Network meta-analysis of randomised trials of pharmacological, psychotherapeutic, exercise and collaborative care interventions for depressive symptoms in patients with coronary artery disease: hybrid systematic review of systematic reviews protocol

As several systematic reviews have already been published in this area (e.g. [6‐11]), we will conduct a hybrid overview of reviews [31] and systematic review methodology. We will find and extract RCTs and their associated data using the content of these reviews and the original RCT papers (including RCTs which are listed as not having being included in the final published reviews (e.g. [6, 9]). This will be supplemented by an updated search for RCTs, as is commonly done in other areas [41‐43]. More precisely, we will search, from inception, the Cochrane Library (CENTRAL), CINAHL, MEDLINE/PubMed, EMBASE, MEDLINE In-Process, Epistemonikos and PsycInfo. Then, we will conduct a search of MEDLINE/PubMed and the Cochrane Library for recent RCTs published in the last 5 years (i.e. from 1st January 2014). We will also supplement this with a search of clinical trials registries: World Health Organization International Clinical Trials Registry Platform (WHO ICTRP) and clinicaltrials.​gov, using similar terms. The reference lists for included RCTs will also be searched. Unpublished data will be requested for unpublished or ongoing studies, but data from abstracts only will be excluded. Searches will not be filtered by language, but non-English language articles will be omitted at the title screening stage. All search terms are provided in Additional file 2.

All references will be downloaded into EndNote or Reference Manager, and duplicates will be found and removed using the software automatic tools. Reviews and trials will be selected by FD and MD independently, with discussion as needed. If both reviewers agree that an RCT does not meet the inclusion criteria, it will be excluded from further analysis. Then, full texts of all eligible RCTs will be obtained and reviewed for final inclusion. Disagreements will be discussed with a third reviewer.

RCT data will be extracted independently by FD and MD. We will adopt a structured data extraction form designed for the present review, to enhance the completeness and consistency of data extraction. Data extracted will include study characteristics (first author, year of publication, journal, setting), participant characteristics (sample size, mean age, % women, inclusion criteria [for CAD and depression], intervention details (anti-depressant [dose, duration, dosing schedule]; for psychotherapy interventions the TIDiER checklist headings will be adopted for extraction criteria (i.e. brief name of intervention, rationale/theory, materials, procedures, who provided the intervention, mode of delivery, location/setting, dose/intensity, tailoring, modifications, fidelity) [44]. While obviously the content of psychotherapies can be heterogeneous, the use of TIDiER headings will allow the careful documentation of any significant disparities in content and delivery forms that may necessitate subsequent sensitivity analysis, although it is difficult to estimate this a priori. TIDiER will also be used to fully describe the comparison groups, prior to grouping for the NMA analysis (see above). Outcomes data will also be extracted—see below for details. Summary effect sizes will be calculated from data extracted from the RCTs, including multi-arm (three or more groups) trials, where data will be extracted at the arm level from the original reports. Two review authors will verify that the data has been inputted correctly into the final dataset.

SMDs and 95% confidence intervals, or means, SDs and number of patients in each trial arm will be extracted for continuous outcomes. Otherwise, the authors will be emailed to request the data. If some data is omitted (e.g. missing SDs or if p values only are reported), we will use the metaeff command procedures in Stata to calculate SMDs and 95% confidence intervals from available data [45]. If insufficient data is available to calculate the SMD, we will include the study for descriptive purposes only and omit the study from the main network analyses. If insufficient data is available to calculate the 95% confidence intervals, we will impute this will the median from the other studies within that particular grouping. If > 5% of studies require such imputation, we will consider multiple imputation techniques. A sensitivity analysis will be conducted to determine if there are any important implications of such imputation.

The numbers of participants in each arm with each event will be extracted for each trial arm. If data is unavailable, we will contact the authors. Values will be imputed where continuous data is provided instead of numeric values, using an approved method [46].

For the synthesis of primary outcomes and the secondary outcomes of adverse events, we will adopt the 8-week threshold as per the previous review, or, if data is unavailable for this duration, we will use the closest available data from 4 to 16 weeks [13, 36]. If data on adverse events (dropout) is not available for this time period, we will consider using the overall dropout rate as a proxy. This was adopted as researchers believed that depression treatments should work in a clinically reasonable period of time. We will adopt a longer-term, 6-month depression assessment as a secondary outcome. For other outcomes, data from the longest duration of follow-up will be obtained.

