Duloxetine versus ‘active’ placebo, placebo or no intervention for major depressive disorder; a protocol for a systematic review of randomised clinical trials with meta-analysis and trial sequential analysis

According to the World Health Organization (WHO), 264 million people suffer from depression around the globe [1] and major depressive disorder has been estimated to be the third leading cause of years lived with disability in both sexes [2]. Major depressive disorder is, depending on the diagnostic system, characterised by the occurrence of depressed mood, loss of interest or pleasure, reduced energy or fatigue accompanied by other symptoms such as suicidal thoughts, sleep disturbances, psychomotor agitation or retardation and difficulty concentrating [3, 4]. With a 12-month prevalence of around 5.5% in high-income countries [5], major depressive disorder is a large economic burden due to decreased work productivity [6] and it significantly impairs quality of life [7, 8].

Different classes of antidepressants are available for treatment of patients with major depressive disorder ranging from older antidepressants like mono-amine oxidase inhibitors (MAOI) and tri-cyclic antidepressants (TCA) to newer groups of drugs like selective serotonin reuptake inhibitors (SSRI) and serotonin-norepinephrine reuptake inhibitors (SNRI) as summarised in Table S1 (Additional file 1).

A report from the National Health and Nutrition Examination survey in the USA found an increase in the use of antidepressants from 7.7% in 1999–2002 to 12.7% in 2011–2014, wherein a quarter of those who took antidepressants had been using them for more than 10 years [9]. Whilst SSRIs remain the most commonly prescribed antidepressants, there has been a consistent increase in the prescription of other antidepressants such as duloxetine [10, 11].

Duloxetine, a SNRI, is approved for the treatment of major depressive disorder in the USA and Europe [12, 13]. It is, additionally, approved for a number of other conditions such as generalized anxiety, diabetic neuropathic pain, and fibromyalgia and is among the top 50 most prescribed drugs in the USA with the number of yearly prescriptions exceeding 16,000,000 [14]. In vivo and in vitro studies indicate that duloxetine inhibits the presynaptic neuronal reuptake of the neurotransmitters serotonin and norepinephrine, leading to their greater availability at the neuronal junctions and potentiating their action in the central nervous system [15, 16]. Serotonin and norepinephrine have been suggested to be involved in the pathogenesis of major depressive disorder [17], and theoretically the antidepressant effects of duloxetine have been speculated to be mediated through antagonising the depletion of these two neurotransmitters in the brain [18]. However, the potential role of these and other neurotransmitters in the pathophysiology and treatment of major depressive disorder is unclear [19, 20].

Duloxetine has an average half-life of around 12 h and is metabolised mainly in the liver [21]. Duloxetine is administered orally at a starting dose for the treatment of major depression of 60 mg/day, potentially increased to a maximum dose of 120 mg/day [13]. The most commonly reported adverse effects are nausea, dry mouth, decreased appetite, excessive sweating and drowsiness, whereas the most serious adverse effects include hepatic failure, orthostatic hypotension leading to syncope and falls, suicidal ideation, serotonin syndrome and increased risk of bleeding [22].

Several previous reviews have shown that antidepressants seem to decrease depressive symptoms with a statistically significant effect [23, 24]. However, the effect is small and of uncertain clinical importance to patients [25]. A recent network meta-analysis including 23 trials on duloxetine reported for duloxetine versus placebo a standardised mean difference (SMD) of − 0.37 on depression scales. This was much lower than the empirically derived threshold of 0.875 SMD suggested by Moncrieff and Kirsch, corresponding to ‘minimal improvement’ on the Clinical Global Impressions-Improvement scale as well as lower than the less stringent criteria of 0.5 SMD, suggested by the National Institute of Clinical Excellence (NICE) in England [25‐27]. More recently, Hengartner and Ploderl, reviewing both within patient and between patient anchor-based approaches, suggested that minimal important difference on 17-item Hamilton Depression Rating Scale (HDRS-17) is likely to be to be in the range of 3–5 points [28]. Whilst the ‘minimum clinically important difference’ on depression scales remains an area of debate with no consensus so far, the small statistically significant improvement in depressive symptoms with duloxetine must be weighed against the questionable clinical significance of the intervention whilst also taking harmful effects and costs into consideration.

