Types of studies

We included studies if they were randomised or quasi‐randomised controlled trials (RCTs) following four weeks of treatment or longer. We enrolled studies with a parallel, cross‐over and enriched enrollment randomised withdrawal design. Trials should have at least 10 participants per treatment arm. We required full journal publication, with the exception of online clinical trial results summaries of otherwise unpublished clinical trials, and abstracts with sufficient data for analysis. We did not include short abstracts (usually meeting reports). We excluded studies that were non‐randomised, studies of experimental pain, case reports and clinical observations.

Types of participants

Studies included adult participants aged 18 years and above, diagnosed with fibromyalgia using the ACR 1990 classification criteria (Wolfe 1990), the ACR 2010 preliminary diagnostic criteria (Wolfe 2010), or the modified ACR 2010 preliminary diagnostic criteria (research criteria) ( Wolfe 2011).

Types of interventions

Antipsychotics at any dose, by any route, administered for the relief of fibromyalgia symptoms and compared to placebo or any active comparator.

Types of outcome measures

We anticipated that studies would use a variety of outcome measures, with the majority of studies using standard subjective scales (numerical rating scale or visual analogue scale) for pain intensity or pain relief, or both. We were particularly interested in the Initiative on Methods, Measurement, and Pain Assessment in Clinical Trials (IMMPACT) definitions for moderate and substantial benefit in chronic pain studies (Dworkin 2008). These are defined as at least 30% pain relief over baseline (moderate), at least 50% pain relief over baseline (substantial), much or very much improved on Patient Global Impression of Change (PGIC) (moderate), and very much improved on PGIC (substantial). These dichotomous outcomes should be used where pain responses do not follow a normal (Gaussian) distribution. Patients with chronic pain desire high levels of pain relief, ideally more than 50%, and with pain not worse than mild (Moore 2013a; O'Brien 2010).

We included a 'Summary of findings' table as per the guidelines given in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). The 'Summary of findings' table includes the primary outcomes as outlined below.

Electronic searches

We searched the following databases without language restrictions:

• Cochrane Central Register of Controlled Trials (CENTRAL 2016, Issue 4);

• MEDLINE via Ovid (1946 to 20 May, 2016);

• EMBASE via Ovid (1974 to 20 May, 2016).

See Appendix 2 for the MEDLINE search strategy, Appendix 3 for the CENTRAL search strategy and Appendix 4 for the EMBASE search strategy.

Searching other resources

We screened the bibliographies of identified randomised trials and relevant review articles for additional information. We also contacted the authors of RCTs with antipsychotics in fibromyalgia and known experts in the field for potential unpublished trials and data.

For ongoing studies, we searched clinical trial databases including ClinicalTrials.gov (https://clinicaltrials.gov/) and the World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) Search Portal (http://apps.who.int/trialsearch/). We contacted investigators or study sponsors for missing data.

Selection of studies

We determined eligibility by reading the abstract of each study identified by the search. We eliminated studies that did not satisfy the inclusion criteria, and obtained full copies of the remaining studies; two review authors (WH, BW) made the decisions. Both of them read these studies independently and reached agreement by discussion. We did not anonymise the studies in any way before assessment. We created a Preferred Reporting Items for Systematic Reviews and Meta‐Analyses (PRISMA) flow chart to illustrate our study selection process.

Data extraction and management

Two review authors (WH, NÜ) independently extracted data using a pre‐standardised data extraction form and checked for agreement before entering data into Cochrane's statistical software, Review Manager 2014. We included information about the study setting, demographic and clinical variables of the patients, number of participants treated, drug and dosing regimen, co‐medication, study design (placebo or active control), study duration and follow‐up, outcome measures and results, withdrawals and adverse events (participants experiencing any adverse event, or serious adverse event).

Assessment of risk of bias in included studies

Two authors (WH, NÜ) independently assessed risk of bias in included studies using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), with any disagreements resolved by discussion.

We assessed the following risks of bias for each study.

• Random sequence generation (checking for possible selection bias). We assessed the method used to generate the allocation sequence as: low risk of bias (i.e. any truly random process, for example random number table; computer random number generator); unclear risk of bias (when the method used to generate the sequence is not clearly stated); high risk of bias (e.g. allocation is generated in terms of odd or even numbers in the date of birth, date of hospital admission or hospital record number, as well as in the case of allocation by judgement of the physician, the patient’s wishes, results of a laboratory test or availability of the intervention).

• 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: low risk of bias (for example, telephone or central randomisation; consecutively numbered, sealed, opaque envelopes); unclear risk of bias (when the method is not clearly stated); high risk of bias (systematic selection bias if participants and investigators could possibly foresee allocations, for example due to the use of an openly available treatment plan (e.g. a list with randomly generated numbers); assignment envelopes were used without appropriate safeguards (e.g. if envelopes were unsealed, non‐opaque or not sequentially numbered).

