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Cochrane Database of Systematic Reviews Protocol - Intervention

Postdischarge interventions for depression

Authors' declarations of interest

Version published: 17 March 2015 Version history

https://doi.org/10.1002/14651858.CD011591
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Abstract

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

To assess the benefits and harms of non‐residential postdischarge interventions for patients with major depressive disorder vs. no intervention or treatment as usual (TAU) in an adult population. More specifically, to assess different service levels of postdischarge interventions on depressive symptoms, suicidal behaviour, quality of life and other beneficial and harmful outcomes.

Background

Description of the condition

Major depressive disorder is a global cause of both short and long term disability. In 2010, it was ranked the second most common cause of years lived with disability (Vos 2012). According to the Diagnostic and Statistical Manual of Mental Disorders, fifth edition (DSM 5) (APA 2013), the diagnosis of major depressive disorder is possible based on a single depressive episode. A depressive episode requires a depressed mood, or loss of interest or pleasure in life activities, or both, for at least two weeks, together with numerous behavioural, cognitive and emotional changes (such as insomnia, loss of energy, feelings of guilt or a diminished ability to concentrate, or both) that cause significant impairment in social, work or other important areas of functioning.

The lifetime prevalence of major depressive disorder is reported to be 16% (Kessler 2003). People who recover from a depressive episode have a high risk of relapse (Kessing 2004; Solomon 2000) and 20% of patients with depression develop a chronic condition (Spijker 2002). Patients with mood disorders also have a higher than average lifetime risk of a suicide attempt (Kessler 1999; Nock 2008), with the risk of suicide being higher in particular during the first three to four weeks after psychiatric admission (Ramana 2003; Windfuhr 2011). Approximately half the number of suicides within one month after hospital discharge occur before the first psychiatric follow‐up consultation (Windfuhr 2011).

Description of the intervention

In some mental health care systems, community care or other non‐residential solutions are offered in the acute phase of major depressive disorder (Horvitz‐Lennon 2001). However, for the most severely depressed (and often suicidal) patients first line of treatment in many mental health care systems is still psychiatric admission (Lin 2011). Psychiatric admission is then usually supplemented by varying amounts of subsequent non‐residential aftercare (Horvitz‐Lennon 2001). However, there is considerable heterogeneity in how the postdischarge intervention is organised (Horvitz‐Lennon 2001; Kallert 2004; Glick 1986), resulting in significantly differing services. The services differ on presumably crucial aspects, such as time of onset (Comtois 2011; Hansen 2012) and intensity of the aftercare (Glick 1986), and a uniform definition of non‐residential care is lacking (Horvitz‐Lennon 2001).

In general terms different postdischarge interventions can be described as a spectrum. At one end of the spectrum, a highly structured aftercare program can be described. Services like these are often referred to as day hospitals or partial hospitalisation (Larivière 2010; Glick 1986; Lin 2011), and are often intensive in structure with an early onset after discharge. A prototype could be a non‐residential program with pre‐defined length of duration, number of contacts (e.g., three contacts per week) and form (e.g., individual or group therapy). At the other end of the spectrum a simple out‐patient aftercare can be described, often a more informal and less intensive service (Glick 1986; Hansen 2012). A prototype could be follow‐up by a single professional (a psychiatrist/physician) with an individually adapted frequency, often planned ad hoc, according to each patient's condition. Both types are in contrast to discharge from hospital with no further planned psychiatric treatment.

How the intervention might work

The first period after discharge is known to be a high‐risk period, with an increased suicide risk (as described above) (Windfuhr 2011), and patients with major depressive disorder often are discharged while still symptomatic (Hansen 2012; Lin 2011). Consequently the postdischarge intervention could be crucial to ensure continued recovery and to prevent future relapses. If, on the other hand, the aftercare intervention is insufficient, there is ― according to the above arguments ― a risk of discontinuation of treatment, relapse of symptoms and, at worst case, suicide.

