Antidepressants for pain management in adults with chronic pain: a network meta-analysis

What are they, and how might they work?

Antidepressants are medicines developed and used primarily for the treatment of clinical depression. A network meta-analysis (NMA) of the 21 most common antidepressants has shown that they are efficacious in the treatment of acute major depression, particularly severe depression. 19

Antidepressants are grouped into different classes based on their chemical structure and presumed mechanism of action. The most common classes are as follows:

1. tricyclic antidepressants (TCAs): amitriptyline, desipramine, imipramine, nortriptyline and others

2. selective serotonin reuptake inhibitors (SSRIs): citalopram, sertraline, fluoxetine and others

3. serotonin norepinephrine reuptake inhibitors (SNRIs): duloxetine, levomilnacipran, milnacipran, venlafaxine

Antidepressants were originally developed to treat depression. Most antidepressants work by targeting monoamine neurotransmitters associated with mood and emotion and their receptors in the nervous system. These receptors, such as 5-hydroxytryptamine receptors, are activated by many neurotransmitters including serotonin, dopamine, adrenaline and noradrenaline. 20 Antidepressants prevent the neurotransmitters from being absorbed into neurons, which prolongs their activity in synapses. While the process by which antidepressants relieve depression is not fully understood, recent theories focus on neurochemical changes and neuroplasticity. 20

Changes in the pain response systems travelling to and from the brainstem and involving the noradrenergic neurotransmitters have been theorised to explain the analgesic properties of antidepressants, and their proposed ability to reduce pain. By increasing the amount of serotonin and noradrenaline in the nervous system, pain signals are hypothesised to be blocked at the peripheral, spinal and supraspinal levels, reducing perceived pain, particularly in neuropathic pain. 21,22

In addition, the locus coeruleus in the brain may have an analgesic effect on perceived pain. 23 Signals from this part of the brain are sent when the body reacts to a stimulus, such as pain, and noradrenaline is released into the dorsal horn in the spine to block receptors. Animal studies have shown that when pain signals are continuously received, as is the case in chronic pain, this analgesic response lessens over time, and noradrenaline is then not released. 23,24 However, when antidepressants are given, the analgesic response from the locus coeruleus is restored. 23,25

Guidelines for antidepressants in the treatment of chronic pain

Antidepressants are one of the few remaining recommended pharmacological interventions for chronic pain, although, to date, the evidence has not allowed the nuance of ranking the prioritisation. Where consideration of the quality of the supporting evidence is reported, it is often unclear. 26 Across guidelines from the USA,27 Canada28 and Japan,29 TCAs (e.g. amitriptyline, nortriptyline) and SNRIs (e.g. duloxetine, milnacipran) are the most common classes recommended. In the UK, the National Institute for Health and Care Excellence (NICE) has produced different sets of recommendations for different pain types: chronic primary pain,30 neuropathic pain,31 low back pain and sciatica32 and osteoarthritis. 33 For chronic primary pain, amitriptyline, citalopram, duloxetine, fluoxetine, paroxetine and sertraline are recommended equally. For neuropathic pain, amitriptyline or duloxetine are recommended. For low back pain and sciatica, the guidelines explicitly advise against use of SNRIs, SSRIs and TCAs; and for osteoarthritis, antidepressants are omitted entirely. The lack of concordance across guidelines can be confusing for clinicians, especially as many patients present with several types of pain concurrently. Furthermore, some of these recommendations are made based on very low-quality evidence. For example, in the chronic primary pain guidelines,9 citalopram is recommended based upon one trial with 42 participants,34 sertraline from one crossover trial with 14 participants,35 and paroxetine from one trial with 46 participants. 36 These small trials are of very low scientific rigour and are not a reliable evidence base. This is especially alarming given that within the context of the guidelines, antidepressants are the only pharmacological intervention recommended. Although the NICE guidelines for treatment of chronic low back pain published in 2016 recommend not prescribing antidepressants (regardless of mood), NICE guidelines for people with depression and chronic health problems recommend antidepressants in cases of mild depression and physical health problems. No advice exists to help practitioners resolve the contradiction between the two sets of advice.

Antidepressants in practice

Prescriptions of antidepressants are relatively common in patients with chronic pain internationally; for example, 12.3% of people with chronic low back pain in Portugal report taking antidepressants for pain relief. 37,38

In the UK, amitriptyline has long been the most commonly prescribed antidepressant for chronic pain. Amitriptyline was widely used to treat depression from the 1960s, but has restricted use now due to the risk of taking a lethal overdose. Its use is also characterised by side effects such as dizziness, dry mouth, constipation and weight gain; side effects are more common with higher dosages. Although amitriptyline is only licensed for the treatment of depression and neuropathic pain, it is commonly prescribed ‘off licence’ at a lower dose to treat any chronic pain. TCAs (of which the most common is amitriptyline) are the 19th most common prescription in primary care, accounting for 1.6% of all prescriptions. 39 Open-source prescribing data recorded over 14.5 million prescriptions for amitriptyline in 2021. 40 It is reasonable to believe that a majority of these prescriptions were for pain: amitriptyline is not recommended to treat depression,41 and chronic pain is the most common indicator for antidepressant prescription in older adults. 42 A multinational comparison of antidepressant use in older adults found that TCAs were the most common class in the UK prescribed for chronic pain, at 55%. In comparison, SNRI prescriptions were very low (1.5%). 41 Indeed, there were 3.4 million duloxetine prescriptions in 2021, less than one-quarter of the number of amitriptyline prescriptions.

Antidepressants and safety

There are also risks in the prescription of antidepressants. Adverse events such as dizziness, headache, nausea, ejaculation disorder, weight loss, tremor, sweating and insomnia have been found by randomised controlled trials (RCTs) to be more common in people taking antidepressants compared with those taking placebo. 43,44 Studies assessing the safety of antidepressants across a range of adverse outcomes in older people45,46 and in people aged 20–64 years47,48 have shown increased risks of falls and fractures associated with most antidepressants, and differences between antidepressants in risks of all-cause mortality, stroke and self-harm or suicide. Antidepressants also increase the risk of onset of seizures,49 while the potential for gastrointestinal bleeding with SSRIs is widely recognised. 50 Long-term use of antidepressants for pain syndromes is therefore expected to be associated with harms at the population level.

The evidence on the efficacy and safety of antidepressants

At the start of this study, there was no evidence comparing classes of antidepressants to each other in the management of chronic pain, as identified by the recent NICE guidelines. 51 There have been several systematic reviews for specific conditions (detailed below). Therefore, in the absence of any one RCT comparing the efficacy and safety of all antidepressants for chronic pain, a NMA was considered a priority to assess the relative effectiveness of each antidepressant, by dose.

Previous Cochrane Reviews investigated the efficacy of specific antidepressants in improving pain in specific conditions. A summary of their findings indicates that there is no high-quality evidence to support or refute the use of amitriptyline, milnacipran, nortriptyline, venlafaxine, desipramine or imipramine for management of neuropathic pain,52–57 principally because trials are few and those that exist have small numbers of participants and typically have high risks of bias. The lack of evidence for some antidepressants stands in stark contradiction to guideline recommendations. For example, amitriptyline is recommended as a first-line treatment for neuropathic pain in primary care in guidelines for the UK, Canada and the International Association for the Study of Pain (IASP). 31,58–60

For fibromyalgia, Cochrane Reviews of antidepressants show that there is no unbiased evidence that amitriptyline, desvenlafaxine, venlafaxine or SSRIs are superior to placebo. 61,62 There is low-quality evidence that duloxetine and milnacipran have some benefit in improving Patient Global Impression of Change (PGIC) scores and providing an improvement in pain relief of 30% or more, but no clinical benefit over placebo for improvement in pain relief of 50% or more, health-related quality of life or fatigue. 62 Similarly for mirtazapine, there is evidence for improvement in pain relief of 30% or more, and reduction of mean pain intensity and sleep problems, but this evidence is of low to medium quality, and there is no benefit for improvement in pain relief of 50% or more, PGIC, 20% improvement of health-related quality of life, reduction of fatigue or reduction in negative mood. 63

Only one Cochrane Review has investigated the use of antidepressants for low back pain, and it found no clear evidence to support the use of any antidepressants. 64 A more recent systematic review supports these conclusions. 65 However, when analysed using the ‘baseline observation carried forward’ (BOCF) imputation method for missing data, pooled individual patient data analyses of RCTs have shown duloxetine and etoricoxib to be effective in reducing pain for pain conditions including chronic low back pain. 3,63,66 These distributions were bimodal: participants generally responded very well or very poorly, with few in between. 3

The current systematic review and NMA allowed us to compare, for the first time, all antidepressants across all chronic pain conditions (bar headache), and identify whether certain classes or doses of antidepressants are useful in the management of pain and mood for people with chronic pain, and for certain chronic pain conditions. As antidepressants are also associated with a number of side effects, the review allowed the comparison of the proportion of adverse events occurring with the use of different antidepressants (including different classes of antidepressants, different types of antidepressants, and different dose regimens) within populations living with chronic pain.

Types of studies

We included RCTs that compared any antidepressant with any comparator. RCTs are the best design to minimise bias when evaluating the effectiveness of an intervention. We followed the guidance in the Cochrane Handbook for Systematic Reviews of Interventions for the inclusion of crossover RCTs, which requires inclusion of this type of study unless there is a justifiable reason not to. 76 The risk in this review was that washout periods between the periods of the study would not be long enough for carry-over effects from the antidepressants or comparators to be sufficiently minimised. Therefore, we only included crossover trials with washout periods of at least five times the length of the antidepressant half-life (this was calculated individually for each antidepressant).

The most common comparators we anticipated finding in the literature were as follows: the same antidepressant at a different dose; a different antidepressant; placebo (both active and inert); other medications for pain management purposes (e.g. pregabalin, gabapentin); analgesics; psychological therapy (e.g. cognitive behavioural therapy, acceptance and commitment therapy); exercise; physiotherapy; multidisciplinary pain programmes; herbal medicines and nutraceuticals (e.g. St John’s Wort); and acupuncture. Where the comparator was a placebo, antidepressant, analgesic or other medication for pain management purposes, these trials were required to be double-blind. We included trials examining any dose of antidepressants, with a study duration of at least 2 weeks and minimum of 10 participants per arm. We excluded non-randomised studies, case reports, experimental studies, clinical observations and prevention studies.

Types of participants

We included adults (aged 18 years or older) reporting primary or secondary pain in any part of their body (except headache) as their primary complaint, that matched the IASP definition of chronic pain (i.e. at least 3 months’ duration). 1 We included all trials regardless of the severity of participants’ chronic pain, although we extracted whether severity was part of the inclusion criteria of the individual studies. We excluded studies where the participants’ primary complaint was headache or migraine, as had been performed in previous Cochrane Reviews. 77 Although this condition does fit within the IASP criteria, the diagnosis, classification and treatment of primary and secondary headache are often different from those of other pain conditions, and clinical trials are primarily aimed at prevention of further headaches or migraines rather than symptomatic treatment. We included participants with multiple health conditions as long as the chronic pain condition was the focus of the trial.

