences in mean, we can calculate them according to the rules described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011): When only the standard error (SE) is reported, SDs are calculated by the formula SD = SE * square root (N). Sections 7.7.3 and 16.1.3 of the Cochrane Handbook for Systematic Reviews of Interventions present detailed formula for estimating SDs from P values, t or F values, confidence intervals, ranges, or other statistics (Higgins 2011). If these formula do not apply, we will calculate the SDs according to a validated imputation method that is based on the SDs of the other included studies (Furukawa 2006). Although some of these imputation strategies can introduce error, the alternative would be to exclude a given study’s outcome and thus to lose information. We nevertheless will examine the validity of the imputations in a sensitivity analysis excluding imputed values (Schünemann 2008).
3.3 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 in reasons for leaving the studies early between groups is often the core problem in randomised schizophrenia trials. We will therefore not exclude studies based on the statistical approach used. However, we will preferably use the more sophisticated approaches. for example we will prefer MMRM or multiple imputation to LOCF, and we will only present completer analyses if some kind of intention‐to‐treat data are not available at all. Moreover, we will address this issue in the item "incomplete outcome data" of the 'Risk of bias' tool.
Assessment of heterogeneity
1. Clinical heterogeneity
We will consider all included studies initially, without seeing comparison data, to judge clinical heterogeneity. We will simply inspect all studies for clearly outlying people or situations that we had not predicted would arise. We will discuss such situations or participant groups if they arise.
2. Methodological heterogeneity
We will consider all included studies initially, without seeing comparison data, to judge methodological heterogeneity. We will simply inspect all studies for clearly outlying methods that we had not predicted would arise. We will discuss such methodological outliers if they arise.
3. Statistical heterogeneity
3.1 Visual inspection
We will visually inspect graphs to investigate the possibility of statistical heterogeneity.
3.2 Employing the I2 statistic
We will investigate heterogeneity between studies by considering the I2 method alongside the Chi2 'P' value. The I2 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 i) magnitude and direction of effects and ii) strength of evidence for heterogeneity (for example 'P' value from Chi2 test, or a confidence interval for I2). We will interpret an I2 estimate greater than or equal to around 50% accompanied by a statistically significant Chi2 statistic as evidence of substantial levels of heterogeneity (Section 9.5.2 ‐ Higgins 2011). When we find substantial levels of heterogeneity in the primary outcome, we will explore reasons for heterogeneity (Subgroup analysis and investigation of heterogeneity).
Assessment of reporting biases
1. Protocol versus full study
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results. These are described in Section 10.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will try to locate protocols of included randomised trials. If the protocol is available, we will compare outcomes in the protocol with those 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
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997). These are again described in Chapter 10 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We are aware that funnel plots may be useful in investigating reporting biases but are of limited power to detect small‐study effects. We will not use funnel plots for outcomes where there are 10 or fewer studies, or where all studies are of similar sizes. In other cases, where funnel plots are possible, we will seek statistical advice in their interpretation.
Data synthesis
We understand that there is no closed argument for preference for use of fixed‐effect or random‐effects models. The random‐effects method incorporates an assumption that the different studies are estimating different, yet related, intervention effects. This often seems to be true to us, and the random‐effects model takes into account differences between studies even if there is no statistically significant heterogeneity. However, there is a disadvantage to the random‐effects model. It puts added weight onto small studies, which are often the most biased ones. Depending on the direction of effect, these studies can either inflate or deflate the effect size. We choose to synthesise data using the random‐effects model.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses
1.1 Primary outcomes
We do not plan a subgroup analysis at present but will consider in the future, if required.
1.2 Clinical state, stage, or problem
We propose to undertake this review and provide an overview of the effects of medications for people with acute and transient psychotic disorders. In addition, we will try to report data on subgroups of people in the same clinical state, stage, and with similar problems.
2. Investigation of heterogeneity
We will report if inconsistency is high. First we will investigate whether data has been entered correctly. Second, if data are correct, we will visually inspect the graph and remove studies outside of the company of the rest successively to see if homogeneity is restored. For this review we have decided that should this occur with data contributing to the summary finding of no more than around 10% of the total weighting, we will present these data. If not, we will not pool data, but discuss any issues instead. We know of no supporting research for this 10% cut‐off but are investigating use of prediction intervals as an alternative to this unsatisfactory state.
When unanticipated clinical or methodological heterogeneity is obvious, we will simply state hypotheses regarding this for future reviews or versions of this review. We do not anticipate undertaking analyses relating to this.
Sensitivity analysis
1. Implication of randomisation
We aim to include trials in a sensitivity analysis if they are described in some way as to imply randomisation. For the primary outcomes we will include these studies, and if there is no substantive difference when the implied randomised studies are added to those with better description of randomisation, then we will use all data from these studies.
2. Assumptions for lost binary data
Where we must make assumptions regarding participants lost to follow‐up (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumption/s and when we use data only from participants who have completed the study to that point. If there is a substantial difference, we will report results and discuss them but will continue to employ our assumption.
Where we must make assumptions regarding missing SDs data (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumption/s and when we use data only from people who have completed the study to that point. We will conduct a sensitivity analysis, testing how prone results are to change when completer‐only data only are compared to the imputed data using the above assumption. If there is a substantial difference, we will report results and discuss them but will continue to employ our assumption.
3. Risk of bias
We will analyse the effects of excluding trials that we judge to be at high risk of bias across one or more of the domains of randomisation (implied as randomised with no further details available) allocation concealment, blinding, and outcome reporting for the meta‐analysis of the primary outcome. If the exclusion of trials at high risk of bias does not substantially alter the direction of effect or the precision of the effect estimates, then we will include data from these trials in the analysis.
4. Imputed values
We will also undertake a sensitivity analysis to assess the effects of including data from trials where we used imputed values for intraclass correlation coefficient in calculating the design effect in cluster randomised trials.
If we note substantial differences in the direction or precision of effect estimates in any of the sensitivity analyses listed above, we will not pool data from the excluded trials with the other trials contributing to the outcome, but will present them separately.
5. Fixed effect and random effects
We will synthesise all data using a random‐effects model; however, we will also synthesise data for the primary outcome using a fixed‐effect model in order to evaluate whether this alters the significance of the results.
| F23.0 | Acute polymorphic psychotic disorder without symptoms of schizophrenia |
| F23.1 | Acute polymorphic psychotic disorder with symptoms of schizophrenia |
| F23.2 | Acute schizophrenia‐like psychotic disorder |
| F23.3 | Other acute predominantly delusional psychotic disorders |
| F23.8 | Other acute and transient psychotic disorders |
| F23.9 | Acute and transient psychotic disorders, unspecified |
