Types of studies

We will include randomised controlled trials (RCTs) with double‐blind assessment of participant outcomes following four weeks of treatment or longer. We will include trials with a parallel, cross‐over, and enriched enrolment randomised withdrawal design. We will not include N‐of‐1 studies. We require full journal publication, with the exception of online clinical trial results, summaries of otherwise unpublished clinical trials, and abstracts with sufficient data for analysis.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 will not include short abstracts (usually meeting reports). We will exclude studies that are non‐randomised, studies of experimental pain, case reports, and clinical observations.

Types of participants

Studies should include 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 2011a).

Types of interventions

Mirtazapine 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 anticipate that studies will use a variety of outcome measures, with the majority using standard subjective scales (numerical rating scale or visual analogue scale) for pain intensity or pain relief, or both. We are 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. People 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).

Electronic searches

We will search the following databases from inception and without language restrictions.

• Cochrane Central Register of Controlled Trials (CENTRAL via Cochrane Register of Studies Online).

• MEDLINE (via Ovid).

• Embase (via OVID).

• Scopus (via Ovid).

The search strategy for MEDLINE is shown in Appendix 2. We will adapt the MEDLINE search strategy for CENTRAL, Embase and Scopus.

Searching other resources

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 We will search the following clinical trial databases to identify additional published or unpublished data: ClinicalTrials.gov and World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (apps.who.int/trialsearch/).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

Selection of studies

We will determine eligibility by reading the abstract of each study identified by the search. We will eliminate studies that clearly do not satisfy the inclusion criteria, and obtain full copies of the remaining studies. Two review authors (WH, PW) will make the decisions. Two review authors (WH, PW) will read these studies independently and reach agreement by discussion. We will not anonymise the studies in any way before assessment. We will create a PRISMA flow chart.

Data extraction and management

Two review authors (WH, RAM) will extract data independently using a standard form and check for agreement before entry into Review Manager 5 (RevMan 2014), or any other analysis tool. We will include information about the study setting, demographic and clinical variables of the participants, number of participants treated, drug and dosing regimen, co‐medication, study design (placebo or active control; parallel, cross‐over, or enriched enrolment randomised withdrawal), 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

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

Two review authors (WH, RAM) will independently assess risk of bias for each study, using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), and adapted from those used by Cochrane Pregnancy and Childbirth, with any disagreements resolved by discussion. We will assess the following for each study.

1. Random sequence generation (checking for possible selection bias). We will assess 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). We will exclude studies at a 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 will assess the methods as: low risk of bias (for example, telephone or central randomisation; consecutively numbered, sealed, opaque envelopes); unclear risk of bias (when method not clearly stated). We will exclude studies that do not conceal allocation and are therefore at a high risk of bias (for example, open list).

3. Blinding of participants and personnel (checking for possible detection bias). We will assess the methods used to blind study participants and outcome assessors from knowledge of which intervention a participant received. We will assess the methods as: low risk of bias (e.g. 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). We will exclude studies at a high risk of bias where participants and study personnel were not blinded.

4. Blinding of outcome assessment (checking for possible detection bias). We will assess the methods used to blind study outcome assessors from knowledge of which intervention a participant received. We will assess 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 of bias (outcome assessors not blinded to treatment).

5. Incomplete outcome data (checking for possible attrition bias due to the amount, nature, and handling of incomplete outcome data). We will assess the methods used to deal with incomplete data as: low risk of bias (i.e. less 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).

6. Reporting bias due to selective outcome reporting (reporting bias). We will check if an a priori study protocol was available and if all outcomes of the study protocol were reported in the publications of the study. We will assess the methods used to deal with incomplete data as: low risk of reporting bias if the study protocol was available and all of the study’s prespecified (primary and secondary) outcomes that were of interest in the review were reported in the prespecified way, or if the study protocol was not available but it was clear that the published reports included all expected outcomes, including those that were prespecified (convincing text of this nature may be uncommon); high risk of reporting bias if not all of the study’s prespecified primary outcomes were reported; one or more primary outcomes was 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 was provided, such as an unexpected adverse effect); one or more outcomes of interest in the review were reported incompletely so that they could not be entered in a meta‐analysis; the study report did not include results for a key outcome that would be expected to have been reported for such a study. We will assess the methods as unclear risk of bias if insufficient information is available to permit judgement of ‘low risk’ or ‘high risk’.

7. Size of study (checking for possible biases confounded by small size). We will assess studies as being at low risk of bias (when there are 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).