Types of interventions

Supplementary sets

We included studies with any active comparator. We included studies where the antidepressant was combined with another intervention, as long as there was an arm solely for the other intervention so we were able to isolate the effects of the antidepressant (e.g. antidepressant + drug vs. drug). We did not include combination trials where there was no way to isolate the effects of an antidepressant (e.g. antidepressant A + drug vs. antidepressant B). For this review we assumed that any participant who met the inclusion criteria was, in principle, equally likely to be randomised to any of the eligible antidepressants; however, we acknowledge there may have been differences in patients’ expectations of treatment and outcomes depending upon which antidepressant was studied.

Types of outcome measures

We anticipated that there would be a variety of outcome measures used throughout the literature. Due to the distinction between distress and depression discussed above, this review used the term ‘mood’ as an outcome, to include depression that is diagnosed, mood that is measured via self-report, and distress.

For pain and mood, where applicable we also dichotomised outcomes into pain relief or improvement of 50% or greater, in line with the Initiative on Methods, Measurement, and Pain Assessment in Clinical Trials (IMMPACT) guidance, to indicate substantial improvement. 79 Where possible, we planned separate NMAs to compare antidepressants to the comparators immediately post intervention, at short-term follow-up (≤ 12 weeks post trial) and at long-term follow-up (> 12 weeks post trial). Where studies included multiple follow-up time points, we took the most recent time point within each period. If multiple measures were used for the same outcome (e.g. for continuous pain intensity, both a 0–10 numerical rating scale and the McGill Pain Questionnaire were reported), then we extracted from the most valid, reliable, and widely used measure in the field.

Electronic searches

We searched the following databases, without language restrictions.

• The Cochrane Central Register of Controlled Trials (CENTRAL) via the Cochrane Library – Issue 12 of 12 2021

• MEDLINE and MEDLINE In-Process (via OVID) – 1946 to 4 January 2022

• EMBASE (via OVID) – 1974 to 4 January 2022

• CINAHL (via EBSCO) – 1981 to December 2021

• LILACS (via Birme – December 2021)

• PsycINFO (via EBSCO) – 1872 to 4 January 2022

• AMED (via OVID) – 1985 to December 2021.

We tailored searches to individual databases. The search strategies used can be found in Appendix 1. The search strategy was developed by the Cochrane Pain, Palliative and Supportive Care (PaPaS) Review Group’s information specialist and was independently peer reviewed. The PaPaS information specialist performed the searches.

Searching other resources

We searched ClinicalTrials.gov (www.clinicaltrials.gov) and the World Health Organization’s International Clinical Trials Registry Platform (apps.who.int/trialsearch/) for unpublished and ongoing trials. In addition, we searched grey literature, checked reference lists of reviews and retrieved articles for additional studies, and performed citation searches on key articles. We contacted study authors for additional information where necessary.

Selection of studies

Two review authors (HB and CF) independently determined eligibility of each study identified by the search. Independent review authors eliminated studies that clearly did not satisfy inclusion criteria, and obtained full copies of the remaining studies. HB and CF read these studies independently to select relevant studies, and in the event of a disagreement, third and fourth authors adjudicated (TP and CE). We did not anonymise the studies in any way before assessment. We have included a PRISMA flow chart which shows the status of identified studies,80 as recommended in the Cochrane Handbook. 76 We included studies in the review irrespective of whether measured outcome data were reported in a ‘useable’ way. We recorded reasons for exclusion of any ineligible studies at the full-text stage.

Data extraction and management

Two review authors (HB and CF) independently extracted data using a standard piloted form and checked for agreement before entry into Review Manager 5.4. 81 In the event of disagreement, third and fourth authors (TP and CE) adjudicated. We collated multiple reports of the same study, so that each study rather than each report was the unit of interest in the review. We collected characteristics of the included studies in sufficient detail to populate the table of ‘Characteristics of included studies’. We extracted the following information:

• Study design: authors, publication year and journal, duration, sponsorship, conflicts of interest, aim (pain or emotional functioning), trial design, number of treatment arms, setting, missing data methods, power calculation used, definition of chronic pain, minimum level of pain for entry, inclusion and exclusion criteria

• Participant characteristics: overall number, number in each arm, withdrawal (total, per arm and by sex), type of participant, chronic pain conditions, sex, age, baseline differences

• Intervention: type of antidepressant, class, dose (freeform and dichotomised), route of administration, duration

• Comparator(s): type (e.g. placebo, psychological therapy), description (if placebo medication: active or inert, appearance, taste, smell, titration, number of tablets), type and class (if other antidepressant), doses, route of administration, length, intensity (if physical or psychological comparator)

• Outcomes (data from all time points reported in the study): domain (e.g. pain, physical functioning), measure, measure validation, baseline data, results for each time point, effect sizes

• Adverse events and withdrawals (proportion overall and per arm): any, serious, withdrawal due to adverse event, withdrawal due to lack of efficacy.

Assessment of risk of bias in included studies

Two review authors (HB and CF) independently assessed risk of bias for each study, using the criteria outlined in the Cochrane Handbook,81 with any disagreements resolved by discussion. We completed a ‘risk of bias’ table for each included study using the Cochrane ‘risk of bias’ tool version 1.0 in Review Manager 5.4. 81

We assessed the following for each study:

• Random sequence generation (checking for possible selection bias):

  • We assessed the method used to generate the allocation sequence as being at low risk of bias (any truly random process, e.g. random number table, computer random number generator) or unclear risk of bias (method used to generate sequence not clearly stated).

  • We excluded studies using a non-random process (e.g. odd or even date of birth, hospital or clinic record number).

• Allocation concealment (checking for possible selection bias). The method used to conceal allocation to interventions prior to assignment determines whether intervention allocation could have been foreseen in advance of or during recruitment, or changed after assignment.

  • We assessed the methods as being at low risk of bias (e.g. telephone or central randomisation; consecutively numbered, sealed, opaque envelopes) or unclear risk of bias (method not clearly stated).

  • We excluded studies that did not conceal allocation (e.g. open list).

• Blinding of participants and personnel (checking for possible performance bias). Due to the inclusion of trials using any comparator, our review contained both double-blinded RCTs and those studies in which double-blinding was not possible (i.e. RCTs of psychological therapy or acupuncture). In the RCTs that were double-blinded, we assessed the methods used to blind study participants and personnel from knowledge of which intervention a participant received.

  • We assessed methods as being at low risk of bias (the study states that it was blinded and describes the method used to achieve blinding, such as identical tablets matched in appearance or smell, or a double-dummy technique) or unclear risk of bias (the study states that it was blinded but does not provide an adequate description of how this was achieved).

  • Studies in which double-blinding was not possible due to the comparator were considered to have high risk of bias.

• Blinding of outcome assessment (checking for possible detection bias). We assessed the methods used to blind study participants and outcome assessors from knowledge of which intervention a participant received. We assessed the methods as being at:

  • low risk of bias (the study has a clear statement that outcome assessors were unaware of treatment allocation, and ideally describes how this was achieved)

  • unclear risk of bias (the study states that outcome assessors were blind to treatment allocation but it lacks a clear statement on how this was achieved)

  • high risk of bias (the outcome assessment was not blinded)

• Selective reporting (checking for reporting bias). We assessed whether primary and secondary outcome measures were prespecified and whether these were consistent with those reported. We assessed the methods as being at:

  • low risk of bias (study protocol is available with prespecified measures)

  • unclear risk of bias (insufficient information available to permit a judgement of high or low risk of bias)

  • or high risk of bias [not all of the study’s prespecified primary outcomes have been reported; one or more primary outcomes have been reported using measurements, analysis methods or subsets of the data (e.g. subscales) that were not prespecified; one or more reported primary outcomes were not prespecified (unless clear justification for their reporting is provided, such as an unexpected adverse effect); one or more outcomes of interest in the review have been reported incompletely so that they cannot be entered in a meta-analysis; the study report failed to include results for a key outcome that would be expected to have been reported for such a study]

• Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data). We assessed the methods used to deal with incomplete data as being at:

  • low risk of bias (no missing outcome data; reasons for missing outcome data are unlikely to be related to the true outcome; missing outcome data are balanced in numbers across intervention groups, with similar reasons for missing data across groups; missing data have been imputed using BOCF analysis)

  • unclear risk of bias [insufficient reporting of attrition/exclusions to permit a judgement of low or high risk of bias (e.g. number randomised not stated; no reasons for missing data provided; or the study did not address this outcome)]

  • high risk of bias (the reason for missing outcome data is likely to be related to true outcome, with either imbalance in numbers or reasons for missing data across intervention groups; ‘as-treated’ analysis was done with substantial departure of the intervention received from that assigned at randomisation; potentially inappropriate application of simple imputation; use of ‘last observation carried forward’ (LOCF) without the addition of any other low risk of bias methods)

• Other bias. We assessed any other potential sources of bias that were not included in the other domains.

We considered studies to be at high risk of bias overall if they met the criteria for high risk of bias in any of the above domains.

Measures of treatment effect

For the outcomes measuring continuous data (pain intensity, mood, physical function, sleep, quality of life and PGIC continuous), data were reported as either post-intervention scores (the mean scores at the end of the intervention period) or change scores (mean change from baseline score). We conducted separate analyses for these. As is common in pain management studies, for all outcomes (apart from PGIC) a broad range of scales were used to measure the outcomes. Therefore, once data were extracted, they were converted into standardised mean difference (SMD) with 95% confidence intervals (CIs). We interpreted SMD as small (0.2), moderate (0.5) and large (0.8), in line with Cohen82 and the Cochrane Handbook. 76 For outcomes with dichotomous data (substantial pain relief, adverse events, moderate pain relief, PGIC much/very much improved, serious adverse events and withdrawal), we used odds ratios (ORs) with 95% CIs.

Unit of analysis issues

For most RCTs, we did not encounter any unit of analysis complexities as trial participants were randomised to different study arms, allowing direct analysis. For crossover RCTs, if the results for the first period (prior to crossover) were reported, we extracted these in an attempt to avoid crossover effects. If the results from the first period were not reported then we extracted the final trial results, provided there was a sufficient washout period of at least five times the length of the antidepressant half-life (minimum washout period length calculated separately for each antidepressant). The majority of crossover studies reported the combined effects of both periods (only one study reported first-period and second-period effects separately); therefore, we analysed crossover trials using these combined effects. Our search did not return any cluster RCTs that met our inclusion criteria.

Dealing with missing data

For all missing study-level statistical data relevant to our outcomes, we first tried to contact the authors of the study. If we could not get the data from the authors, then we followed the guidance from the Cochrane Handbook. 76 If standard deviations were missing, then we used the Review Manager calculator to calculate these from other data reported in the study. We did not impute any data, but assessed each study’s risk of bias due to missing data.

Assessment of heterogeneity

We assessed heterogeneity within the NMAs using the Tau statistic, in line with the guidance in the Cochrane Handbook. 76 We assessed heterogeneity using Confidence in Network Meta-Analysis (CINeMA) software, which calculated the chi-squared test and the I² statistic for each pairwise comparison on each outcome. As outlined in the Cochrane Handbook, we interpreted the I² statistic as follows:76

• 0–40%: might not be important

• 30–50%: may represent moderate heterogeneity

• 50–90%: may represent substantial heterogeneity

• 75–100%: considerable heterogeneity.

We took into account the magnitude and strength of effects when assessing heterogeneity.