Moreover, in many systematic reviews and meta-analyses including randomised placebo-controlled trials of duloxetine, remission and response defined as dichotomous outcomes were used as primary outcome measures and duloxetine was found to be superior compared with placebo (Table 1). However, dichotomisation of continuous scales to calculate response and remission has been criticised and might over-estimate the beneficial effects [25]. A decrease of only one point on the depression symptom severity scales can change categorisation of a trial participant from ‘non-remitter/non-responder’ to ‘remitter/responder’. It is therefore important to synthesise the evidence using the depression symptom severity scales without dichotomising the scores to assess the benefits associated with the use of antidepressants.

In most reviews on duloxetine, adverse effects have not been sufficiently assessed. Instead, proxy measures like tolerability, acceptability and drop-outs due to adverse events have been used to assess safety profile of antidepressants compared with placebo [24, 35]. In other reviews, non-serious adverse events such as anticholinergic adverse effects, dizziness, nausea, sedation and hyperhidrosis have been frequently reported and discussed [29]. However, there is little to no information on more serious adverse events such as suicides or suicide attempts [29, 33, 34].

With regards to serious adverse events, some systematic reviews and meta-analyses report no increased risk of suicide or suicidal tendency with the use of antidepressants including duloxetine versus placebo in adult populations [37, 42], whilst others have observed an age-dependant increase in risk of suicidality [32, 44]. It is important to consider that these analyses suffered from incomplete reporting of adverse events in the included trials and limitations such as a lack of a pre-registered protocol [32, 44], no access to case-report forms [32] which are more likely to record adverse events in particular suicidal events as highlighted in other reviews [45] and low statistical power [42]. Moreover, some of the reviews on duloxetine were at risk of for-profit bias as the authors were employed at or the research was funded by the pharmaceutical industry [37, 42]. In one systematic analysis, Khan et al. examined safety data submitted to the U.S. Food and Drug Administration (FDA) during the period 1991–2013 for the approval of fourteen investigational antidepressants including duloxetine and reported a decline in suicide rates in the antidepressant groups of the clinical trials [46]. However, their analytical approach relied on patient-exposure years (PEY), which was deemed inappropriate by Hengartner and Ploderl [37]. They stressed that the risk of suicidal events is highest during the first few weeks of antidepressant use and this violates the constant-hazard requirement for a PEY analysis. Hengartner and Ploderl argued that this analytical approach can obscure the increased suicide risk associated with initiation of antidepressant use. They therefore reanalysed the data used by Khan et al. and found three times higher odds of suicide with the use of antidepressants [47]. The potential increase in suicide risk presented by Hengartner and Ploderl highlights the importance and need of evaluating adverse effects using appropriate methods.

A retrospective analysis of clinical study reports from 268 trials of drugs assessed by The German Institute for Quality and Efficiency in Health Care (IQWiG) between 2006 and Feb 2011 found that registry reports and publications were inferior to clinical study reports with regards to the outcome reporting, particularly of adverse events [48]. Another cross-sectional study of clinical trial registration summaries and their associated publications observed ambiguities and discrepancies in reporting of serious adverse events in journal articles and trial registration summaries [49]. A study comparing clinical study reports from nine randomised placebo-controlled trials of duloxetine with publicly available documents such as journal articles and results posted on trial registries found not only publication bias in favour of significant findings on efficacy analysis but also that information on serious adverse events was missing from journal articles and registry reports [50]. In addition, treatment emergent adverse effects were only reported in journal articles if the incidence was higher than a certain percentage, whereas information on discontinuation related adverse events was unavailable or vaguely reported if at all [50]. Another issue observed was that the coding of suicidality events from investigator reported adverse events resulted in inaccurate reporting of this information in clinical study reports as compared to the patient data [51]. Taken together, the evidence points to a need to extend the assessment of adverse events beyond published literature to get a more accurate assessment of benefits and harms associated with the use of antidepressants.