8. Group similarity at baseline (selection bias). We will assess similarity of the study groups at baseline for the most important prognostic clinical and demographic indicators. We will assign a low risk of bias if groups were similar at baseline for demographic factors, value of main outcome measure(s) and important prognostic factors. We will assign as unclear risk of bias if important prognostic clinical and demographic indicators were not reported. There was high risk of bias if groups were not similar at baseline for demographic factors, value of main outcome measure(s), and important prognostic factor.

Two review authors (WH, PW) will make quality ratings separately for each of the eight methodology quality indicators as defined by the ’Risk of bias’ tool. We will define a study to be of high quality if six to eight of the domains are of low risk of bias, to be of moderate quality if three to five of eight domains are of low risk of bias, and to be of low quality if zero to two of eight domains are of low risk of bias (Schaefert 2015).

Measures of treatment effect

We will calculate NNTBs as the reciprocal of the absolute risk reduction (ARR; McQuay 1998). For unwanted effects, the NNTB becomes the number number needed to treat for an additional harmful outcome (NNTH) and is calculated in the same manner.

We will use the following terms to describe adverse outcomes in terms of harm or prevention of harm.

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

• When significantly more adverse outcomes occur with treatment compared with control (placebo or active), we will use the term: 'number needed to treat for an additional harmful outcome (NNTH)'.

For dichotomous data we will calculate risk differences (RDs) (inverse variance method) with 95% confidence intervals (CIs) using a fixed‐effect model unless significant statistical heterogeneity is found (see below). We will set the threshold for a clinically‐relevant benefit for categorical variables as a NNTB of less than 10 (Moore 2008).

For continuous data we will calculate standardised mean differences (SMDs) with 95% CIs using a fixed‐effect model unless significant statistical heterogeneity is found. We will use 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 will label g < 0.2 to be a 'not substantial' effect size. We will assume a minimally important difference if Hedges' g was ≥ 0.2 Fayers 2014). We will calculate the number needed to treat for an additional beneficial outcome (NNTB) for continuous variables (sleep problems, depression) using the Wells calculator software available at Cochrane Musculoskeletal editorial office, which estimates from SMDs the proportion of patients who will benefit from treatment. We will use a minimal clinically important difference of 20% for the calculation of NNTB from SMDs for all continuous outcomes.

Unit of analysis issues

We will split the control treatment arm between active treatment arms in a single study if the active treatment arms are not combined for analysis.

We will include studies with a cross‐over design where separate data from the two periods are reported, where data are presented that exclude a statistically significant carry‐over effect, or where statistical adjustments are carried out in the event of a significant carry‐over effect.

Dealing with missing data

We will use 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. Missing participants will be assigned zero improvement wherever possible. Where standard deviations (SDs) are not reported, we will calculate them from t‐values, CIs or standard errors, where reported in articles (Higgins 2011). Where 30% and 50% pain relief rates and 20% FIQ improvement rates are not reported and not provided on request, we will calculate them from means and SDs by a validated imputation method (Furukawa 2005).

Assessment of heterogeneity

We will deal with clinical heterogeneity by combining studies that examine similar conditions. We will assess statistical heterogeneity visually (L'Abbé 1987), and with the use of the I² statistic. When the I² value is greater than 50%, we will consider possible reasons for this.

Assessment of reporting biases

The aim of this review is to use dichotomous outcomes of known utility and of value to patients (Hoffman 2010; Moore 2010b; Moore 2010c; Moore 2010d; Moore 2013a). The review will not depend on what the authors of the original studies chose to report or not, though clearly difficulties will arise in studies failing to report any dichotomous results.

We will 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 NNTB of 10 or higher; Moore 2008).

Data synthesis

We plan to use a fixed‐effect model for meta‐analysis. We will use a random‐effects model for meta‐analysis if there is significant clinical heterogeneity and it is considered appropriate to combine studies.

If data are sufficient, we will undertake a quantitative synthesis and present data in forest plots. In the event of substantial clinical heterogeneity, we will switch off the totals in the forest plots.

We will undertake a meta‐analysis only if participants, interventions, comparisons, and outcomes are judged to be sufficiently similar to ensure an answer that is clinically meaningful, and only where there are data from at least 2 studies and 200 participants for analysis.

We will use RevMan for meta‐analysis (RevMan 2014) and Excel for NNTB and NNTH.

Subgroup analysis and investigation of heterogeneity

We do not plan subgroup analyses since experience of previous reviews indicates that there will be too few data for any meaningful subgroup analysis.

Sensitivity analysis

We plan no sensitivity analysis because the evidence base is known to be too small to allow reliable analysis.