Assessment of the transitivity assumption

We carefully scrutinised transitivity, which is the key underlying assumption of NMA. Transitivity requires studies to be similar on average across all factors that might alter treatment effects other than the intervention comparison being made. 76 To address this, we only included studies with similar clinical populations (i.e. participants reporting pain lasting at least 3 months). 83 Previous research, combined with review authors’ clinical experience and knowledge, identified variables that could potentially influence our primary outcome:

• pain condition

• age

• pain intensity at baseline

• depressive severity at baseline

• treatment duration

• dosing schedule.

We explored the impact of these factors by assessing the indirectness of the network. The inclusion of placebo and concerns about its potential to violate the transitivity assumption have been highlighted in general,84 and particularly in depression studies. 85 Therefore, we compared placebo-controlled studies with those that provided head-to-head evidence as a form of validation of the network.

Assessment of reporting biases

We assessed reporting biases using the Cochrane ‘risk of bias’ tool version 1.0 in Review Manager 5.481 by checking for study protocols and prespecified outcomes (as detailed in Assessment of risk of bias section). We also used funnel plots for pairwise analyses for antidepressants where more than 10 studies were available, as advised in the Cochrane Handbook. 76 Funnel plots were drawn using the ‘Risk Of Bias due to Missing Evidence in Network meta-analysis’ (ROB-MEN) tool, which is part of CINeMA, and used to assess the significant small study effects via funnel plot asymmetry.

Subgroup analysis and investigation of heterogeneity

Where data allowed, we performed subgroup analyses for the class of antidepressant and the type of pain condition. We used a Bayesian random-effects NMA to account for expected heterogeneity and variation in the data. These methods allowed the uncertainty inherent in the between-study variance component to be reflected in effect estimate precision. We performed these subgroup analyses by building separate models; however, this was dependent on the geometry and connectedness of the networks.

Due to sparsity of data, we were unable to perform subgroup analyses on the aim of the trial (whether the trial targeted pain or mood) or on baseline levels of mood. Upon examination, the average scores for the five most commonly used scales for mood (Beck Depression Inventory, Brief Pain Inventory Mood Item, SF-36 Mental Component Score, SF-36 Mental Health Subscale, and Hamilton Depression Rating Scale) were all in the none/minimal ranges for depression.

Sensitivity analysis

Analysis by risk of bias judgement (high and not high) was only possible for substantial pain relief. We were unable to perform sensitivity analyses for any outcome comparing active placebo to inert placebo, as in total only nine studies used an active placebo.

Results of the search

We ran the original search on 6 May 2020, and the top-up search on 4 January 2022. Both searches searched six databases and www.clinicaltrials.gov. The original search returned 21,569 records, and the top-up search returned 1814 records for a total of 23,383. After removing duplicates, we screened 16,569 records at title and abstract. From this, we excluded 15,738 records, leaving 831 records at full text. After full-text screening, we included 176 studies. The study flow diagram is presented in Figure 1.

FIGURE 1.

Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA) flow diagram.

Included studies

In total, we included 176 studies in the review, with a total of 28,664 adult participants with a mean age of 50.6 years. A table of included studies is provided in Appendix 4.

There were a variety of study designs across trials:

• antidepressant versus placebo: 83 (e.g. Hudson)96

• antidepressant versus active comparator: 22 (e.g. Enomoto)97

• antidepressant versus the same antidepressant at different doses versus placebo: 17 (e.g. Arnold)98

• antidepressant versus active comparator versus combined antidepressant + active comparator: 13 (e.g. Ang)99

• antidepressant versus active comparator versus placebo: 9 (e.g. Rowbotham)100

• antidepressant versus different antidepressant: 9 (e.g. Kaur)101

• antidepressant versus active comparator versus combined antidepressant + active comparator versus placebo: 8 (e.g. Gilron)102

• antidepressant versus different antidepressant versus placebo: 7 (e.g. Heymann)103

• antidepressant versus different antidepressant versus active comparator: 4 (e.g. Boyle)104

• antidepressant versus the same antidepressant at different doses: 2 (e.g. Chappell)105

• antidepressant versus same antidepressant at different doses versus different antidepressant at different doses versus placebo: 1106

• antidepressant versus different antidepressant versus combined antidepressants versus placebo: 1107

Most studies had a parallel-arm design (141 studies) compared to a crossover design (35 studies).

Studies mainly included participants with only one type of chronic pain:

• 59 studies included fibromyalgia.

• 49 studies included neuropathic pain.

• 40 studies included musculoskeletal pain.

• 9 studies included primary pain syndromes (not including fibromyalgia) for example described only as ‘somatoform’ or ‘idiopathic’ pain.

• 6 studies included gastrointestinal pain.

• 4 studies included non-cardiac chest pain.

• 2 studies included burning mouth syndrome.

• 2 studies included visceral pain.

• 1 study included atypical facial pain.

• 1 study included phantom limb pain.

• 1 study included pelvic pain.

Most studies were funded by pharmaceutical companies:

• 72 studies were fully funded by pharmaceutical companies.

• 5 were partially funded by pharmaceutical companies.

• 67 studies were funded through non-pharmaceutical means, mainly government, charity or institutional funding.

• 32 studies did not report the source of funding.

Most studies had a primary aim of reducing pain:

• 144 studies had a primary aim of reducing pain.

• 2 studies had a primary aim of treating depression.

• 6 studies had a primary aim of treating both depression and pain.

• 14 studies had other primary aims (e.g. sleep, other symptoms).

Studies ranged in length from 2 weeks to 9 months, with an average length of 10 weeks. Only six studies followed up with participants after the trial finished. 108–113 The follow-up time points ranged from 4 weeks post trial to 1 year post trial. Seven studies, with a total of 156 participants, provided no useable data and were therefore omitted from the NMAs. 106,114–119

Of the 176 studies and 28,664 participants, the numbers of participants receiving each antidepressant (not including combined interventions) were as follows:

• amitriptyline: 1843 (43 studies)

• bupropion: 54 (1 study)

• citalopram: 97 (5 studies)

• clomipramine: 124 (2 studies)

• desipramine: 336 (7 studies)

• desvenlafaxine: 884 (2 studies)

• dothiepin: 55 (3 studies)

• doxepin: 30 (2 studies)

• duloxetine: 6362 (43 studies)

• escitalopram: 93 (3 studies)

• esreboxetine: 978 (2 studies)

• fluoxetine: 277 (11 studies)

• imipramine: 300 (7 studies)

• maprotiline: 135 (4 studies)

• mianserin: 107 (2 studies)

• milnacipran: 3110 (18 studies)

• mirtazapine: 255 (2 studies)

• moclobemide: 42 (1 study)

• nortriptyline: 374 (7 studies)

• paroxetine: 422 (9 studies)

• pirlindole: 50 (1 study)

• reboxetine: 18 (1 study)

• sertraline: 91 (3 studies)

• trazodone: 63 (3 studies)

• trimipramine: 18 (1 study)

• venlafaxine: 489 (8 studies)

• zimeldine: 10 (1 study)

In total, 9854 participants received a placebo across 130 studies.

Risk of bias in included studies

Risk of bias findings from the included studies by domain are shown in Figure 2. To see risk of bias findings by study, please see the full Cochrane Review (www.cochranelibrary.com/cdsr/doi/10.1002/14651858.CD014682.pub2/full#CD014682-fig-0003). Overall, we rated 116 of 176 studies as ‘high risk’ and 60 as ‘not high risk’. However, of the 60 studies not rated as high risk, 29 had three or more domains rated as ‘unclear’.

FIGURE 2.

Risk of bias of included studies by domain.

Allocation

We did not assess any studies as at high risk of bias for sequence generation or allocation concealment. For sequence generation, we judged 95 studies to be of low risk, and 81 studies were judged as unclear. For allocation concealment, we judged 75 studies to have satisfactory procedures and rated them as low risk, and the other 101 studies were rated as unclear. We rated only 64 studies as at low risk of bias for both sequence generation and allocation concealment.

Blinding

For this review, we required studies comparing antidepressants with other antidepressants, different doses of the same antidepressant, or other pharmacological interventions to be double-blind. We accepted that some interventions could not be blinded by their nature (e.g. psychological therapy, physiotherapy). These studies were included but judged to be at high risk of bias for both blinding of participants and blinding of outcomes assessors. Seventeen studies were of non-pharmacological interventions and therefore rated as at high risk of bias for both domains. As this review is focused on pain, all outcomes were self-reported by participants, and therefore judgements were often the same for both domains. In total, we rated 106 studies as at low risk for both domains and 49 studies as unclear for both domains. Low risk of bias was achieved in studies by study drugs appearing identical, having matched/sham dosing schedules across all arms, and using active placebos that mimic the side effects of antidepressants.

Incomplete outcome data

We rated the majority of studies as at high risk of bias for incomplete outcome data; 102 studies were high risk. Studies were high risk primarily due to only using the LOCF imputation method, reporting data only on participants who completed the trial, or having significantly unequal attrition across arms. We rated 37 studies as at low risk of bias; these studies either had no/very little attrition, or used appropriate imputation methods such as BOCF or multiple imputation. We rated 37 studies as unclear due to them not clearly specifying missing data methods.

Selective reporting

We could not find protocols or trial registrations for the majority of studies. We rated 108 studies as having an unclear risk of bias, due to missing protocols or trial registrations being published retrospectively, after the study had begun. We rated 44 studies as at low risk of bias; outcomes and analyses in the published papers matched prospective protocols or registrations. We rated 24 studies as at high risk of bias. Four of these studies were never published in journal articles, and data were extracted from trial registries. 112,120–122 For the other studies rated as at high risk of bias, there were discrepancies between the protocols and published papers that were judged to result in a significant risk of bias (e.g. protocol stated that outcomes would be collected that were not reported).

Other potential sources of bias

We did not identify any other sources of bias for 145 studies. We rated 17 studies as having an unclear risk of bias, primarily due to data not being presented in numerical form or being reported by a different method to that in the protocol (e.g. percentage change rather than post intervention). We rated 14 studies as at high risk of bias for the following reasons:

• no published, peer-reviewed articles112,120–122

• washout periods and tapering issues102,123

• poor reporting with mistakes in article124

• insufficient power125

• significant differences at baseline126

• selection bias prior to participation36

• significant differences between published article and trial registry127,128

• using a potential intervention as a placebo. 113

We found some evidence of publication bias in one analysis (duloxetine vs. placebo for substantial pain relief), as identified from funnel plots (used to assess small study effects as a proxy for publication bias).

Overview

The following sections detail the results of the NMAs for all outcomes included in the review. Due to the scale of the analysis, we only include studies of antidepressants with ≥ 200 participants in the write-ups and Summary of findings tables. Each outcome has a table listing all the interventions included in the NMA. Antidepressant studies with < 200 participants, and non-antidepressant interventions, are also included in figures for completeness and context.

For all outcomes, we made decisions on which networks to report in this results section. For all outcomes, we considered treatment and treatment–dose networks. For continuous outcomes, we considered both change scores and post-intervention scores networks. For each outcome, we have reported the most robust and reliable network. The details of these decisions are reported in Appendix 2. The networks that we have not reported in this manuscript are available in Report Supplementary Material 1.

The sections are reported in order of primary and secondary outcomes (Tables 2–13).

Primary outcomes:

• substantial pain relief

• pain intensity

• mood

• adverse events.

Secondary outcomes:

• moderate pain relief

• physical function

• sleep

• quality of life

• PGIC: proportion of participants reporting much/very much improved, and continuous scores

• serious adverse events

• withdrawal.