The cognitive impairment (Airaksinen 2004; Rose 2006; Snyder 2013), lack of energy (van Noorden 2012) and low self‐esteem (Korrelboom 2012) often seen in people with major depressive disorder can consequently lead to difficulties with participating, planning, remembering guidance, adhering to medication and carrying out advice or behavioural changes. We propose that these are all challenges the psychiatric aftercare must aim to meet to ensure a satisfying treatment result.

postdischarge care can organisationally mean many things (as discussed above). Therefore, it is necessary to discuss the organisation of the aftercare when considering how the intervention might work. An early onset, pre‐scheduled and intensive aftercare makes intuitive clinical sense, considering the above arguments on residual symptoms and suicidality postdischarge. However, the organisation of postdischarge interventions is poorly investigated (Glick 1986; Hansen 2012). Also, the existing body of knowledge shows ambiguous results as some trials suggest that an early onset and intensive approach is beneficiary for non‐psychotic patients with reductions in suicidal ideation, symptom distress, increased hope and self‐esteem, and ameliorated social participation (Comtois 2011; Dick 1991; Larivière 2010; Tyrer 1987), whereas others have failed to prove any difference between an intensive and a less intensive aftercare (Glick 1986). All in all, it has been suggested, but not sufficiently investigated, that deficiencies in aftercare could be the foundation of persisting symptoms and disability in major depressive disorder (Ramana 2003). In accordance with this, we hypothesise that postdischarge interventions can enhance treatment results and affect the long term treatment outcome, with the organisation of the aftercare as a potentially important enhancing factor.

Why it is important to do this review

Over the past decades, there has been a tendency towards reducing the number of psychiatric beds (Malone 2007; Shek 2009), Due to an increased pressure on remaining beds, shortened admission times probably place high demands on the postdischarge interventions as a supplement to inpatient care, as patients are discharged while still symptomatic (as stated above). Therefore, it is important to clarify whether postdischarge interventions can alter the recovery rate of major depressive disorder, increase the patients' quality of life or reduce the number of suicides in the high risk postdischarge period, or both.

To our knowledge, studies of psychiatric postdischarge interventions have mainly focused on participants with psychotic disorders, as opposed to major depressive disorder (Ramana 2003). Furthermore, both clinical organisation and research have predominantly focused on establishing and evaluating partial hospitalisation and crisis resolution teams, to replace psychiatric admission (Horvitz‐Lennon 2001). Consequently, we lack knowledge on both the benefits and harms of post discharge aftercare and the optimal organisation of postdischarge interventions for patients with major depressive disorder (Crawford 2007; Hansen 2012; Ramana 2003).

This Cochrane review will primarily summarise the benefits and harms of postdischarge aftercare and, secondly, explore the optimal organisation of postdischarge interventions for major depressive disorder. This information is highly relevant in order to aid professionals and policy makers in developing efficient, effective and safe mental‐health‐care services in the future. Currently, even the most modest standards for postdischarge interventions are frequently not met (Pfeiffer 2011; Ramana 2003).

Objectives

To assess the benefits and harms of non‐residential postdischarge interventions for patients with major depressive disorder vs. no intervention or treatment as usual (TAU) in an adult population. More specifically, to assess different service levels of postdischarge interventions on depressive symptoms, suicidal behaviour, quality of life and other beneficial and harmful outcomes.

Methods

Criteria for considering studies for this review

Types of studies

We will include all relevant clinical randomised controlled trials (RCTs) and cluster RCTs. Trials will be included irrespective of language, publication type, publication year or publication status. We will exclude crossover trials as they are unsuitable for this type of intervention.

Types of participants

Included participants
Participant characteristics

Adult participants, aged 18 years or older, who has provided informed consent to participate in the trial. We will only include participants admitted to a psychiatric care facility due to major depressive disorder (diagnosed as stated below).

Diagnosis

Participants diagnosed with major depressive disorder, as defined in DSM‐IV: Major depressive Episode or Major Depressive Disorder with any specifier, or as defined in ICD‐10: Depressive Episode (F32.x) or Recurrent Depression (F33.x) with any specifier. Only participants diagnosed using standardised diagnostic criteria corresponding to either DSM‐IV (APA 1994)/DSM‐IV‐TR (APA 2000)/DSM‐5(APA 2013) or ICD10 (WHO 1993) (or earlier versions of these diagnostic systems) are eligible for inclusion, diagnosed with —for example— the following diagnostic schedules: Present State Examination (PSE)/Schedules for Clinical Assessment in Neuropsychiatry (SCAN) (Wing 2007) or Structured Clinical Interview for DSM‐IV® Axis I Disorders (SCID‐I) (First 1997).