• Blinding of participants and personnel/treatment providers (systematic performance bias). We assessed the methods used to blind participants and personnel/treatment providers from knowledge of which intervention a participant received. We assessed the methods as: low risk of bias (study states that it was blinded and describes the method used to achieve blinding, for example, identical tablets; matched in appearance and smell); unclear risk of bias (study states that it was blinded but does not provide an adequate description of how it was achieved); high risk (blinding of participants was not ensured, e.g. tablets different in form or taste).

• Blinding of outcome assessment (checking for possible detection bias). We assessed the methods used to blind study outcome assessors from knowledge of which intervention a participant received. We assessed the methods as: low risk of bias (study states that outcome assessor was not involved in treatment); unclear risk of bias (study states that the assessor was blinded but does not provide an adequate description of how it was achieved); high risk: data analysis was conduced by the investigators.

• 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: low risk (fewer than 10% of participants did not complete the study and/or used 'baseline observation carried forward' analysis); unclear risk of bias (used 'last observation carried forward' (LOCF) analysis); high risk of bias (used 'completer' analysis).

• Reporting bias due to selective outcome reporting (reporting bias). We checked if an a priori study protocol was available and if all outcomes in the study protocol were reported in the publications of the study. There is low risk of reporting bias if the study protocol is available and all of the study's prespecified (primary and secondary) outcomes that are of interest in the review have been reported in the prespecified way, or if the study protocol is not available but it is clear that the published reports contain all expected outcomes, including those that were prespecified (convincing text of this nature may be uncommon). There is a high risk of reporting bias if not all of the study’s prespecified primary outcomes have been reported; one or more primary outcomes is reported using measurements, analysis methods or subsets of the data (for example 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 are reported incompletely so that they cannot be entered in a meta‐analysis; the study report fails to include results for a key outcome that would be expected to have been reported for such a study.

• Group similarity at baseline (selection bias). We assessed similarity of the study groups at baseline for the most important prognostic clinical and demographic indicators. There is low risk of bias if groups are similar at baseline for demographic factors, value of main outcome measure(s) and important prognostic factors. There is an unclear risk of bias if baseline for demographic factors, value of main outcome measure(s), and important prognostic factors are not or incompletely reported. There is high risk of bias if groups are not similar at baseline for demographic factors, value of main outcome measure(s) and important prognostic factors.

• Size of study (checking for possible biases confounded by small size). We assessed studies as being at low risk of bias (200 participants or more per treatment arm); unclear risk of bias (50 to 199 participants per treatment arm); high risk of bias (fewer than 50 participants per treatment arm).

We defined studies with 0 to 2 unclear or high risks of bias to be high quality studies, with 3 to 5 unclear or high risks of bias to be moderate quality studies, and with 6 to 8 unclear or high risks of bias to be low quality studies (Häuser 2015b).

Measures of treatment effect

We calculated numbers needed to treat for an additional benefit (NNTB) as the reciprocal of the absolute risk reduction (ARR) (McQuay 1998). For unwanted effects, the NNTB becomes the number needed to treat for an additional harm (NNTH) and is calculated in the same manner. For dichotomous data we calculated risk differences (RRD) (method inverse variance) with 95% confidence intervals (CIs) using a random‐effects model because we found clinical heterogeneity (different numbers of patients with major depressive disorder in both placebo‐controlled studies) (Assessment of heterogeneity). We set the threshold for a clinically relevant benefit or a clinically relevant harm for categorical variables as a NNTB or NNTH of less than 10 (Moore 2008). For continuous data we calculated standardised mean differences (SMDs) with 95% confidence intervals (CIs) using a random‐effects model because we found clinical heterogeneity (different numbers of patients with major depressive disorder in both placebo‐controlled studies). We used Cohen's categories to evaluate the magnitude of the effect size, calculated by SMD, with Hedges' g of 0.2 = small, 0.5 = medium and 0.8 = large (Cohen 1988). We labelled g < 0.2 to be a 'not substantial' effect size. We assumed a minimally important difference if Hedges' g was ≥ 0.2 (Fayers 2014). We calculated the numbers needed to treat for an additional outcome of benefit (NNTB) for continuous variables (sleep problems, depression) using the Wells calculator software available at the Cochrane Musculoskeletal Group editorial office, which estimates the proportion of patients who will benefit from treatment from SMDs. The estimation of responders is nearly independent from the minimally important difference (MID) (Norman 2001). We used a minimal clinically important difference of 15% for the calculation of NNTB from SMDs for all continuous outcomes.