Primary outcomes

Substantial pain relief (50% reduction)

Results

We report the treatment–dose network for substantial pain relief, as it was the model with the least heterogeneity and had no evidence of inconsistency.

We included 42 RCTs with a total of 14,626 participants (range in study from 47 to 1108). There were 25 different interventions, and some comparisons were informed only by direct evidence from one trial. We could not include data from two trials due to disconnected networks.

The antidepressants with ≥ 200 participants and therefore included in the summary are as follows:

• desvenlafaxine high dose

• duloxetine low dose

• duloxetine standard dose

• duloxetine high dose

• esreboxetine standard dose

• esreboxetine high dose

• milnacipran standard dose

• milnacipran high dose

• mirtazapine standard dose.

An overview of all interventions included in the analysis, the number of RCTs, and the number of participants is given in Appendix 3, Table 15.

There were no concerns regarding model fit based on residual deviance and convergence diagnostics. The network diagram is presented in Figure 3 and the forest plot in Figure 4.

FIGURE 3.

Substantial pain relief: network plot.

FIGURE 4.

Substantial pain relief: summary forest plot (log OR with CrIs).

Duloxetine standard dose and duloxetine high dose were the highest-ranked antidepressants for substantial pain relief, and equally efficacious in comparison to placebo (OR 1.91, 95% CI 1.69 to 2.17 and OR 1.91, 95% CI 1.66 to 2.21, respectively). Milnacipran high dose (OR 1.64, 95% CI 1.04 to 2.58) and esreboxetine standard dose (OR 1.72, 95% CI 1.13 to 2.62) were also equally ranked, but less effective than duloxetine standard dose and duloxetine high dose. Mirtazapine standard dose, esreboxetine high dose and desvenlafaxine high dose showed no significant difference in comparison to placebo.

A visual representation of the cumulative rankings for every treatment included in the analysis did not substantially alter the interpretation of relative effects or mean rank CrIs. The UME model had similar DICs to the dose treatment model, with no evidence of inconsistency in the dev-dev plot. We confirmed this with node-splitting models for all nine comparisons where it was possible to compare direct and indirect evidence. The comparison of pregabalin with placebo had the smallest Bayesian p-value (p = 0.3) indicative of inconsistency where direct evidence suggests underestimation of the effect of pregabalin based on a single trial. These figures are available in Report Supplementary Material 1. The availability of a consistent evidence network precluded the need for exploration of transitivity violations.

Exploration of heterogeneity

Despite the risk of overfitting, we summarise results for multiple models because of the importance of substantial pain as an outcome for patients, clinicians and overall quality of life. The full results of all models are reported in Report Supplementary Material 1.

Class

We generated a network by aggregating treatment into classes. The analysis included four antidepressant classes: SNRI, TCA, TeCA and NaSSA; however, we could not draw any reliable conclusions about class differences due to inconsistency and overlapping CrIs.

Condition

Trials reporting substantial pain included neuropathic, fibromyalgia, musculoskeletal, primary and gastrointestinal pain conditions. However, only neuropathic and fibromyalgia pain conditions had connected networks. We could not derive reliable treatment rankings for neuropathic pain, as the UME models and node-splitting indicated inconsistency. For fibromyalgia, although the network geometry precluded analysis of inconsistency, esreboxetine, milnacipran and duloxetine were relatively equally ranked: esreboxetine (mean rank = 2.02, 97.5% CrI 1 to 4); milnacipran (mean rank = 2.30, 97.5% CrI 1 to 4); duloxetine (mean rank = 2.48, 97.5% CrI 1 to 4).

Risk of bias

We conducted a sensitivity analysis to explore the effect of removing high-risk-of-bias studies. We rated 15 studies as having low risk of bias. The model of the resulting network was unstable with divergent transitions indicating problems with model convergence. UME models and the dev-dev plot did not identify inconsistency, but we could not confirm this by node-splitting due to network geometry. Results were consistent with the treatment–dose model. The two best-ranked antidepressants were esreboxetine (mean rank = 3.73. 97.5% CrI 2 to 7) and duloxetine (mean rank = 4.64, 97.5% CrI 3 to 6).

Confidence in network meta-analysis

In addition to fitting multiple models to explore heterogeneity and utilising UME and node-splitting models to explore inconsistency, we undertook further analysis of pairwise direct evidence and network evidence (excluding multiarm trials of dose) to facilitate strength of evidence assessment using CINeMA.

The design-by-treatment test showed no inconsistency between direct and indirect evidence (χ² = 14.069, p = 0.296), although duloxetine low dose and desvenlafaxine high dose had high I² values (73.6% and 65.8%), indicating heterogeneity. We rated duloxetine low, standard and high doses as moderate certainty. We rated all other antidepressant doses as low, or very low certainty primarily due to major concerns regarding high-risk-of-bias studies, imprecision (estimates crossing zero), and a small number of RCTs and participants contributing to the estimates.

Pain intensity

Results

For pain intensity, we report the change score treatment–dose network, as it was more robust than the other networks with low heterogeneity and no indications of inconsistency.

We included 49 RCTs with a total of 14,504 participants (range 26–1191). We removed one study from this analysis due to implausible results. 129 Of these, 28 studies compared against placebo, 9 were trials with a head-to-head comparison versus another active comparator and 12 were dose-comparison trials. There were 21 different interventions, and some comparisons were informed only by direct evidence from one trial.

The antidepressants with ≥ 200 participants and therefore included in the summary are as follows:

• duloxetine low dose

• duloxetine standard dose

• duloxetine high dose

• milnacipran standard dose

• milnacipran high dose.

An overview of all interventions included in the analysis, the number of RCTs and the number of participants is given in Appendix 3, Table 16.

There were no concerns regarding model fit. The network diagram is presented in Figure 5 and the forest plot in Figure 6.

FIGURE 5.

Pain intensity: network diagram.

FIGURE 6.

Pain intensity: summary forest plot (SMD with CrIs).

Ranking of antidepressants

Duloxetine high and standard dose were the highest-ranked antidepressants for pain intensity, with small to moderate effects (SMD −0.37, 95% CI −0.45 to −0.28 and SMD −0.31, 95% CI −0.39 to −0.24 respectively). Milnacipran high and standard doses had a small effect (SMD −0.22, 95% CI −0.40 to −0.05). Duloxetine low dose showed no significant difference in comparison to placebo.

A visual representation of the cumulative rankings for every intervention included in the analysis did not alter interpretation. The UME model had similar DICs to the dose treatment model, with no evidence of inconsistency. We confirmed this with node-splitting models for all nine comparisons where it was possible to compare direct and indirect evidence. The lowest Bayesian p-value was for the comparison of duloxetine standard dose versus duloxetine high dose (p = 0.08). These figures are available in Report Supplementary Material 1.

Condition and risk of bias

We were unable to undertake further NMAs of condition or risk of bias due to small sample sizes, network geometry and the risk of overfitting, but these were examined in pairwise analyses and network analysis (excluding multidose arms) in CINeMA to inform strength of evidence assessment.

Confidence in network meta-analysis

The design-by-treatment test showed no inconsistency between direct and indirect evidence (χ² = 8.34, p = 0.82), although duloxetine standard dose and milnacipran standard dose had high I² values (65.3% and 67.7%), indicating heterogeneity. We had moderate certainty in the estimates for duloxetine low and standard and milnacipran standard doses. We rated all other antidepressant doses as low certainty due to major concerns regarding high-risk-of-bias studies and imprecision (estimates crossing zero).

Mood

Results

For mood, we report the change score treatment network as this was the most robust and reliable network, with low heterogeneity and no indications of inconsistency.

We included 38 RCTs with a total of 12,985 participants (range 42–1191). Of these, 22 trials compared against placebo only, 6 were multiarm trials with another active comparator, 9 were comparing the same antidepressant in different doses, and 1 compared two antidepressants together. There were 16 different interventions, and some comparisons were informed only by direct evidence from one trial. We rated 23 trials as having a high risk of bias. We could not include data from one trial due to disconnected networks.

The antidepressants with ≥ 200 participants and therefore included in the summary are:

• duloxetine

• milnacipran

• mirtazapine.

An overview of all interventions included in the analysis, the number of RCTs, and the number of participants is given in Appendix 3, Table 17.

At baseline, the average scores for the five most commonly used scales (Beck Depression Inventory, Brief Pain Inventory Mood Item, SF-36 Mental Component Score, SF-36 Mental Health Subscale, and Hamilton Depression Rating Scale) were all in the none/minimal ranges.

There were no concerns regarding model fit. The network diagram is presented in Figure 7 and the forest plot is presented in Figure 8.

FIGURE 7.

Mood: network plot.

FIGURE 8.

Mood: summary forest plot (SMD with CrIs).

Ranking of antidepressants

Mirtazapine was the highest-ranked antidepressant for mood with a moderate effect (SMD −0.5, 95% CI −0.78 to −0.22), based on one RCT. Duloxetine and milnacipran were equally ranked. Duloxetine showed very small effects (SMD −0.16, 95% CI −0.22 to −0.1), and milnacipran showed no difference in comparison to placebo.

A visual representation of the cumulative rankings for every intervention included in the analysis did not alter interpretation of the results. This figure is available in Report Supplementary Material 1. The UME model had similar DICs to the dose treatment model, with no evidence of inconsistency.

Class, condition and risk of bias

We did not undertake further analyses because of small sample sizes, network geometry and the risk of overfitting, but pairwise and NMA (excluding multidose trials) were performed in CINeMA to inform strength of evidence assessment.

Confidence in network meta-analysis

The design-by-treatment test showed no evidence of inconsistency (χ² = 1.83, p = 0.4), and all I² values were below 40%, despite the analysis being unable to run node-splitting. Both duloxetine and milnacipran were rated as having moderate-certainty evidence; there were no domains indicating major concern. We rated mirtazapine as having low-certainty evidence as the estimates were formed from only one trial.

Adverse events

Results

For adverse events, we report the treatment–dose network. There were similar levels of heterogeneity and inconsistency across networks but we were able to run node-splitting models for treatment–dose.

We included 93 RCTs with a total of 22,558 participants. Of all the studies in the network, 47 trials compared antidepressants only against placebo, 27 were multiarm trials with another active comparator, 15 were dose-comparison trials, and 4 compared two antidepressants to each other. We rated 62 trials as having a high risk of bias. There were 60 different interventions, and some comparisons were informed only by direct evidence from one trial. We could not include data from one trial due to disconnected networks.

The antidepressants with ≥ 200 participants and therefore included in the summary are as follows:

• amitriptyline standard dose

• desvenlafaxine high dose

• duloxetine high dose

• duloxetine low dose

• duloxetine standard dose

• esreboxetine standard dose

• milnacipran high dose

• milnacipran standard dose

• mirtazapine standard dose.

An overview of all interventions included in the analysis, the number of RCTs, and the number of participants is given in Appendix 3, Table 18.

There were no concerns regarding model fit. The network diagram is presented in Figure 9, the forest plot of all interventions is presented in Figure 10 and the forest plot of antidepressants only is presented in Figure 11.

FIGURE 9.

Adverse events: network plot.

FIGURE 10.

Adverse events: summary forest plot (log OR with CrIs).

FIGURE 11.

Adverse events (antidepressants only): summary forest plot.