Co‐morbidities

We will include participants with co‐morbid non‐psychotic mental health disorders and somatic illness.

Setting

There will be no restrictions to the setting of the postdischarge intervention, as long as it is part of the mental healthcare system.

Excluded participants
Participant characteristics

We will exclude participants who have not provided informed consent to participate in the trial.

Diagnosis

We will exclude participants diagnosed with schizophrenia or other psychotic disorder (including mania with psychotic symptoms, exempting depression with psychotic symptoms), dependency problem or an organic brain disorder (such as, brain cancer, epilepsy) or cognitive disabilities (such as developmental disorders, mental retardation or dementia) or both, according to standardised diagnostic criteria (as stated above).

Co‐morbidities

We will exclude participants with a co‐morbid psychotic disorder, according to standardised diagnostic criteria (as stated above).

Types of interventions

Experimental interventions

Any postdischarge intervention where:

  1. The intervention is defined by trialists as a postdischarge intervention (using any corresponding term, such as aftercare/follow‐up), and

  2. The intervention is conducted by mental healthcare professionals (i.e. psychiatrists, medical doctors, psychotherapists, psychologists or nurses), and

  3. The intervention includes at least one 'face‐to‐face' contact, and

  4. The intervention is commenced within the first month after discharge.

The organisation of the intervention can vary in two ways:

  1. The postdischarge intervention can have a late onset (here defined as later than one week after discharge) or an early onset (here defined as first appointment within one week) (Comtois 2011);

  2. The postdischarge intervention can have a low intensity (here defined as once or less than once weekly 'face‐to‐face' contact with a mental healthcare professional) or a high intensity (here defined as more than one weekly 'face‐to‐face' contact) (Glick 1986).

We will investigate these aspects further in the Subgroup analysis and investigation of heterogeneity section.

Adjunctive therapy:

In addition to the postdischarge intervention, we will allow adjunctive therapy (e.g., medication, physical training, relaxation) as long as it is delivered equally in both intervention and control groups. Adjunctive therapy is defined as within the aftercare service if it is organised by the same service provider as the intervention.

Comparator interventions

  • No intervention; or

  • Treatment as usual (TAU), defined according to the trialists.

To clarify, a trial can for example include an experimental intervention compared with TAU, or an experimental intervention compared with 'no intervention'. Inclusion follows the definition of the trialists.

The definition of TAU as 'according to the trialists' is chosen to ensure inclusion of all potentially relevant trials, as the purpose of this Cochrane review is to compare any kind of postdischarge intervention (low or high intensity) with nothing or TAU. However, this broad definition of TAU might result in similar interventions being categorised as experimental in one study and as TAU in another. Therefore, we will describe in the review what was actually received by participants receiving TAU in each trial. We also plan to undertake sensitivity analyses on the basis of different levels of support offered as part of TAU.

Types of outcome measures

Primary outcomes
1. Depressive symptoms

Symptom level, measured as a continuous outcome, defined as the difference between the mean values from the two groups, using the 17‐item Hamilton Depression Rating Scale (HDRS) (Hamilton 1960). We will also accept any other form of the HDRS, Becks Depression Inventory (BDI) (Beck 1961) or Montgomery‐Asberg Depression Rating Scale (MADRS) (Montgomery 1979). In this case we will analyse the outcome as the difference between the mean values from the two groups, using standardised mean difference (SMD). If all studies include HDRS‐17 scores, then we will use the raw endpoint score. If some studies use other measures, then a SMD metric will also be used for all, including the HDRS‐17.

2. Suicides, suicide attempts and self‐harm

  • Suicides, measured as a dichotomous outcome ('suicide' vs. 'no suicide');

  • Suicide attempts, measured as a dichotomous outcome ('suicide attempt' vs. 'no suicide attempt');

  • Episodes of self‐harm, measured as a dichotomous outcome ('episodes of self‐harm' vs. 'no episodes of self‐harm').

Secondary outcomes
3. Quality of life

Assessed on any continuous outcome scale. We will report results from any validated scale separately and then assess the results using SMD.

4. Treatment efficacy

Relapse of depressive symptoms at end of intervention, as defined by trialists and measured as a dichotomous outcome.