We searched PubMed and Google Scholar for existing evidence on duloxetine using the search terms ‘duloxetine’, ‘major depression’ and ‘systematic reviews’. We identified a total of 16 meta-analyses, overviews or systematic reviews including randomised clinical trials on duloxetine versus placebo as summarised in Table 1 [36, 39‐41, 43]. We identified three reviews and meta-analyses that summarised the evidence on both benefits and harms of duloxetine and which also assessed the risk of bias in the included trials. Only one of these reviews met all the criteria outlined in the Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA) checklist [52]. However, this review was of low generalisability as it focussed only on elderly participants and only included trials published in English [31]. Furthermore, the review included only three duloxetine trials and no duloxetine-related serious adverse events were reported or discussed in this review. Of the other two reviews, one focussed on older adults only [29], and one included only four duloxetine trials, did not publish a protocol and limited electronic searches to English language [29, 38]. None of the reviews evaluated duloxetine versus ‘active placebo’, i.e. an active substance with no anti-depressant effect, e.g. an antihistamine that mimics the adverse effects of duloxetine such as dizziness, dry mouth and nausea [20, 22].

We also searched for ongoing systematic reviews comparing duloxetine versus ‘active’ placebo, placebo or no intervention for the treatment of major depression in the international prospective register of systematic reviews PROSPERO. We only found one protocol for a systematic review comparing duloxetine versus placebo; it plans to include trials where duloxetine was used for a wide range of indications apart from major depressive disorder such as generalized anxiety disorder, fibromyalgia and diabetic peripheral neuropathic pain [53]. Other identified ongoing systematic reviews on duloxetine will only include head-to-head comparisons with other antidepressants [54‐56] or involve indications other than major depression [57]. We identified no systematic reviews assessing the benefits and harms of duloxetine compared with ‘active’ placebo.

Thus, no former or presently planned review has systematically reviewed the beneficial and harmful effects of duloxetine taking into account both the risk of random errors and the risk of systematic errors in all randomised clinical trials on major depressive disorder [58]. Hence, we planned this systematic review to assess the beneficial and harmful effects of duloxetine versus ‘active’ placebo, placebo or no intervention in the treatment of major depressive disorder. This review will also contribute data to a larger project assessing the beneficial and harmful effects of all anti-depressants in patients with major depressive disorder [59].

We will search the Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE, EMBASE, PsycInfo, Science Citation Index Expanded, Social Sciences Citation Index (SSCI), Conference Proceedings Citation Index—Science (CPCI-S) and Conference Proceedings Citation Index—Social Science & Humanities (CPCI-SSH) (Additional file 3). We will also search Chinese databases (CNKI, Wanfang, VIP, Sinomed) and Google Scholar. We will search all databases from their inception to present. We will check relevant publications, e.g. included trials and systematic reviews, for relevant trials. To identify unpublished trials, we will search trials registers of pharmaceutical companies, the WHO trial registry, clinicaltrials.​gov, including the websites of the FDA and the European Medicines Agency (EMA). Furthermore, we will request clinical study reports from FDA, EMA and national medicines agencies. We will contact trial authors to seek required information.

Two of the review authors (FS and MB) will independently select relevant trials, based on criteria described in the above section. If a trial only has been identified by one of the two, it will be discussed whether the trial should be included. If the two review authors disagree, a third review author (JCJ) will decide if the trial should be included. All excluded trials assessed in full text will be entered on a list, stating the reason for exclusion.

Data will be extracted by two reviewers independently. The following data will be extracted from the included trials:

1. Trial: publication status, date of publication, year of study conduction/randomisation, duration of trial, trial design, for-profit funding of trial, NCT/EudraCT number.

2. Participants: mean age, sex distribution, number randomised to each comparison group, number analysed, number lost to follow-up, drug or alcohol dependence, chronically depressed or treatment resistant depression (any definition used by the trialists), baseline depression scores, comorbid psychiatric diagnoses, borderline personality disorder, inclusion and exclusion criteria.

3. Intervention: length of intervention period and follow-up period, dose of duloxetine, dosing schedule, co-interventions such as psychotherapy or electroconvulsive therapy, whether the experimental intervention is an add-on therapy on other antidepressants, placebo washout period, choice of control (‘active’ placebo, placebo or no intervention).

4. Outcomes: primary and secondary outcomes (e.g. HDRS scores, BDI scores, number of suicides), type of outcome reported (e.g. change in scores, post-intervention scores), mean, standard deviation (SD) and number analysed for all continuous outcomes, number of events and number analysed for dichotomous outcomes, method of data collection for adverse effects, i.e. active monitoring or spontaneous report monitoring.