Ranking of antidepressants

Data for adverse events were sparse, and studies were underpowered. All antidepressants with over 200 participants in the antidepressant arm were closely ranked. Desvenlafaxine and mirtazapine were the highest-ranked antidepressants, with no significant difference compared to placebo (OR 1.67, 95% CI 0.92 to 2.41 and OR 1.70, 95% CI 0.48 to 2.91, respectively). The evidence for both of these antidepressant doses was based on only two studies each. Duloxetine standard dose, milnacipran standard dose and duloxetine high dose were equally ranked. Duloxetine low dose, milnacipran high dose, amitriptyline standard dose and esreboxetine standard dose were the lowest-ranked antidepressants, with all ORs > 2.

A visual representation of the cumulative rankings for every intervention included in the analysis did not alter interpretation. We further investigated inconsistency through UME models and node-splitting models for all 30 comparisons where it was possible to compare direct and indirect evidence. There was evidence of inconsistency in UME but not node-splitting models. These figures are available in Report Supplementary Material 1. However, multiple divergent transition warnings indicate the potential for inconsistency to be poorly estimated in the latter models.

Class, condition and risk of bias

Our overall model of adverse events is problematic due to divergent transitions, low effective sample sizes and inconsistency in the UME model. We were unable to undertake further exploration of class, condition and risk of bias given the high uncertainty in overall effects.

Confidence in network meta-analysis

We were unable to use CINeMA for this outcome due to the complexity of the network. Therefore, two authors (HB and GS) made the judgements based on GRADE and CINeMA domains and the available results. We judged all antidepressants and doses as very low confidence, primarily due to concerns with within-study bias, and imprecision in the network.

Secondary outcomes

Moderate pain relief

Results

For moderate pain relief, we report the treatment network as this model had low heterogeneity and no evidence of inconsistency.

We included 40 RCTs with a total of 14,208 participants (range 37–1025). Of these, 20 trials compared against placebo, 8 were multiarm trials with another active comparator, 11 were dose-comparison trials, and 1 study compared two antidepressants head to head. There were 17 different interventions, and some comparisons were informed only by direct evidence from one trial. We rated 25 studies as at high risk of bias.

The antidepressants with ≥ 200 participants and therefore included in the summary are:

• duloxetine

• esreboxetine

• milnacipran

• mirtazapine.

An overview of all interventions included in the analysis, the number of RCTs, and the number of participants is given in Appendix 3, Table 19.

There were no concerns regarding model fit. The network diagram is presented in Figure 12 and the forest plot is presented in Figure 13.

FIGURE 12.

Moderate pain relief: network plot.

FIGURE 13.

Moderate pain relief: summary forest plot (log OR with CrIs).

Ranking of antidepressants

All antidepressants with over 200 participants in the antidepressant arm showed an effect for moderate pain relief and were very closely ranked. Mirtazapine was the highest-ranked antidepressant (OR 1.92, 95% CI 1.45 to 2.39), followed by duloxetine (OR 1.79, 95% CI 1.67 to 1.91), milnacipran (OR 1.7, 95% CI 1.48 to 1.92) and esreboxetine (OR 1.65, 95% CI 1.32 to 1.98).

A visual representation of the cumulative rankings for every intervention included in the analysis did not alter interpretation. The UME model showed no evidence of inconsistency. We confirmed this with node-splitting models for all nine comparisons where it was possible to compare direct and indirect evidence. The comparison of duloxetine and placebo had the lowest Bayesian p-value (p = 0.18) with indirect evidence indicative of a larger effect than direct evidence. These figures are available in Report Supplementary Material 1.

Exploration of heterogeneity

We also explored the impact of including dose in the model. There was low heterogeneity (Tau = 0.11), and while there was no evidence of inconsistency in UME and node-splitting models, there were several divergent transitions. The analysis showed similar rankings of antidepressants to the treatment-only model, with mirtazapine, duloxetine and milnacipran remaining the highest-ranked drugs across doses. The full results of all the analyses are reported in Report Supplementary Material 1.

Class

There were three classes included in the treatment-only analysis: NaSSA, SNRI and TCA. Only the NaSSA and SNRI classes had over 200 participants in the analyses. SNRI was the highest-ranked class (logOR 0.56, CrI 0.45 to 0.60), followed by NaSSA (logOR 0.67, CrI 0.11 to 1.23).

Condition and risk of bias

We were unable to undertake further NMAs due to small sample size, network geometry and risk of overfitting, but pairwise and NMA excluding multidose trials were undertaken to inform strength of evidence assessment using CINeMA.

Confidence in network meta-analysis

The design-by-treatment test showed no evidence of inconsistency between the direct and indirect evidence in the network (χ² = 2.65, p = 0.62), and only esreboxetine had an I² value of above 40% (44.6%). We rated duloxetine and milnacipran as having moderate certainty in the results, while we downgraded mirtazapine and esreboxetine due to low numbers of studies and participants.

Physical function

Results

For physical function, we report the change score treatment–dose network as it had lower heterogeneity than other models and no inconsistency.

We included 32 RCTs with a total of 11,760 participants (range 42–1025). Of these, 20 trials compared against placebo, 4 were head-to-head trials with another active comparator, 7 were dose-comparison trials, and 1 was a direct head-to-head comparison between two different antidepressants. There were 18 different interventions, and some comparisons were informed only by direct evidence from one trial. We rated 21 studies as at high risk of bias.

The antidepressants with ≥ 200 participants and therefore included in the summary are:

• duloxetine high dose

• duloxetine standard dose

• milnacipran high dose

• milnacipran standard dose

• mirtazapine standard dose.

An overview of all interventions included in the analysis, the number of RCTs, and the number of participants is given in Appendix 3, Table 20.

There were no concerns regarding model fit. The network diagram is presented in Figure 14 and the forest plot of placebo comparisons in Figure 15.

FIGURE 14.

Physical function: network plot.

FIGURE 15.

Physical function: summary forest plot (SMD with CrIs).

Ranking of antidepressants

Duloxetine standard dose (SMD −0.24, 95% CI −0.32 to −0.18), duloxetine high dose (SMD −0.23, 95% CI 0.30 to 0.16) and milnacipran standard dose (SMD −0.18, 95% CI −0.30 to −0.07) were the highest-ranked antidepressants, with small effects. Duloxetine standard dose and duloxetine high doses were equally effective. Milnacipran high dose showed no significant difference compared to placebo (SMD −0.10, 95% CI −0.22 to 0.07). Mirtazapine standard dose was the lowest-ranked antidepressant (SMD 0.62, 95% CI 0.11 to 0.69).

A visual representation of the cumulative rankings for every intervention included in the analysis did not alter interpretation. We performed node-splitting models for all four comparisons where it was possible to compare direct and indirect evidence (see Figure 26). The lowest Bayesian p-value was for the comparison of duloxetine high dose versus placebo, where direct evidence showed a larger effect than indirect evidence (p = 0.07). These figures are available in Report Supplementary Material 1.

Class

Four classes of antidepressants were included in the analysis (SNRI, SSRI, TCA and NaSSA); however, due to interventions including combinations of drugs, models including class could not be analysed.

Condition and risk of bias

We were unable to undertake further NMAs due to small sample sizes, network geometry and the risk of overfitting.

Confidence in network meta-analysis

The design-by-treatment test showed no evidence of inconsistency between the direct and indirect evidence (χ² = 6.45, p = 0.69), and no antidepressant had an I² value of over 40%, although values could not be generated for mirtazapine. We rated duloxetine and milnacipran as moderate certainty, downgraded only due to some concerns with within-study bias. We downgraded esreboxetine and mirtazapine further to low certainty due to the small number of studies and participants included in the analyses.

Sleep

Results

For sleep, we report the change score treatment–dose network as this was the most robust and reliable model.

We included 18 RCTs with a total of 6301 participants (range 42–1195). Of these, 12 studies compared against placebo and 6 were dose-comparison studies. There were eight different interventions, and some comparisons were informed only by direct evidence from one trial. We rated nine trials as at high risk of bias overall.

The antidepressants with ≥ 200 participants and therefore included in the summary are as follows:

• duloxetine standard dose

• duloxetine high dose

• milnacipran standard dose

• milnacipran high dose.

An overview of all interventions included in the analysis, the number of RCTs and the number of participants is given in Appendix 3, Table 21.

There were no concerns regarding model fit. The network diagram is presented in Figure 16 and the forest plot for placebo comparison is presented in Figure 17.

FIGURE 16.

Sleep: network plot.

Ranking of antidepressants

Duloxetine standard and high doses were the highest-ranked antidepressants and the only antidepressants to show a significant effect when compared to placebo, although the effects were small (standard dose: SMD −0.21, 95% CI −0.30 to −0.12; high dose: SMD −0.14, 95% CI −0.27 to −0.01). Milnacipran standard dose (SMD −0.06, 95% CI −0.30 to 0.17) and high dose (SMD −0.03, 95% CI −0.29 to 0.20) showed no significant difference in comparison to placebo.

A visual representation of the cumulative rankings for every intervention included in the analysis did not alter interpretations. Node-splitting models had divergent transitions and indicated inconsistency for the comparison of high- and standard-dose duloxetine (p = 0.02). We therefore downgraded the strength of evidence for the high-dose duloxetine estimate. These figures are available in Report Supplementary Material 1.

Class, condition and risk of bias

Although there were two different classes in the network (SNRI and SSRI), SSRI was only represented by one study using citalopram with 21 participants; therefore, only SNRI crossed the threshold of 200 participants. We did not explore condition and risk of bias further using NMA because of concerns about sample size, network geometry and the risk of overfitting.

Confidence in network meta-analysis

The design-by-treatment test showed no evidence of inconsistency between the direct and indirect evidence in the network (χ² = 7.39, p = 0.4), despite the concerns identified in node-splitting models. No antidepressants had I² values of above 40%, although values could not be calculated for milnacipran high or standard doses. We rated only duloxetine as moderate certainty, downgraded from high due to some concerns about within-study bias and inconsistency from the NMA. We rated duloxetine high dose, milnacipran high dose and milnacipran standard dose as having a very low certainty of evidence. We downgraded duloxetine high dose due to major concerns regarding within-study bias and incoherence. We downgraded milnacipran standard and high doses due to major concerns regarding within-study bias, and some concerns regarding imprecision, heterogeneity and inconsistency. Of note, both milnacipran dose analyses were informed by the same study.

Quality of life

Results

For quality of life, we report the post-intervention treatment network, as this was the network with the lowest heterogeneity.

We included 19 RCTs with a total of 3103 participants (range 30–998). Of these, 5 studies compared against placebo, 11 were multiarm trials with another active comparator, 2 were direct head-to-head comparisons of different antidepressants and 1 was a dose-comparison trial. There were 23 different interventions, and some comparisons were informed only by direct evidence from one trial. Data from one study could not be included due to disconnected networks. We rated 13 studies as at high risk of bias overall.

The antidepressants with ≥ 200 participants and therefore included in the summary are as follows:

• duloxetine

• esreboxetine.

An overview of all interventions included in the analysis, the number of RCTs, and the number of participants is given in Appendix 3, Table 22.

There were no concerns regarding model fit. The network diagram is presented in Figure 18 and the forest plot is presented in Figure 19.

FIGURE 17.

Sleep: summary forest plot (SMD with CrIs).

FIGURE 18.

Quality of life: network plot.

FIGURE 19.

Quality of life: summary forest plot (SMD with CrIs).