5. Serious adverse events

We will define serious adverse events as medical events that are life threatening, result in death, disability or significant loss of function, which cause hospital admission or prolonged hospitalisation, relapse of symptoms (ICH‐GCP 1997) or discontinuation of treatment, measured as a dichotomous outcome.

6. Social adjustment or social functioning

Measured with Global Assessment of Functioning (GAF) (APA 2000) or otherwise as defined by trialists (e.g., 'time to return to work' or 'time to resumption of normal activities').

7. Service use

  • Bed‐days since incidence discharge, measured as a count or rate;

  • Emergency ward contacts since incidence discharge, measured as a count or rate.

8. Cost‐effectiveness

The cost‐effectiveness of the type of organisation studied, measured as defined by trialists.

Hierarchy of outcome measures

If several outcome measures are available for each outcome, we will use results from the HDRS. If results from HDRS is not available, we will use results from BDI. However, if results from neither of the two are available, we will use results from the MADRS.

Timing of outcome assessment

We will assess all outcomes at the end of intervention (as defined by the trialists) and at longest follow‐up (exception: 'treatment efficacy' will only be measured at end of intervention). We will consider the 'end of intervention' as the primary time point.

Search methods for identification of studies

Cochrane Depression, Anxiety and Neurosis Review Group's Specialized Register (CCDANCTR)

The Cochrane Depression, Anxiety and Neurosis Group (CCDAN) maintain two clinical trials registers at their editorial base in Bristol, UK: a references register and a studies based register. The CCDANCTR‐References Register contains over 37,000 reports of RCTs in depression, anxiety and neurosis. Approximately 65% of these references have been tagged to individual coded trials. The coded trials are held in the CCDANCTR‐Studies Register and records are linked between the two registers through the use of unique study ID tags. Coding of trials is based on the EU‐Psi coding manual, using a controlled vocabulary (please contact the CCDAN Trials Search Coordinator for further details). Reports of trials for inclusion in the group's registers are collated from routine (weekly) generic searches of MEDLINE (1950‐), EMBASE (1974‐) and PsycINFO (1967‐); quarterly searches of the Cochrane Central Register of Controlled Trials (CENTRAL) and review specific searches of additional databases. Reports of trials are also sourced from international trials registers c/o the World Health Organization (WHO) trials portal (the International Clinical Trials Registry Platform (ICTRP)), pharmaceutical companies, the handsearching of key journals, conference proceedings and other (non‐Cochrane) systematic reviews and meta‐analyses.

Details of CCDAN's generic search strategies (used to identify RCTs) can be found on the CCDAN website (http://ccdan.cochrane.org/).

Electronic searches

1. We will search the CCDANCTR‐Studies and References Register using the following terms:
Title/Abstract/Keywords= (depress* or “affective disorder*” or “mood disorder*”)

AND

Free‐text =(aftercare or 'after care' or after‐care or ((hospital* or inpatient or in‐patient* or patient* or psychiatric or community) NEAR3 discharge*) or postdischarge* or “post discharge*” or post‐discharge* or posthospital* or “post hospital*” or post‐hospital* or ((followup or "follow up" of follow‐up) NEXT (care or service)) or ((posttreatment or "post treatment" or post‐treatment or outpatient or "out patient" or out‐patient) NEXT (followup or "follow up" or follow‐up)) or ((postacute or "post acute" or post‐acute) NEXT care))

2. We will conduct complementary searches on the following bibliographic databases using relevant subject headings (controlled vocabularies) and search syntax, appropriate to each resource: LILACS and CINAHL (see Appendix 1 for CINAHL search strategy).

There will be no restrictions on date, language or publication status applied to the searches.

3. We will search international trial registries via the WHO's trials portal (ICTRP) and ClinicalTrials.gov to identify unpublished or ongoing studies.

Searching other resources

Reference lists

We will check the reference lists of all included studies and relevant systematic reviews to identify additional studies missed from the original electronic searches (e.g., unpublished or in‐press citations). Also, we will conduct a cited reference search on the Web of Science.

Grey literature

We will search sources of grey literature, including dissertations and theses, clinical guidelines and reports from regulatory agencies, where appropriate:

Handsearching

Relevant conference proceedings (titles not already indexed in EMBASE or PsycINFO, or already handsearched within The Cochrane Collaboration), will be handsearched where appropriate.