5. Others: author’s affiliations, an evaluation of the bias risk and choice of method (see below).

Two review authors will assess risk of bias in the included trials independent of each other using Cochrane’s risk of bias tool version 2 (RoB 2) [73]. The risk of bias assessment will be made for each outcome as well as overall risk of bias for the trial. We will evaluate the methodology to identify bias resulting from the randomisation process, deviation from the intended interventions, missing outcome data, measurement of the outcome as well as the selective reporting of results. We will classify the trials according to the components below as summarised in the RoB 2 guidance document (Table 2) [74].

Low risk of bias: The study is judged to be at low risk of bias for all domains for this result. Some concerns: The study is judged to be at some concerns in at least one domain for this result. High risk of bias: The study is judged to be at high risk of bias in at least one domain for this result OR the study is judged to have some concerns for multiple domains in a way that substantially lowers confidence in the result.

For our purposes, we will combine some concerns and high risk of bias judgements so that in our overall assessment of risk of bias, we will classify trials either to be at overall low risk of bias or at overall high risk of bias.

On all outcomes, we will create and inspect a funnel plot to assess possible small-study biases if ten or more trials are included, unless the trials are of similar size. For dichotomous outcomes, we will test asymmetry with the Harbord test if τ² is less than 0.1 and with the Rücker test if τ² is more than 0.1. For continuous outcomes, we will use the regression asymmetry test [75] and the adjusted rank correlation [76].

We will account for for-profit interests under publication bias in the GRADE assessment. Trials initiated, conducted or funded by pharmaceutical industry as well as the trials with any of the authors affiliated with the industry or where authors received grants from industry (self-reported in the article) will be considered at risk of for-profit interests [77]. We will downgrade for for-profit influence if the subgroup analysis according to risk of for-profit interests (see below) shows a difference between the intervention groups.

The review will be conducted in accordance with this protocol. Deviations from the protocol, if any, will be reported in the systematic review under the section ‘Differences between the protocol and the review’.

Data will be meta-analysed using statistical software STATA 16.1 (StataCorp 2019. Stata Statistical Software: Release 16. College Station, TX: StataCorp LLC). We will undertake meta-analysis according to the recommendations stated in the Cochrane Handbook for Systematic Reviews of Interventions and the eight-step assessment suggested by Jakobsen et al. [58]. When analysing continuous outcomes, we will calculate mean differences (MDs) with 95% confidence intervals (CIs). We will use the Sidik-Jonkman model for random-effects meta-analysis [78]. We will also use the SMD with a 95% CI to analyse the results when different scales have been used. We will pool trials reporting change in scores and post intervention scores for mean difference; however, they will not be pooled for SMD [72]. We will also calculate trial sequential analysis-adjusted CIs (see below). When analysing dichotomous outcomes, we will calculate risk ratios (RRs) with 95% CI as well as the trial sequential analysis-adjusted CIs (see below). For rare outcomes such as adverse effects, we will use binomial regression analysis [79].

Intervention effects will be assessed by both random-effects model meta-analyses and fixed-effect model meta-analyses and we will use the more conservative point estimate of the two [72]. The more conservative point estimate is the estimate with the highest P value. We plan to assess a total of five primary and secondary outcome therefore we will consider P ≤ 0.016 as statistically significant [58]. We will investigate possible heterogeneity through subgroup analyses. We will use the eight-step procedure to assess if the thresholds for significance are crossed [58]. Our primary conclusion will be based on trials at overall low risk of bias. Where multiple trial arms are reported in a single trial, we will include only the relevant arms. For trials with multiple intervention arms, we will correspondingly divide the control group. If quantitative synthesis is not appropriate due to considerable heterogeneity or a small number of included trials, we will report the results in a descriptive way.