Ranking of antidepressants

Neither esreboxetine or duloxetine showed a significant difference compared to placebo for quality of life (SMD −0.30, 95% CI −1.24 to 0.64 and SMD 0.02, 95% CI −0.56 to 0.58, respectively).

A visual representation of the cumulative rankings for every intervention included in the analysis did not alter interpretations. Node-splitting models were undertaken for all 13 comparisons where it was possible to compare direct and indirect evidence. The comparison with the lowest Bayesian p-value (p = 0.16) was for fluoxetine compared to amitriptyline. These figures are available in Report Supplementary Material 1. UME models also failed to identify inconsistency.

Exploration of heterogeneity

We explored models including both treatment and dose; this model had higher heterogeneity (Tau = 0.67) and similar residual deviance to that of the treatment-only model.

Class, condition and risk of bias

We were unable to generate meaningful networks including class, condition and risk of bias. Only one class had antidepressants with over 200 participants (SNRI). Small sample sizes, network geometry and the risk of overfitting precluded analyses of condition and risk and bias.

Confidence in network meta-analysis

The design-by-treatment test showed evidence of significant inconsistency between the direct and indirect evidence in the network (χ² = 80.27, p = 0.00) despite node-splitting and UME models indicating no concern. The I² value for duloxetine showed evidence of heterogeneity (I² = 67.2%) and could not be calculated for esreboxetine. Therefore, we rated duloxetine as having low certainty of evidence (downgraded due to within-study bias, heterogeneity and inconsistency) and esreboxetine as having very low certainty of evidence (downgraded due to within-study bias, inconsistency and low numbers of studies).

Patient Global Impression of Change (responders)

Results

For PGIC much/very much improved, we report the treatment–dose network as this had low heterogeneity with no inconsistency.

We included 12 RCTs with a total of 6995 participants (range 43–1025). Of these, eight studies compared against placebo and four were dose-comparison trials. There were nine different interventions, and some comparisons were informed only by direct evidence from one trial. We judged seven studies to be at high risk of bias.

The antidepressants with ≥ 200 participants and therefore included in the summary are:

• desvenlafaxine high dose

• duloxetine high dose

• duloxetine standard dose

• esreboxetine high dose

• esreboxetine standard dose

• milnacipran high dose

• milnacipran standard dose.

An overview of all interventions included in the analysis, the number of RCTs and the number of participants is given in Appendix 3, Table 24.

There were no concerns regarding model fit. The network diagram is presented in Figure 20 and the forest plot is presented in Figure 21.

FIGURE 20.

Patient Global Impression of Change much/very much improved: network plot.

Ranking of antidepressants

Duloxetine standard dose was the highest-ranked antidepressant for PGIC much and very much improved, with a large effect (OR 2.29, 95% CI 1.98 to 2.60). Duloxetine high dose (OR 2.03, 95% CI 1.62 to 2.44), milnacipran high dose (OR 1.99, 95% CI 1.77 to 2.21) and milnacipran standard dose (OR 1.95, 95% CI 1.73 to 2.17) were the next highest-ranked antidepressants. Both esreboxetine doses showed a smaller effect (standard: OR 1.79, 95% CI 1.44 to 2.14; high: OR 1.63, 95% CI 1.24 to 2.02) but were among the lowest-ranked antidepressants. Desvenlafaxine high dose showed no significant effects when compared to placebo (OR 1.01, 95% CI 0.58 to 1.44).

A visual representation of the SUCRA rankings for every intervention included in the analysis did not alter the interpretation. The UME model had no evidence of inconsistency. We were only able to compare direct and indirect evidence for milnacipran standard versus milnacipran high dose, with a Bayesian p-value of 0.66 indicative of no inconsistency. These figures are available in Report Supplementary Material 1.

Class, condition and risk of bias

We were unable to include class, condition and risk of bias in the models. For class, all the antidepressants included in the model were SNRIs. For condition and risk of bias, the sparse network geometry created disconnected networks with small sample sizes and high risk of overfitting.

Confidence in network meta-analysis

The design-by-treatment test showed no evidence of inconsistency (χ² = 0.35, p = 0.84), and no antidepressants had I² values of over 40%. We rated the majority of the evidence to be very low certainty, due to within-study bias and low study and participant numbers. We rated milnacipran high dose as low certainty, downgraded due to major concerns of within-study bias. We rated milnacipran and duloxetine standard dose as moderate certainty, only downgraded due to concerns about within-study bias.

Patient Global Impression of Change (continuous)

Results

For PGIC (continuous), we report the treatment–dose network as it had the lowest heterogeneity and the most clinical utility.

We included 24 RCTs with a total of 8415 participants (range 194–804). Of these, 12 studies compared against only placebo, 3 were multiarm trials with another active comparator, and 9 were dose-comparison trials. There were seven different interventions, and some comparisons were informed only by direct evidence from one study. We judged 15 studies as at high risk of bias overall.

The antidepressants with ≥ 200 participants and therefore included in the summary are:

• duloxetine low dose

• duloxetine standard dose

• duloxetine high dose.

An overview of all interventions included in the analysis, the number of RCTs and the number of participants is given in Appendix 3, Table 25.

There were no concerns regarding model fit. The network diagram is presented in Figure 22 and the forest plot of placebo comparisons is presented in Figure 23.

FIGURE 21.

Patient Global Impression of Change much/very much improved: summary forest plot (log OR with CrIs).

FIGURE 22.

Patient Global Impression of Change (continuous): network plot.

FIGURE 23.

Patient Global Impression of Change (continuous): summary forest plot (SMD with CrIs).

Ranking of antidepressants

Duloxetine standard and high doses were the highest-ranked antidepressants, with a small to moderate effect (SMD −0.36, 95% CI −0.44 to −0.29 and SMD −0.33, 95% CI −0.40 to −0.26, respectively). Duloxetine low dose was the lowest-ranked antidepressant with a small effect (SMD −0.23, 95% CI −0.35 to −0.11).

A visual representation of the cumulative rankings for every intervention included in the analysis did not alter interpretations. Both UME and node-splitting models showed evidence of inconsistency. The highest Bayesian p-value (p = 0.03) suggested that direct evidence overestimated the effectiveness of high-dose duloxetine versus placebo compared to indirect evidence, resulting in the strength of evidence being downgraded. These figures are available in Report Supplementary Material 1.

Class, condition and risk of bias

We were unable to run models including class, condition and risk of bias. We were unable to analyse class as there was only one class present in the network (SNRI). We were unable to analyse condition and risk of bias due to the high risk of overfitting.

Confidence in network meta-analysis

The design-by-treatment test showed no evidence of inconsistency between the direct and indirect evidence in the network (χ² = 14.98, p = 0.13), and no antidepressant had an I² value higher than 40%. We rated duloxetine standard and high doses as having moderate-certainty evidence as a result of incoherence. We downgraded duloxetine low dose to moderate certainty due to some concerns regarding within-study bias in addition to network inconsistency.

Serious adverse events

Results

For serious adverse events, we report the treatment–dose model. Both treatment and treatment–dose models had studies with high levels of imprecision, but treatment–dose was selected for reporting due to its clinical utility.

We included 70 RCTs with a total of 19,304 participants (range 26–1025). Of these, 39 studies compared against placebo, 12 compared against another active comparator, 15 were dose-comparison trials, and 4 studies compared two different antidepressants against each other. There were 31 different interventions, and some comparisons were informed only by direct evidence from one trial. We judged 45 studies as at high risk of bias. We could not include data from three studies due to disconnected networks.

The antidepressants with ≥ 200 participants and therefore included in the summary are as follows:

• desvenlafaxine high dose

• duloxetine high dose

• duloxetine low dose

• duloxetine standard dose

• esreboxetine high dose

• esreboxetine standard dose

• milnacipran high dose

• milnacipran standard dose

• milnacipran dose unable to be categorised

• mirtazapine standard dose.

An overview of all interventions included in the analysis, the number of RCTs and the number of participants is given in Appendix 3, Table 26.

There were no concerns regarding model fit. The network diagram is presented in Figure 24 and the forest plot of placebo comparisons is presented in Figure 25.

FIGURE 24.

Serious adverse events: network plot.

FIGURE 25.

Serious adverse events: summary forest plot (log OR with CrIs).

Ranking of antidepressants

Data for serious adverse events were very sparse, and studies were generally underpowered to detect rare events. No antidepressant showed any significant difference when compared with placebo, and the CIs were very wide.

We undertook a visual representation of the cumulative rankings for every intervention included in the analysis. The UME model had no evidence of inconsistency. We confirmed this with node-splitting models for all 16 comparisons where it was possible to compare direct and indirect evidence The lowest Bayesian p-value (p = 0.07) was for the comparison of pregabalin and low-dose duloxetine. These figures are available in Report Supplementary Material 1.

Class, condition and risk of bias

We were unable to undertake further analysis of class, condition or risk of bias in networks due to small sample sizes, network geometry and the risk of overfitting.

Confidence in network meta-analysis

We were unable to use CINeMA for this outcome due to the complexity of the network. Therefore, two review authors (HB and GS) made the judgements based on GRADE and CINeMA domains and the available results. We judged all antidepressants and doses as very low confidence, primarily due to concerns with within-study bias, heterogeneity and imprecision in the network.

Withdrawal

Results

For withdrawal, we report the treatment network. Although this model has high heterogeneity, we determined that including dose would increase the network complexity to a point where analysis would be infeasible.

We included 152 RCTs with a total of 28,120 participants (range 24–1025). Of these, 73 studies compared against placebo, 47 were multiarm trials with another active comparator, 18 were dose-comparison trials and 14 were head-to-head trials comparing two different antidepressants. There were 77 different interventions, and some comparisons were informed only by direct evidence from one trial. We rated 106 studies as at high risk of bias. We could not include data from two studies due to disconnected networks.

The antidepressants with ≥ 200 participants and therefore included in the summary are:

• amitriptyline

• desipramine

• desvenlafaxine

• duloxetine

• esreboxetine

• imipramine

• milnacipran

• mirtazapine

• nortriptyline

• paroxetine

• venlafaxine.

An overview of all interventions included in the analysis, the number of RCTs and the number of participants is given in Appendix 3, Table 27.

There were no concerns regarding model fit. We present the network diagram in Figure 26 and the forest plot of placebo comparisons in Figure 27.

FIGURE 26.

Withdrawal: network plot.

FIGURE 27.

Withdrawal: summary forest plot (log OR with CrIs).

Ranking of antidepressants

Nortriptyline was the highest-ranked antidepressant. Nortriptyline, mirtazapine, amitriptyline, desvenlafaxine and venlafaxine all showed no significant difference compared to placebo for withdrawal. Duloxetine, milnacipran, esreboxetine, desipramine and paroxetine all showed significant effects, ranging from small to moderate.

A visual representation of the cumulative rankings for every intervention included in the analysis is available in Report Supplementary Material 1. We were unable to draw any very reliable conclusions due to all antidepressants having wide, overlapping CrIs.

Exploration of heterogeneity

Due to the complexity and geometry of the network, we were only able to examine models including class, and were unable to examine condition or risk of bias.

Class

Ten classes of antidepressant were included in the analysis: SNRI, SSRI, TCA, MAOI reversible, NARI, NaSSA, NDRI, SARI, TCA+SSRI and TeCA. There was slightly higher heterogeneity than the treatment-only model (Tau = 0.33), but no evidence of inconsistency in the UME models. Half of the classes had fewer than 200 participants, leaving SNRI, SSRI, TCA, NaSSA and TeCA with reliable sample sizes. The rankings of these classes are presented in Table 14.

