Types of studies

We included randomised controlled trials (RCTs) with double‐blind assessment of participant outcomes and a duration of eight weeks or longer. We required full journal publication, with the exception of online clinical trial results summaries of otherwise unpublished clinical trials, and abstracts with sufficient data for analysis.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.

Trials had to have at least 20 participants per treatment arm. This is based on growing evidence of bias in small studies (Dechartres 2013; Dechartres 2014; Moore 1998).

Types of participants

Studies included adult participants aged 18 years and above, with pain due to fibromyalgia, diagnosed using the 1990 or 2010 criteria (Wolfe 1990; Wolfe 2010).

Types of interventions

Pregabalin at any dose, by any route, administered for the relief of fibromyalgia pain, 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 a visual analogue scale (VAS) for pain intensity or pain relief, or both. We were particularly interested in 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:

1. at least 30% pain relief over baseline (moderate);

2. at least 50% pain relief over baseline (substantial);

3. much or very much improved on Patient Global Impression of Change scale (PGIC) (moderate);

4. very much improved on PGIC (substantial).

These outcomes are analytically relevant, concentrating as they do on dichotomous outcomes where pain responses do not follow a normal (Gaussian) distribution. They are also clinically relevant; people with chronic pain desire high levels of pain relief, ideally more than 50%, and ideally no worse than mild pain (Moore 2013a; O'Brien 2010).

Electronic searches

We searched the following databases, without language restrictions.

• Cochrane Central Register of Controlled Trials (CENTRAL, via the Cochrane Register of Studies Online database (CRSO)) to 16 March 2016.

• MEDLINE (via Ovid) from 1946 to 16 March 2016.

• EMBASE (via Ovid) from 1974 to 16 March 2016.

The search strategies for CENTRAL, MEDLINE, and EMBASE are in Appendix 2, Appendix 3, and Appendix 4.

Searching other resources

We reviewed the bibliographies of any RCTs identified and review articles, and searched clinical trial databases (ClinicalTrials.gov (ClinicalTrials.gov) and the World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (apps.who.int/trialsearch/)) to identify additional published or unpublished data. We did not contact investigators or study sponsors for this update.

Selection of studies

Two review authors read the abstract of each study identified by the search, eliminated studies that clearly did not satisfy the inclusion criteria, and obtained full copies of the remaining studies. The same review authors then independently read these studies to determine eligibility; any disagreements or uncertainty were settled by discussion, with a third review author if necessary. Studies were not anonymised in any way before assessment. We have included a Preferred Reporting Items for Systematic Reviews and Meta‐Analyses (PRISMA) flow chart (Figure 1).

Figure 1

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Study flow diagram.

Data extraction and management

Two review authors independently extracted data using a standard form and checked these for agreement before entry into Review Manager 5 (RevMan 2014), or any other analysis tool. We included information about the pain condition and number of participants treated, drug and dosing regimen, study design (placebo or active control, standard design or EERW), study duration and follow‐up, analgesic 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

We used the Oxford Quality Score as the basis for inclusion (Jadad 1996), limiting inclusion to studies that were randomised and double blind as a minimum.

Two review authors independently assessed risk of bias for each study, using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Chapter 8, Higgins 2011), and adapted from those used by the Cochrane Pregnancy and Childbirth Group, resolving any disagreements by discussion. We assessed the following for each study.

1. Random sequence generation (checking for possible selection bias). We assessed the method used to generate the allocation sequence as: low risk of bias (any truly random process, random number table; computer random number generator); unclear risk of bias (when the method used to generate the sequence is not clearly stated). We excluded studies that used a non‐random process (odd or even date of birth; hospital or clinic record number) and were therefore at a high risk of bias.

2. 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 (telephone or central randomisation; consecutively numbered, sealed, opaque envelopes); unclear risk of bias (when method not clearly stated). We excluded studies that did not conceal allocation and were therefore at a high risk of bias (open list).

3. Blinding of participants and personnel, and outcome assessment (checking for possible performance bias and detection bias). We assessed the methods used to blind study participants, personnel and outcome assessors from knowledge of which intervention a participant received. We assessed the methods as: low risk of bias (study stated that it was blinded and described the method used to achieve blinding, identical tablets, matched in appearance and smell); unclear risk of bias (study stated that it was blinded but did not provide an adequate description of how this was achieved). We excluded studies that were not double blind and therefore at a high risk of bias.

4. 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 of bias (fewer than 10% of participants did not complete the study or used 'baseline observation carried forward' analysis, or both); unclear risk of bias (used 'last observation carried forward' analysis); or high risk of bias (used 'completer' analysis).

5. 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); or high risk of bias (fewer than 50 participants per treatment arm).

Measures of treatment effect

We calculated NNTs as the reciprocal of the absolute risk reduction (McQuay 1998). For unwanted effects, the NNT becomes the number needed to harm (NNH) and is calculated in the same manner. We used dichotomous data to calculate risk ratio with 95% confidence intervals using a fixed‐effect model unless we found significant statistical heterogeneity (see below). We did not use continuous data in analyses.

We have used the following terms to describe adverse outcomes in terms of harm or prevention of harm.

• When significantly fewer adverse outcomes occurred with treatment than with control (placebo or active), we used the term 'number needed to treat to prevent' one event (NNTp).

• When significantly more adverse outcomes occurred with treatment compared with control (placebo or active), we used the term 'number needed to harm' (NNH).

Unit of analysis issues

We accepted randomisation to individual participant only. In the event of a study having more than one active treatment arm in which data were not combined for analysis, we planned to split the control treatment arm between active treatment arms.

Dealing with missing data

We have used intention‐to‐treat (ITT) analysis where the ITT population consists of participants who were randomised, took at least one dose of the assigned study medication, and provided at least one post‐baseline assessment. We assigned missing participants zero improvement wherever possible.

Assessment of heterogeneity

We dealt with clinical heterogeneity by combining studies that examined similar conditions. We assessed statistical heterogeneity visually (L'Abbé 1987), and by using the I² statistic. When the I² value was greater than 50%, we considered possible reasons for this for in studies of classic design.

Assessment of reporting biases

The aim of this review was to use dichotomous outcomes of known utility and of value to patients (Hoffman 2010; Moore 2010b; Moore 2010c; Moore 2010d; Moore 2013a). The review did not depend on what the authors of the original studies chose to report or not, though clearly difficulties would arise if studies failed to report relevant dichotomous results. We extracted and used continuous data, which probably reflect efficacy and utility poorly, where useful for illustrative purposes only.

We planned to assess 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 a NNT of 10 or higher) (Moore 2008), but this was not possible with low effect sizes.

Data synthesis

We planned to use a fixed‐effect model for meta‐analysis. We would have used a random‐effects model if we had found significant clinical heterogeneity and considered it appropriate to combine studies.

We analysed data for each painful condition in 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 last observation carried forward (LOCF) or other imputation method for dropouts, report an 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 2012a; Moore 2012b). We have reported these top‐tier results first.

• The second tier used data from at least 200 participants but where one or more of the first‐tier conditions above was not met (reporting at least 30% pain intensity reduction (or equivalent), 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 significant problems were expected because, for example, 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.

Subgroup analysis and investigation of heterogeneity

We did not plan subgroup analyses since our experience based on previous reviews indicates that there would be inadequate information for meaningful subgroup analysis beyond dose, for example information on age or severity of pain is not usually recorded separately.

Sensitivity analysis

We did not plan any sensitivity analysis.