Although there is no current consensus on the issue, the National Institute for Clinical Excellence (NICE) of the National Health Service in England has formerly defined a threshold for clinical significance for major depressive disorder as an effect size of 0.50 SMD or a drug-placebo difference of three points on the 17-item HDRS [27]. Others have suggested and used the following ‘rule of thumb’: 0.2 SMD represents a small effect, 0.5 SMD a moderate effect and 0.8 SMD a large effect [72, 80]. We have chosen, as NICE has formerly recommended and other reviewers have chosen [27, 81, 82], a drug-placebo difference of three points on the 17-item HDRS (for our primary outcome) or an effect size of 0.50 SMD (for our exploratory outcome) as the threshold for clinical significance. This is in line with findings from a recent review, suggesting that the most likely minimal important difference on the HDRS-17 is between 3 and 5 points [28].

To control the risk of type I and type II errors, we will use Trial Sequential Analyses. We will perform trial sequential analyses on all the outcomes [83‐85], in order to calculate the diversity-adjusted required information size (that is, the number of participants needed in a meta-analysis to detect or reject a certain intervention effect) and the cumulative Z-curve’s breach of relevant trial sequential monitoring boundaries. A more detailed description of trial sequential analysis can be found at http://​www.​ctu.​dk/​tsa [84]. For continuous outcomes, trial sequential analysis will use the empirical SD, a mean difference of three points on the Hamilton Depression Rating Scale (17 or 21 item) and the observed SD/2 when other depression scales or quality of life scales are used, an alpha of 1.7%, a beta of 10% and adjustment for the observed diversity. For dichotomous outcomes, trial sequential analysis will use the proportion of participants with an outcome in the control group, a relative risk reduction of 25%, an alpha of 1.7% for primary outcomes, a beta of 10% and adjustment for the observed diversity of the trials in the meta-analysis.

We will use intention-to-treat data if reported by the trialists [86]. If intention-to-treat data are not reported, we will use the data as reported by the trialists. We will, as the first option, contact all trial authors to obtain any relevant missing data (i.e. for data extraction and for assessment of risk of bias, as specified above).

Dichotomous outcomes: we will not impute missing values for any outcomes in our primary analysis. In our sensitivity analyses (see paragraph below), we will impute data.

Continuous outcomes: we will primarily analyse scores assessed at single time points (end scores). If only changes from baseline scores are reported, we will analyse the results together with end scores [72]. If SDs are not reported, we will calculate the SDs using trial data, if possible. We will not use intention-to-treat data if the original report did not contain such data. We will not impute missing values for any outcomes in our primary analysis. In our sensitivity analysis (see paragraph below) for continuous outcomes, we will impute data.

To assess the potential impact of the missing data for dichotomous outcomes, we will perform the following two sensitivity analyses on both the primary and the secondary dichotomous outcomes. We will present results of both scenarios in our review.

We will present results of these scenarios in our review. Other post hoc sensitivity analyses might be warranted if unexpected clinical or statistical heterogeneity is identified during the analysis of the review results.

We will primarily investigate forest plots to visually assess any sign of heterogeneity. We will secondly assess the presence of statistical heterogeneity by chi² test (threshold P < 0.10) and measure the quantities of heterogeneity by the I² statistic. We will investigate possible heterogeneity through subgroup analyses. According to the Cochrane Handbook, I² statistic above 50% will be regarded as substantial heterogeneity and we may ultimately decide that a meta-analysis should be avoided [72].

We have planned the following subgroup analyses on all the outcomes:

We will assess the certainty of evidence of all outcomes using GRADE (Grading of Recommendations Assessment, Development and Evaluation) tool. Cochrane Handbook for Systematic Reviews of Interventions (Chapter 8: Section 8.5 and Chapter 12) will be followed for GRADE evaluation using the GRADEpro software [72]. We will use the five GRADE domains (bias risk of the trials, consistency of effect, imprecision, indirectness and publication bias) to assess the quality of a body of evidence. Imprecision will be assessed using trial sequential analysis [58]. We will downgrade imprecision in GRADE by two levels if the accrued number of participants is below 50% of the diversity-adjusted required information size (DARIS), and one level if between 50% and 100% of DARIS. We will not downgrade if the cumulative Z-curve crosses the monitoring boundaries for benefit, harm or futility, or DARIS is reached [88]. The findings for primary outcomes will be presented in a summary of findings table where each GRADE domain will be presented for trials contributing data to the meta-analyses for the prespecified outcomes [58, 89]. We will justify all decisions when downgrading the certainty of evidence using footnotes, and we will add comments to aid the reader’s understanding of the review where necessary.