TABLE 14 - Top-ranked antidepressant classes in withdrawal analysis

Class	Antidepressant	n	Mean rank	Credible intervals
				2.5%	97.5%
NaSSA	Mirtazapine	242	3.61	1	10
TCA	Amitriptyline Clomipramine Desipramine Dothiepin Doxepin Imipramine Nortriptyline	2593	4.33	2	7
SNRI	Duloxetine Esreboxetine Milnacipran Venlafaxine	7804	6.24	4	9
TeCA	Maprotiline Mianserin	207	6.96	2	11
SSRI	Citalopram Escitalopram Fluoxetine Paroxetine Sertraline Zimeldine	713	7.7	4	10

Confidence in network meta-analysis

We were unable to use CINeMA for this outcome due to the complexity of the network. Therefore, two review authors (HB and GS) made the judgements based on GRADE and CINeMA domains and the available results. We judged all antidepressants except duloxetine as very low certainty, primarily due to concerns with within-study bias, heterogeneity and imprecision in the network. We rated duloxetine as low certainty, as the only antidepressant without major concerns due to imprecision.

Overall

We report a NMA of 176 double-blind RCTs investigating antidepressants for chronic pain. Studies included 28,664 adult participants with a mean age of 50.6 years. The majority of studies investigated antidepressants from three classes: SNRI (74 studies), TCA (72 studies) and SSRI (34 studies). There was a variety of study designs; however, the majority of trials were placebo controlled (83 studies). The remainder compared an antidepressant against an active comparator with no placebo (22 studies), or compared two or more different doses of the same antidepressant with a placebo arm (17 studies). Most studies had a parallel-arm design (141 studies) compared to a crossover design (35 studies). Studies mainly included participants with only one type of chronic pain: 59 studies included participants with fibromyalgia, 49 neuropathic pain, 40 musculoskeletal pain and 26 included participants with other conditions (e.g. gastrointestinal, primary pain conditions, non-cardiac chest pain). Finally, 72 studies were fully funded by pharmaceutical companies, and 30 studies did not report the source of funding.

Seven studies, with a total of 156 participants, provided no useable data and were therefore omitted from the NMAs. At the time of the review, the majority of antidepressants are not licenced for use in chronic pain. Only amitriptyline and duloxetine are indicated for types of chronic pain in the British National Formulary: amitriptyline for neuropathic pain, and duloxetine for diabetic neuropathy. 41,130

The following results are based on NMA. One study131 reported the results separately according to the type of pain condition. This study was stratified into two to include the results for both conditions.

Primary efficacy outcomes

For the primary efficacy outcomes (substantial pain relief, pain intensity and mood), duloxetine was consistently the highest-ranked antidepressant that had data from over 200 participants in total across trials, and the only antidepressant with robust evidence that showed an effect with moderate-certainty evidence. For substantial pain and pain intensity, standard-dose duloxetine was equally as efficacious as high dose. For pain intensity and mood, milnacipran also showed reliable effectiveness, with moderate-certainty evidence. At a class level, SNRIs were the only class to have an effect with reliable evidence. For pain intensity, we removed one study that showed improbable effects from the data extracted from the published article. 129 We e-mailed the study authors for clarification but received no response.

Secondary efficacy outcomes

Across all the secondary efficacy outcomes (moderate pain relief, physical function, sleep, quality of life and PGIC) duloxetine and milnacipran were the highest-ranked and most trustworthy antidepressants, respectively. Very few other antidepressants had been studied in over 200 participants, and those that had been were ranked as having very low-certainty evidence. For both duloxetine and milnacipran, standard doses were equally as effective as high doses, although effects for both were small.

Safety

We extracted adverse event, serious adverse event, and withdrawal data from the studies included in the review. The data for these outcomes were poor. Although we have reported the ranking of antidepressants in the Summary of findings tables, the quality and certainty of this evidence for all antidepressants and doses is very low, and we cannot draw any reliable conclusions from the analyses.

Participants

The sample of participants in the included studies was mostly female (68.3%) and had a mean age of 50.6 years. Most studies had a minimum pain intensity inclusion criterion, with 92 studies requiring participants to score ≥ 4 on a 0–10 scale or equivalent at baseline, and most participants reported experiencing pain for over 1 year.

Our inclusion criteria for participants were strict, and we required the study population to have had pain for 3 months or longer. If this time frame was not explicitly reported by the study or required for a diagnosis of the pain condition, then the study was excluded. Therefore, we excluded six studies from our full-text screening with a study population described as having a ‘chronic’ pain condition without information regarding duration. This may mean that we excluded other relevant studies, but we believe the number of studies to be affected by this to be minimal.

Interventions

There were 89 different interventions included in the review, 26 of which were antidepressants. We included all interventions that matched the inclusion criteria regardless of dose, formulation and route of administration. Only four antidepressants were investigated in more than 10 studies. The only antidepressant that had robust studies and evidence is duloxetine, with 43 studies and a total of 11,608 participants randomised. Participants in duloxetine trials accounted for over one-third of all the participants included in this review. Milnacipran also showed some reliable evidence across outcomes, with 11 studies and a total of 5083 participants. Amitriptyline was investigated in 43 studies, with a total of 3372 participants, although the certainty of this evidence was very low, and only 3 studies randomised more than 200 participants. Fluoxetine was the fourth antidepressant to be included in more than 10 studies, but the quality and certainty of the evidence was very low, with 11 studies including 630 participants in total. All other antidepressants were included in fewer than 10 studies.

Study designs and comparisons

A variety of study designs were used by studies included in the review. Half the studies included in the review were two-arm, parallel designed trials comparing antidepressant to placebo (89 out of 176 studies). There were also dose-comparison trials, comparisons against active comparators, and combined antidepressant interventions (e.g. antidepressant + psychological therapy), and a number of studies included multiple types of these comparisons. Some of the combined antidepressant comparisons precluded full analysis in the NMA as we were unable to isolate the effects of the antidepressant alone. There were few head-to-head trials comparing two antidepressants with a placebo arm for reference.

The majority of studies provided useable data for the primary efficacy outcomes: 131 studies measured pain intensity, and 87 measured mood. Although these figures represent the majority of studies, it is evident that a large number of trials in chronic pain do not report these key outcomes. In the review, over half of trials did not measure mood, and almost one-third did not measure or report pain intensity. Despite the 2005 publication of the IMMPACT guidelines79 for core outcomes of chronic pain trials, only 44 and 43 studies reported the proportion of participants achieving 50% and 30% pain relief, respectively. For the secondary outcomes, around one-third of studies reported physical function, less than one-quarter reported sleep and only one-quarter reported quality of life.

All outcomes aside from withdrawal used self-reported measures. There was considerable heterogeneity in the outcome measures used across all outcomes such that SMD was required for the continuous outcomes. Additionally, studies reported a mix of change scores (change in outcome from baseline to post intervention) and post-intervention scores. As we had to use SMD, this meant that we could not build one NMA including all data for each outcome; rather, we were required to build both change score and post-intervention score models and subsequently decide which model to report for each outcome. Typically, larger, pharmaceutical-funded trials reported change scores, while smaller trials reported post-intervention scores. Future reviews would benefit from studies reporting both types of scores, so that results can be combined for a holistic evidence synthesis. We found that the data for the safety outcomes were particularly poor; adverse events were reported in various different ways across studies, and studies were often not powered adequately or had not lasted long enough to detect events.

Mood

As antidepressants are primarily designed and used to manage depression, and low mood is a common comorbidity with chronic pain, we planned to explore their impact upon mood in this analysis in several ways.

First, we planned to undertake a subgroup analysis exploring whether there were any differences in outcomes between studies reporting a primary aim of targeting pain and those reporting a main aim of targeting mood. We were unable to undertake this analysis as only two studies had a main aim of targeting mood. In contrast, 144 studies had a main aim of targeting pain.

Second, we planned to undertake analyses examining differences in outcomes for studies stratified by levels of depression at baseline (none, mild, moderate and severe as defined by the diagnostic tools used). The majority of studies excluded participants with diagnoses of major depressive disorder and other mental health conditions. Because of this, baseline measures of depression and/or anxiety failed to exceed average scores of mild depression at baseline.

As we were unable to undertake these analyses, we were unable to assess the effect of depression and mood on the outcomes of the NMA, and unable to draw any meaningful conclusions regarding the mood outcome.

Follow-up

We were only able to undertake analyses at the post-intervention time point because only a small number of studies had follow-up periods of any length (6/176 studies). Therefore, we were unable to draw any conclusions regarding the long-term efficacy and safety of using antidepressants for chronic pain.

Overall quality

We assessed the quality of the evidence using CINeMA (and ROB-MEN and GRADE where appropriate). Across the outcomes, the only antidepressant with consistently robust evidence was duloxetine, followed by milnacipran. All other antidepressants were judged as having low or very low certainty of evidence. The most common reasons for downgrading comparisons were within-study bias, imprecision in the NMA (wide CrIs), and small numbers of studies and participants. Additionally, all evidence for safety data was graded as very low due to heterogeneity, imprecision and sparsity of data.

Risk of bias

Overall, the risk of bias for included studies was relatively high. Using the Cochrane Risk of Bias Tool 1 resulted in 116 studies being defined as at high risk of bias overall. Evidence was often downgraded due to within-study bias across antidepressants and outcomes. There are several points relating to risk of bias to be discussed. The common method of deciding the overall rating of a study’s risk of bias stipulates that if any one domain is high risk, then the whole study is rated as at high risk of bias. As we included studies that compared antidepressants to other active comparators, this included interventions whose designs inherently require participants and trial staff to be unblinded (e.g. psychological therapies). To be consistent with other studies in the review, these trials have been rated as having a high risk of bias for the blinding domains, but it has been recognised previously that these domains are not appropriate for these interventions, and in previous reviews, these domains have been omitted. 77

Additionally, we found that a number of studies simply do not report the information required needed to make a judgement. Of the 60 studies rated as ‘not high’ risk of bias, over half had three or more domains judged as ‘unclear’. Therefore, this raises concerns as to the reporting quality of these trials, an ongoing problem in health research. 132 There are a number of clinical trial reporting guidelines available which these trials have not abided by, which suggests that some of the studies might have been rated as at high risk of bias if the correct information had been provided.

Heterogeneity

We found substantial heterogeneity in direct comparisons and entire networks across outcomes when lumping doses of each treatment together in the NMAs. Where this was evident, splitting treatments by dose removed heterogeneity for most outcomes. Therefore, most of the outcomes were analysed using a split dose model. Further exploration of heterogeneity by including antidepressant class and pain condition had to be balanced against the risk of overfitting multiple models. 91 The decision process for this is discussed within each outcome results section.

Imprecision

Imprecision was a problem across most of our NMAs. Of the 26 different antidepressants included in our review, only four were used in more than 10 studies. Although we included all treatments in each analysis, for each outcome we graded any antidepressants with fewer than 200 participants in the antidepressant arms as very low by default and excluded these from the written summaries and Summary of findings tables. The remaining networks were generally robust at a network level, but problems remained with network connectivity relying on single trials. Imprecision was a major problem for safety data, particularly adverse events and serious adverse events, meaning that we cannot be sure of the true effect for these outcomes.

