Types of studies

We included randomised controlled trials (RCTs) with double‐blind assessment of outcomes reporting outcomes after eight weeks of treatment or longer. We required full journal publication, with the exception of extended abstracts with sufficient data for analysis and online clinical trial results summaries of otherwise unpublished clinical trials. We excluded short abstracts (usually meeting reports), non‐randomised studies, studies of experimental pain, case reports, and clinical observations.

Types of participants

Studies included participants aged 18 years and above, with fibromyalgia diagnosed using the 1990 or 2010 criteria (Wolfe 1990; Wolfe 2010), and with initial pain of at least moderate intensity.

Types of interventions

Gabapentin at any dose, by any route, administered for the relief of pain in fibromyalgia, and compared to placebo or any active comparator. We excluded studies that used gabapentin to treat pain resulting from the use of other drugs.

Types of outcome measures

We anticipated that studies would use a variety of outcome measures, with most studies using standard subjective scales (numerical rating scale (NRS) or 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 were 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 (PGIC; moderate);

4. very much improved on PGIC (substantial).

These outcomes differ from those used in most earlier reviews (Wiffen 2005), as they concentrate on dichotomous outcomes where pain ratings do not follow a normal (Gaussian) distribution. People with chronic pain desire high levels of pain relief, ideally more than 50%, and ideally leaving them with no worse than mild pain (Moore 2013a; O'Brien 2010).

Electronic searches

We searched the following databases, without language restrictions.

1. Cochrane Central Register of Controlled Trials (CENTRAL; via the Cochrane Register of Studies Online) to 24 May 2016.

2. MEDLINE (via Ovid) from 1946 to 24 May 2016.

3. Embase (via Ovid) from 1974 to 24 May 2016.

The individual search strategies for CENTRAL, MEDLINE, and Embase are shown in Appendix 4.

Searching other resources

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International Clinical Trials Registry Platform (apps.who.int/trialsearch/), to identify additional published or unpublished data.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

Selection of studies

In order to determine study eligibility, two authors (TC and PW) independently read the abstract of each study identified by the search. We eliminated studies that clearly did not satisfy the inclusion criteria, and obtained full‐text copies of the remaining study reports. TC and PW independently read these reports and reached agreement regarding inclusion by discussion. We did not anonymise the studies in any way before assessment. We have included a Preferred Reporting Items for Systematic Reviews and Meta‐Analyses (PRISMA) flow chart (Figure 2).

Figure 2

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Study flow diagram.

Data extraction and management

Two review authors (TC and PW) independently extracted the data using a standard form and confirmed agreement before entering the data 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), 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 (TC and PW) independently assessed the risk of bias for each included study, using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), and adapted from those used by the Cochrane Pregnancy and Childbirth Group. We resolved any disagreements by discussion. We assessed the following for each included study.

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

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 being at either low risk of bias (for example, telephone or central randomisation; consecutively numbered, sealed, opaque envelopes) or unclear risk of bias (when the method is not clearly stated). We excluded studies that did not conceal allocation and were therefore at high risk of bias (for example, an open list).

3. Blinding of participants, personnel, and outcome assessment (checking for possible performance and 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 either low risk of bias (authors state that it was blinded and describe the method used to achieve blinding, for example, identical tablets, matched in appearance and smell) or unclear risk of bias (authors state that it was blinded but do not provide an adequate description of how blinding was achieved). We excluded studies at high risk of bias that were not double‐blind.

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 being at low risk of bias (less than 10% of participants did not complete the study, or authors used 'baseline observation carried forward' analysis, or both), unclear risk of bias (used 'last observation carried forward' (LOCF) 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 used dichotomous data to calculate the risk ratio (RR) with 95% confidence interval (CIs) using a fixed‐effect model unless we found evidence of significant statistical heterogeneity (see Assessment of heterogeneity).

We calculated NNTs as the reciprocal of the absolute risk reduction (McQuay 1998). For unwanted effects, the NNT becomes the number needed to treat for an additional harmful outcome (NNTH) and is calculated in the same manner. Where the unwanted effect is less common with treatment than control, we used the term Number Needed to Treat to Prevent (NNTp).

We did not use continuous data in analyses because it is inappropriate where there is an underlying skewed distribution, as is usually the case with analgesic response.

Unit of analysis issues

We accepted randomisation to the 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 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 planned to deal with clinical heterogeneity by combining studies that examine similar conditions, and to assess statistical heterogeneity visually (L'Abbé 1987), and with the I² statistic. When the I² statistic value was greater than 50%, we would consider the possible reasons for this.

Assessment of reporting biases

The aim of this Cochrane 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 does not depend on what the authors of the original studies chose to report or not, though clearly difficulties would arise if included studies failed to report relevant dichotomous results.

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 in this condition; Moore 2008). In the event, this was not possible.

Data synthesis

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

We planned to analyse data in three tiers, according to outcome and freedom from known sources of bias.

1. The first tier would use 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 analysis 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 planned to report these top‐tier results first.

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

3. 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.

Subgroup analysis and investigation of heterogeneity

We did not plan to perform any subgroup analyses since the experience of previous reviews indicated that there would be too few data for any meaningful subgroup analysis.

Sensitivity analysis

We did not plan to perform any sensitivity analyses.