Correspondence

We will contact the trialists of included trials if necessary to request additional trial data.

Data collection and analysis

Selection of studies

Two review authors (SA and MN) will independently assess eligibility of trials. These two review authors will examine the titles of all publications obtained through the search strategy and will remove obviously irrelevant reports. SA and MN will obtain and inspect the full text articles of potentially relevant reports. Any conflicts of opinion regarding eligibility of trials will be discussed with a third review author (JJ), having retrieved the full paper and consulted the trial authors if necessary, until consensus is reached. We will consult external subject or methodological experts if necessary.

Data extraction and management

1. Extraction

Two review authors (SA and MN) will independently extract data from all included trials (including data presented only in graphs and figures whenever possible), according to a pre‐designed data collection form (see Appendix 2). SA and MN will discuss any disagreements with a third review author (JJ) and, where necessary, will contact the trial authors for clarification. We will document all decisions.

We will extract data presented only in graphs and figures whenever possible. In order to obtain any missing information, we will contact trial authors whenever necessary. We will link multiple reports of the same study together.

2. Management
2.1 Forms

Data relating to source, eligibility, methods (including concerns about bias), participants, interventions, outcomes, results and conclusions will be abstracted from the original reports into a pre‐formed data collection form, according to standards suggested in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). The data will then be inputted into Review Manager 5 software (RevMan 2014).

2.2 Data

2.2.1 Scale‐derived data

Any scales of measure used for evaluation should be described in a peer‐reviewed journal (Marshall 2000) and be widely recognised for use in the target population. Furthermore, the scale should not be modified for use in the particular trial. If any of the above is not fulfilled, we will not include the results in a meta‐analysis, but will describe them in the review text.

2.2.2 Skewed data

Continuous data on outcomes often do not have a normal distribution. Therefore, we will apply the following standards to all data before inclusion:

  1. Standard deviations (SDs) and means should be reported in the paper or obtainable from the trial authors;

  2. When a scale starts from zero, the SD, when multiplied by two, must be less than the mean (otherwise the mean is unlikely to be an appropriate measure of the centre of the distribution (Altman 1996));

  3. If a scale starts from a positive value, we will modify the calculation described above to take the scales starting point into account.

In these cases, skew is present if 2SD > (S‐Smin), where S is the mean score and Smin is the minimum score. These rules can be applied on endpoint data, as scales often have a finite start and end point. 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. When data are skewed, we will contact a knowledgeable statistician for further advice.

Main comparisons

We plan to make the following main comparison:

  1. A postdischarge intervention vs. no intervention or TAU.

Assessment of risk of bias in included studies

Two review authors (MN and SA) will independently assess the risk of bias for each included trial by the domains listed in Appendix 3. We have chosen the domains described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), supplemented by the domain 'financial interest bias'.

If there is disagreement regarding assessment of risk of bias, the two review authors will reach a final decision by discussion, if necessary by involving a third review author (JJ). Where inadequate details are provided (of randomisation and other characteristics), we will contact trial authors to obtain further information. We will report non‐concurrence in 'Risk of bias' assessment.

For further details please refer to Appendix 3.

Measures of treatment effect

Whenever possible, we will convert the data reported in diverse formats into a single format, suitable for meta‐analysis.

Dichotomous data

As recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), we will calculate a risk ratio (RR) and its 95% confidence interval (CI) for dichotomous data, as the concept of risk is considered more familiar to the expected reader of this review, than the concept of odds. For statistically significant results, we will calculate the number needed to treat for an additional beneficial outcome (NNTB) or the number needed for an additional harmful outcome (NNTH) and 95% CIs. We will analyse data classified in more than two categories and data from ordinal measurement scales as dichotomous data when there are few categories or the scale is short.

Continuous data

Where trials have used similar scales and outcome measures for comparison, we will pool data by calculating the mean difference (MD) and 95% CIs.

Where considerably different scales or measures are used to assess the same outcome, we will adjust the values for any differences in the direction of the scales used. We will also pool data with standardised mean difference (SMD) and calculate 95% CIs. If scales of very considerable similarity are used, we will calculate SMD and transform the effect back to the units of one of the specific instruments used.