Unit of analysis issues

We split the control treatment arm between active treatment arms in a single study if the active treatment arms were not combined for analysis. We included one study with a cross‐over design because separated data from the two periods were reported.

Dealing with missing data

Where means or standard deviations (SDs) were missing, we attempted to obtain these data through contacting trial authors. Where SDs were not available from trial authors, we calculated them from t‐values, CIs or standard errors, where reported in articles (Higgins 2011). Where 30% and 50% pain reduction rates and 14% FIQ improvement rates were not reported and not provided on request, we calculated them from means and SDs by a validated imputation method (Furukawa 2005).

Assessment of heterogeneity

We dealt with clinical heterogeneity from combining studies by analysing the inclusion and exclusion criteria of the studies included. We assessed statistical heterogeneity visually (L'Abbé 1987), and with the use of the I² statistic. When I² was greater than 50%, we considered the possible reasons.

Assessment of reporting biases

We assessed publication bias using a method designed to detect the amount of unpublished data with a null effect required to make any result clinically irrelevant (usually taken to mean an NNTB of 10 or higher) (Moore 2008).

Data synthesis

We used a random‐effects model for meta‐analysis because there was significant clinical heterogeneity due to different numbers of patients with major depression in both placebo‐controlled studies.

We analysed data in the following three tiers according to outcome and freedom from known sources of bias.

• The first tier used data meeting current best standards, where studies report the outcome of at least 50% pain intensity reduction over baseline (or its equivalent), without the use of LOCF or other imputation method for drop‐outs, report an intention‐to‐treat (ITT) analysis, last eight or more weeks, have a parallel‐group design, and have at least 200 participants (preferably at least 400) in the comparison (Moore 1998; Moore 2010a; Moore 2012). We reported these top‐tier results first.

• The second tier used data from at least 200 participants but where one or more of the above conditions was not met (for example, reporting at least 30% pain intensity reduction, using LOCF or a completer analysis, or lasting four to eight weeks).

• The third tier of evidence related to data from fewer than 200 participants, or where there were expected to be significant problems because, for example, of very short duration studies of less than four weeks, where there was major heterogeneity between studies, or where there were shortcomings in allocation concealment, attrition or incomplete outcome data. For this third tier of evidence, no data synthesis is reasonable, and may be misleading, but an indication of beneficial effects might be possible.

We employed the Grading of Recommendations, Assessment, Development and Evaluation (GRADE) approach (Guyatt 2011 a) to interpret findings (Langendam 2013), and the GRADE profiler (GRADEpro GDT 2015) allowed us to import data from Review Manager 5.3 (Review Manager 2014) to create 'Summary of findings' tables. These tables provide outcome‐specific information concerning the overall quality of evidence from studies included in the comparison, the magnitude of effect of the interventions examined and the sum of available data on the outcomes we considered. The GRADE approach defines the quality of the evidence as the extent of confidence in the estimates of treatment benefits and their safety. We made quality ratings separately for each of the 12 outcomes. We downgraded the quality of evidence from 'high quality' by one level for each of the following factors encountered (Guyatt 2011 b; Häuser 2015b):

• Limitations of study design: more than 50% of participants were from low quality studies as defined by the 'Risk of bias' tool.

• Inconsistency of results: the I² value was above 50%.

• Indirectness: we assessed whether the question being addressed by the systematic review diverged from the available evidence, in terms of the population in routine clinical care, if exclusion of patients with clinically relevant somatic disease and/or major mental disorders in the included studies resulted in ≥ 50% of the total patient collective of the systematic review coming from studies in which patients with relevant somatic disease and/or major mental disorders were excluded.

• Imprecision: there was only one trial or where there was more than one trial, the total number was fewer than 400 patients.

• Publication bias: all studies were initiated and funded by the manufacturer of the drug.

We categorised the quality of evidence as follows (Guyatt 2011 a):

• High (++++): we are very confident that the true effect lies close to that of the estimate of the effect.

• Moderate (+++): we are moderately confident in the effect estimate; the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different.

• Low (++): our confidence in the effect estimate is limited; the true effect may be substantially different from the estimate of the effect.

• Very low (+): we have very little confidence in the effect estimate; the true effect is likely to be substantially different from the estimate of effect; any estimate of effect is very uncertain.

Subgroup analysis and investigation of heterogeneity

We planned to pursue subgroup analyses (studies with and without stratifying for comorbid mental disorders; different antipsychotics) if there were at least two studies available.

Sensitivity analysis

We did not plan to conduct any sensitivity analysis because the evidence base was known to be too small to allow reliable analysis.