We will primarily adopt the results as reported in the original trials, irrespective of whether they adopted appropriate methods for dealing with missing data or not (e.g. reporting per protocol results instead of intention-to-treat). Ratings of the appropriateness or otherwise of the missing data imputation is already part of the risk of bias assessment conducted in prior meta-analyses (e.g. [6, 11]).

We will adopt the methods of the recent anti-depressant NMA when dealing with a unit of analysis issues [13, 36], if these were not addressed by the obtained meta-analyses. Data extracted for cluster RCTs will account for clustering in the design (e.g. we will use data from multi-level models), whereas data from only the first period of cross-over trials will be used, due to potential carryover effects.

Where available, we will extract the Cochrane risk of bias tool [47] ratings from prior reviews (e.g. [6, 11]). Where published reviews disagree on the quality rating, or where there is no such rating, FD and MD will independently assess included RCTs using this Cochrane risk of bias tool, with disagreements discussed and resolved with a third team member. Risk of bias will be assessed for the following design areas (for placebo-controlled trials): generation of allocation sequence, allocation concealment, blinding of outcome assessor, attrition (adopting similar criteria to Furukawa et al. [13, 36]), selective outcome reporting (for the primary outcomes only) and other domains (e.g. sponsorship bias). If any details are inadequate, RCT authors will be contacted for missing information. Given the nature of complex or psychotherapeutic interventions, assessing the blinding of treatment assignment is not usually possible, so it is likely that most of these trials will exhibit high risk of bias, whereas the placebo-controlled drug trials will be less biassed. We will also consider whether different risks of bias estimates are needed for particular arms of multi-arm trials [28]. When comparing the trials, the blinding of outcome assessments will take precedence [9].

We will also follow the recommendations for NMA and use the Grading of Recommendations Assessment, Development and Evaluation (GRADE) framework for obtained results [13, 36, 48]. This framework characterises the overall evidence contributing to the main outcomes from the network estimates incorporating information from the study limitations, imprecision, inconsistency, indirectness and publication bias, any of which could downgrade the obtained summary evidence [49]. GRADE ratings will be presented in a summary findings table.

Descriptive statistics for the RCTs will be used to profile the overall study and clinical features, such as publication year, age, proportions of women, clinical setting, number of trial arms, intervention content and comparator group content. A network diagram will be used, with node size indicating the number of patients for each treatment (or comparator) group, and edge width used as an indicator of the numbers of studies making the comparison [20]. Several comparator groups will be used in the main network, as outlined in the ‘Comparison groups’ section above. The most influential network comparisons will be evaluated using a contribution matrix, which describes the proportion of the contribution to the entire network of each direct meta-analysis [50]. Two main networks will be evaluated using frequentist multivariate meta-analysis (commands network meta and mvmeta, which underpins the first command) in Stata 15 [51]. These commands perform restricted maximum likelihood methods for random effects multivariate meta-analysis by using a Newton-Raphson procedure, accounting for within- and between-study correlations. The assumptions of this model are that the multiple modelled effects represent a multivariate normal approximation of the estimated effects; that a multivariate linear regression can be performed due to linear effects between studies; a constant between-studies covariance matrix, where conditional variances of all components of the random effect are constant; and a symmetrical normal distribution which does not allow for light or heavy tails (which consequently means that outlier trial results can be overly influential for final estimates) [51]. The interested reader is referred to the following references for more detail [51, 52].

The first analysis will contain the original groupings as outlined above (i.e. pharmacotherapy, psychotherapies, exercise, collaborative care, comparator groups). A second main analysis will separate the different groupings, i.e. by type of anti-depressant (e.g. fluoxetine, sertraline), type of psychotherapy (e.g. CBT, interpersonal psychotherapy, mindfulness), if there is enough available data. Any derived ranking of treatments will only be done for primary outcomes, although given the probable sparsity of evidence we acknowledge in advance that this ranking may have a substantial error. As some trials may not report change scores, but may report end-of-trial scores only, we will consider a supplementary analysis where we include the end-of-trial only scores if this is required to generate the network, or there is likely to be substantial missing data (i.e. > 10% of trial estimates missing).