We will analyse data classified in more than two categories and data from ordinal measurement scales as continuous data when there are many categories or the scale is long.

Endpoint vs. change data

Change data requires two assessments (baseline and endpoint), as well as an assessment of the SD of the change value, both of which may not be available for all participants, or from all trials, or both. We will therefore primarily use endpoint data. We will only use change data if endpoint data are not available. Endpoint and change data can be combined for analysis.

Counts and rates

If a counted event happens to a participant more than once during a study, it is often accounted for as a rate. We will summarise this as a rate ratio in meta‐analysis.  

Unit of analysis issues

Cluster‐RCTs

If data from cluster‐RCTs are interpreted as though the group had been the individual participants, a 'unit of analysis' error occurs (Divine 1992). We will note if clustering is unaccounted for and we will assume that there is a 'unit of analysis' error.

For dichotomous data presented in the report of a cluster‐RCT, both the number of participants and the number experiencing the event should be divided by a 'design effect'. This design effect is calculated using the mean number of participants per cluster (m) and the intra‐class correlation coefficient (ICC) [Design effect =1+ (m‐1) * ICC] (Donner 2002).

Where continuous data are presented in the report of a cluster‐RCT, only the sample size should be divided by the design effect, whereas means and SDs remain unchanged.

Where we assume that there is a 'unit of analysis' error, we will attempt to contact the trial authors to obtain an ICC value for their clustered data (Gulliford 1999). If the ICC is unaccounted for, we will assume the value to be 0.1 (Ukoumunne 1999).

Where clustering has been incorporated into the analysis of trials, we will present these data as if from a non‐cluster‐RCT, but will adjust for the clustering effect by use of the ICC value. If ICC values are taken into account and relevant data is documented in the study report, synthesis with other trials will be possible.

Trials with multiple treatment groups

If a trial involves more than two treatment arms and the arms have intervention groups in common, we will take measures not to 'double‐count' the participants. We will make multiple pair‐wise comparisons between intervention groups. Where the additional treatment arms are irrelevant, we will not use the data.

Dealing with missing data

In our primary analyses we will use results from trials where less than 5 % of the participants are lost to follow‐up, or appropriate methods (e.g., multiple imputation) have been used to handle missing data. If trial results are based on the per protocol population, we will assume that participants lost to follow‐up have not obtained remission. Otherwise, missing dichotomous and continuous outcomes will not be imputed in our analysis. We will assess the potential impact of the missing data via best‐case and worst‐case scenarios.

Assessment of heterogeneity

We expect there will be clinical heterogeneity as the interventions included are likely to differ with regards to numbers of contacts and types of services provided. This can influence the observed (and true) effectiveness of the intervention. Therefore, we will categorise the numbers of contacts and types of services provided. We will then analyse the categories and present them separately. We will investigate both methodological and statistical heterogeneity further, as well as both the I2 statistic and the Chi2 test P value (Higgins 2011).

We will interpret the I2 statistic as recommended in Higgins 2011:

  • 0% to 40%: might not be important;

  • 30% to 60%: may represent moderate heterogeneity;

  • 50% to 90%: may represent substantial heterogeneity;

  • 75% to 100%: considerable heterogeneity.

We will interpret an I2 estimate ≥ 50% and a statistically significant Chi2 statistic as evidence of a substantial problem with heterogeneity (Higgins 2011). However, if the I2 value is below 50% and the direction and magnitude of treatment effects suggests important heterogeneity, investigation of the sources may also be necessary. If any of the above is the case, we will explore the reasons for heterogeneity.

If we consider the data from the included trials to be too heterogeneous and, in particular, if there is inconsistency in the direction of effect, we will not perform meta‐analysis and instead we will present data separately.

Assessment of reporting biases

The impact of reporting biases will be minimised by a thorough literature search, as described in the Search methods for identification of studies section. We will also try to identify outcome reporting bias in included trials by recording both trial outcomes planned in the protocol and outcomes actually reported. Where discrepancies are found, we will attempt to obtain available data on missing outcomes from the trial authors.

Where ten or more trials meet our inclusion criteria, we will construct funnel plots for outcomes to establish the potential influence of reporting biases and small study effects. We will not use funnel plots for outcomes where there are fewer than ten trials or where all trials are of similar size. Where funnel plots are possible, we will seek statistical advice to interpret them.