Inconsistency

For each outcome, we used UME and node-splitting models to assess inconsistency in treatment and split treatment–dose networks and found no evidence of inconsistency for the primary outcomes. Therefore, we concluded that transitivity across sex, age and pain condition was valid in our models.

Publication bias

We used ROB-MEN133 to assess publication bias in the review. For the primary outcomes, we were only able to produce funnel plots for the duloxetine–placebo comparison as it was the only comparison with over 10 studies. These funnel plots showed some evidence of publication bias, and therefore the comparisons were rated as ‘some concerns’. As all other antidepressants tended to report small effects with small numbers of studies and participants, we judged all comparisons to have ‘some concerns’.

Potential biases in the review process

We minimised the potential for bias in the review process as much as possible. We published our protocol through the Cochrane Library and followed this for the review process. We had an extensive search strategy that included six databases and also searched clinical trial registries for unpublished and ongoing trials. The chance of a missed trial is minimal, and even more minimal is the chance of any missed trial having a substantial effect on the overall results.

Screening, data extraction and risk of bias assessments were completed in duplicate and independently by two researchers, with all disagreements resolved by discussion. Where possible, we contacted authors to request missing data, but the response rate from authors was low. Where the study had a clinical trial registry, we collected data that were not reported in the published paper from the results section of the registry.

We used CINeMA92 and ROB-MEN133 to assess our confidence in the results. The final interpretation and judgements were made by two review authors in discussion.

Implications for practice

Implications for policy-makers and guidelines

A full analysis of international guidelines is out of scope, but the NICE guidelines for the treatment of chronic primary pain recommend antidepressants as the only pharmacological treatment option. 30 In these guidelines, NICE specifically recommends amitriptyline, citalopram, duloxetine, fluoxetine, paroxetine or sertraline, with no recommendations regarding dose. Our review and analyses found moderate- to high-certainty evidence for only duloxetine in the management of chronic pain; evidence for amitriptyline, citalopram, fluoxetine, paroxetine or sertraline was of low quality and of very low certainty. Our findings challenge current guidelines on several grounds. They suggest that there is insufficient evidence for NICE guidelines to recommend amitriptyline on the same level as duloxetine. It is important to note that the issue is a lack of quality evidence for amitriptyline, not necessarily evidence showing an absence of benefit. Therefore, guideline recommendations could be improved by including an evidence-based ranked hierarchy rather than a broad recommendation of several interventions, some of which are only supported by weak evidence. This is already implemented elsewhere: the Japanese guidelines categorise their recommendations with the qualifications ‘weakly recommend’, ‘moderately recommend’ and ‘strongly recommend’ for amitriptyline and duloxetine for each pain condition. 29 A similar approach would be appropriate for NICE guidelines, particularly when considering the weak evidence for the other antidepressants (citalopram, fluoxetine, paroxetine, sertraline), all of which are currently recommended equally for chronic primary pain. Second, our analyses by pain condition demonstrate the effectiveness of duloxetine across three major groups of people with pain: fibromyalgia, musculoskeletal (low back pain and osteoarthritis), and neuropathic pain. It is therefore unclear why the recommendation of antidepressants varies across the NICE guidelines for these conditions. From our findings, duloxetine should be recommended for all of these conditions.

Implications for funders of the intervention

Currently, amitriptyline is the most common and first-line antidepressant prescribed for the management of chronic pain; however, there are no large high-quality trials to support this position. There is also a lack of head-to-head trials where multiple antidepressants are compared in the same trial. It is important to recognise that there are no long-term safety data available for any antidepressant used for chronic pain treatment, and that collection and reporting of such data during trials is essential.

Implications for research

Research participants

As this study was a systematic review, it did not recruit participants. We reviewed the equality, diversity and inclusion aspects of the trials in the review. Most studies were undertaken in Western populations, primarily USA and Western Europe, with the majority of participants being of white ethnicity. Furthermore, nearly all studies excluded participants with mental health comorbidities, including depression and anxiety. Therefore, the studies in this review do not reflect real-world settings. It is essential that future research in this area focuses on equality, diversity and inclusion principles, particularly the inclusion of participants of non-white ethnicities and with comorbidities.

Research team and wider involvement

The research team is a multidisciplinary team including psychologists, pain researchers, a psychiatrist, a pharmacist, an anaesthetist and statisticians, ranging from junior members (pre- and post-PhD research associates) to professors. The review was led by an early-career researcher (HB), and provided opportunities for development including training, gaining of new skills, conference attendance and presenting, and dissemination.

Equality, diversity and inclusion was championed in our PPI groups. We had representation from both men and women with a range of chronic pain conditions, a mix of younger and older adults, and members from both white and black ethnicities.

Strengths and limitations

This is the first and only full systematic review with NMA for all antidepressants in all chronic pain conditions. The strength of this review is in the design and methodology, which applied gold-standard guidance at all stages of the project. We believe our search was comprehensive, that we minimised human bias by using double extraction, and that we graded each trial on the quality of the methodology, therefore providing information on the certainty we can attach to each finding. We are also able to compare direct and indirect evidence for some antidepressants in some conditions.

The main limitation of this study is that we were unable to assess the harms associated with any antidepressant. None of the ways in which adverse events were measured in individual trials produced results that were interpretable in meta-analysis or NMA. The inconsistency and unreliability of adverse event reporting has been raised previously,139 and improvement is still needed. This is important to consider in relation to the recommendations for antidepressants given by guidelines; a judgement has to be made as to the balance between efficacy and potential adverse events.

A second limitation is that the majority of trials included in our analyses excluded people with diagnoses of depression, anxiety, and other mental health conditions. Across trials, the average scores at baseline on mood measures were all within the ‘normal’ or ‘subclinical’ range. These results may not therefore be representative of the large group of people who experience any mental health conditions alongside chronic pain.

Finally, as the average length of trials was only 11.5 weeks, there are no data on the longer-term efficacy of any antidepressants in the management of chronic pain. This is critical, as clinically patients with chronic pain usually use medicines for long periods of time to consistently manage their pain.

Networks: which model is the best fit?

Our primary analysis was a Bayesian NMA including treatment. This analysis had high heterogeneity (Tau² = 0.26) and inconsistency in both UME and node-splitting models. We also explored networks that separated treatments into different doses, conditions and risk of bias categories and aggregated treatment by class. These networks resulted in models that had similar heterogeneity and variable indications for inconsistency, but the model that included antidepressant dose reduced the estimate of heterogeneity by half (Tau² = 0.11) and there was no indication of inconsistency. Therefore, the results are based on the treatment–dose model.

Change scores and post-intervention scores

Studies in the review reported pain intensity results in two ways: change scores and post-intervention scores. A total of 50 studies with 14,926 participants reported change scores, while 74 studies with 7703 participants reported post-intervention scores. As these two types of scores cannot be combined directly, we selected model–data combinations on the basis of parsimony, minimisation of inconsistency (identified via UME and node-splitting models), residual deviance and heterogeneity (measured as Tau²) to minimise the risk of overfitting.

Networks: which model is the best fit?

For both change score and post-intervention analyses, we generated networks and models based on treatment and treatment dose.

Change scores and post-intervention scores

Studies in the review reported pain intensity results in two ways: change scores and post-intervention scores. A total of 38 studies with 12,985 participants reported change scores, while 46 studies with 3885 participants reported post-intervention scores. As these two types of scores cannot be combined, we reported the most appropriate and robust model for the data.

Networks: which model is the best fit?

For both change score and post-intervention analyses, the primary analysis was a Bayesian NMA including treatment.

Networks: which model is the best fit?

Our primary analysis was a Bayesian NMA including treatment. This analysis had high heterogeneity (Tau² = 0.49), with the UME model indicating high inconsistency and divergent transitions within the network. We were unable to run node-splitting models due to network geometry. Models including dose continued to have high heterogeneity (Tau² = 0.59), and the UME model showed high inconsistency, similar to the treatment-only model. There continued to be divergent transitions within the network and low effective sample sizes; however, the node-splitting models were able to run and showed no evidence of inconsistency. Due to the network geometry and inappropriateness of running extra models, no further analyses including other covariates were run. The results are based on the treatment–dose model, due to similar levels of heterogeneity and inconsistency, and the ability to run node-splitting models.

Networks: which model is the best fit?

Our primary analysis was a Bayesian NMA including treatment. This analysis had low heterogeneity (Tau² = 0.13) and no evidence of inconsistency in both UME and node-splitting models. Therefore, the results are based on a model including treatment only. Divergent transitions suggested unstable models when analysing treatment–dose networks.

Change scores and post-intervention scores

Studies in the review reported physical function results in two ways: change scores and post-intervention scores. A total of 32 studies with 11,760 participants reported change scores, while 30 studies with 3645 participants reported post-intervention scores. As these two types of scores cannot be combined, we reported the most appropriate and robust model for the data.

Networks: which model is the best fit?

For both change score and post-intervention score analyses, the primary analysis was a Bayesian NMA including treatment.

Change scores and post-intervention scores

Studies in the review reported sleep results in two ways: change scores and post-intervention scores. A total of 18 studies with 6301 participants reported change scores, while 18 studies with 1921 participants reported post-intervention scores. As these two types of scores cannot be combined, we reported the most appropriate and robust model for the data.

Networks: which model is the best fit?

For both change score and post-intervention score analyses, the primary analysis was a Bayesian NMA including treatment.

Model used

Comparing the post-intervention and change score analyses shows that the change score treatment network is more robust and reliable than the post-intervention network as models without divergent transitions were generated. Therefore, the results are based on a model of change scores including both treatment and dose. Results for the treatment-only model are available in the appendices.

Change scores and post-intervention scores

Studies in the review reported pain intensity results in two ways: change scores and post-intervention scores. A total of 27 studies with 9693 participants reported change scores, while 19 studies with 3103 participants reported post-intervention scores. As these two types of scores cannot be combined, we reported the most appropriate and robust model for the data.

Networks: which model is the best fit?

For both change score and post-intervention analyses, the primary analysis was a Bayesian NMA including treatment.

Model used

Comparing the post-intervention and change score analyses shows that the post-intervention score treatment network has lower heterogeneity than the change score treatment–dose network. Therefore, the results are based on a model of post-intervention scores including treatment. The results of the change score analyses are included in the appendices.

Patient Global Impression of Change (much/very much improved)

Patient Global Impression of Change (continuous)

Networks: which model is the best fit?

Our primary analysis was a Bayesian NMA including treatment. This analysis had low heterogeneity (Tau² = 0.13) and no inconsistency in both UME and node-splitting models. Including dose into the model did not alter the level of heterogeneity (Tau² = 0.16), and continued to have no inconsistency in the UME and node-splitting models. Both treatment-only and treatment–dose models had multiple studies with high residual deviance and imprecision. As both models were very similar, we decided to use the treatment–dose model due to clinical utility. The results for the treatment-only model are included in Report Supplementary Material 1.

Networks: which model is the best fit?

Our primary analysis was a Bayesian NMA including treatment. This analysis had high residual deviance and relatively high heterogeneity (Tau² = 0.23). We were unable to examine the model using node-splitting models due to the network geometry, as a large proportion of the model was formed of single study connections only. We decided to use this treatment model for the analysis despite the relatively high heterogeneity, as including dose or condition would increase network complexity and dilute already weakly informative edges.