As interventions are by definition heterogeneous, random effects pairwise meta-analyses will be used to obtain SMDs or odds ratios (with associated 95% confidence intervals) for continuous and binary outcomes respectively [51, 53], with the I² statistic used to quantify heterogeneity. All pairwise estimates and associated 95% confidence intervals will be reported. Pairwise meta-analytic estimates are usually reported in addition to the network estimates [13, 36, 52]. Among other reasons, they are useful (1) to determine the potential effects of any outliers and (2) to demonstrate any differences in estimated effects from the network meta-analysis which could be attributed to the correlation between the outcomes—which is ignored in a pairwise meta-analysis [52].

Transitivity is a key assumption of NMA and refers to the belief that an indirect comparison is a valid estimate of the unobserved direct comparison [48]. The transitivity assumption was initially addressed by the inclusion of patients with CAD only—as treatments for CAD are largely similar, i.e. risk factor control such as hypertension management, lipid-lowering and smoking cessation—these patients were considered similar enough for synthesising the information. Transitivity assessment will follow previous research [13, 36, 48]—by investigating effect modifiers across treatment comparisons, such as subthreshold depression or baseline depression severity, age, dosing (or intensity) [54‐56], sex and cardiovascular disease severity [2], and differences in placebo-controlled versus other comparator group studies [39, 40]. Comparing the relative distribution of such variables across RCTs may provide some evidence for this assumption. Furthermore, we will compare the placebo-controlled trials to any head-to-head trials to ascertain any differences [36]. We assume that all RCT participants would have had equal opportunity to be randomised to any of the trial arms (apart from any potential patient preference studies). If transitivity is not demonstrated (e.g. if there are clear, statistically significant and/or clinically important differences in patients enrolled to trials in terms of age, sex, CAD or depression severity indices [48]), we may explore building separate networks to reflect the evidence.

Prior to conducting the NMA, inconsistency, which is the disagreement between direct and indirect evidence [48], will be assessed using both local and global methods in Stata as appropriate, and also by calculating the I² for network heterogeneity and inconsistency [20, 28, 50, 57]. Heterogeneity variance will be considered equal within groupings, but possibly different among groups. Local parts of the network will be evaluated using the loop-specific and node-splitting methods. The global network will be evaluated using a design-by-treatment interaction model. We will also display inconsistency factors as recommended, but will use caution in interpretation due to the chance of finding inconsistency by chance alone, or have wide 95% confidence intervals [20].

Sensitivity analysis will also mainly follow previous work [13, 36]—the treatment effects for the primary outcomes will be explored in subgroup analysis and meta-regression for the following variables: study year, RCT sponsorship/funding (industry versus government/charity), baseline depression severity, intervention intensity or dosing schedule, comparator grouping, study design, setting or country. Where practicable, analyses will also be conducted addressing enrolment period: studies that enrol patients up to 6 months after an acute coronary event (or those that assess depressive symptoms on two or more occasions prior to enrolment) versus those that enrol stable patients or 6 months after an acute event; studies that provide depression treatment choice versus those that do not. Sensitivity analysis will address different levels of risk of bias (low, medium, high) [58], but also intensity of interventions as rated by a dichotomous variable (as rated by FD and MD, i.e. using the recommended to maximum doses of pharmacotherapies or greater than four sessions of psychotherapies—these will be classified as high-intensity interventions; otherwise, low dosage pharmacotherapy or four or fewer sessions of psychotherapy will be classed as low-intensity).

Funnel plots for NMA, which plot the difference between the study-specific effect sizes from the corresponding comparison-specific summary versus the inverted standard error, will be used to ascertain whether estimates from more imprecise RCTs are different from those RCTs with more precision (such as larger effect sizes for depression treatment in smaller studies) [28, 50]. A network meta-regression will investigate associations between effect size and study sample size.

Rankograms and surface under the cumulative ranking (SUCRA) curves will be used for treatment ranking [20]. SUCRA can be usefully re-expressed as the percentage of effectiveness/acceptability of depression interventions that would be rated first ranking, without uncertainty. Although we will report the probability that a given treatment is best, second best, third best etc., such probability statements will be interpreted cautiously unless there are actual clinically meaningful differences among the interventions.

All analyses will be implemented in Stata 15.