Data synthesis

There is no closed argument for preference of fixed‐effect or random‐effects models. The random‐effects model puts added weight onto small trials, which often are the most biased ones. Depending on the direction of effect, these trials can either inflate or deflate the effect size. Due to the likely diversity of interventions and the likely heterogeneity amongst primary studies, we will analyse data using the random‐effects model (DerSimonian 1986) and then examine potential differences with the fixed‐effect model (Demets 1987) as part of a sensitivity analysis.

Subgroup analysis and investigation of heterogeneity

Subgroup analyses

If possible we will perform the following subgroup analyses: 

  1. Trials with a high intensity experimental intervention vs. trials with a low intensity experimental intervention;

  2. Trials with an early onset experimental intervention vs. trials with a late onset experimental intervention;

  3. Trials with no intervention as control intervention vs. TAU as control intervention;

  4. Trials with short follow‐up (defined as follow‐up shorter than mean follow‐up) vs. trials with long follow‐up (defined as follow‐up longer than mean follow‐up);

  5. Adult participants vs. elderly participants (defined as such by trialists).

We will only perform the subgroup analyses on primary outcomes.

Investigation of heterogeneity

We will report if inconsistency is high. Firstly, we will investigate whether data has been entered correctly. If data are correctly entered, we will inspect the graph visually and successively remove trials that are placed outside of the company of the rest on the graph, to see if homogeneity is restored. When unanticipated clinical or methodological heterogeneity are obvious, we will state a hypotheses regarding these findings and not undertake analyses relating to these data.

Sensitivity analysis

Binary outcomes

We will perform the following sensitivity analyses:

1a. 'Best‐worst‐case' scenario: we will assume that all participants lost to follow‐up in the experimental group have survived, had no suicide attempt, had no adverse event and have obtained remission; and all those with missing outcomes in the control group did not survive, attempted suicide, had a adverse event and have obtained 'no remission';
1b. 'Worst‐best‐case' scenario: we will assume that all participants lost to follow‐up in the experimental group have not survived, had a suicide attempt, had a adverse event and have obtained 'no remission'; and that all those lost to follow‐up in the control group survived, had no suicide attempt, had no adverse event and have obtained remission.

We will present results from both scenarios 1a and 1b.

2a. 'High level of TAU': removing all participants receiving TAU with a high level of support ‐ defined as more than one contact per week;
2b. 'Low level of TAU': removing all participants receiving TAU with a low level of support ‐ defined as one, or less than one, contact per week;

3. Examine potential differences when using the fixed‐effect model (Demets 1987) compared to the random‐effects model (DerSimonian 1986).

Cluster‐RCTs

Where we have to assume the ICC value, we will compare our assumption findings with findings from trials with reported ICCs.

Trial sequential analysis

For binary and continuous outcome measures, we will perform trial sequential analyses of results from the RCTs (Brok 2008; Wetterslev 2008) in order to calculate the desired quantity of information and the cumulative Z‐curve's breach of relevant trial sequential monitoring boundaries. For binary outcomes, we will estimate the required information size based on the proportion of patients with an outcome in the control group, a relative risk reduction of 20%, an alpha of 5%, a beta of 20%, and heterogeneity of 30% and 60%. For continuous outcomes, we will estimate the required information size based on a MD of three points on the HDRS, the SD observed in the control group of trials with low risk of bias, an alpha of 5%, a beta of 20%, and heterogeneity of 30% and 60% (Thorlund 2011). We will use the eight‐step procedure proposed by Jakobsen 2014 to assess whether the thresholds for significance are crossed or not.

'Summary of findings' tables

We will produce 'Summary of findings' tables in order to provide outcome‐specific information concerning the overall risk of bias of each included study, the magnitude of effect of the interventions examined and the sum of available data on seven of the clinically most important outcomes, namely: 

  1. Symptom level;

  2. Suicides;

  3. Suicide attempts;

  4. Quality of life;

  5. Treatment efficacy;

  6. Social adjustment or social functioning;

  7. Service use.

We will use the GRADE approach to interpret findings (Atkins 2004), and the GRADEpro tool (GRADEpro).