Types of studies

We included studies if they were randomised controlled trials (RCTs) with double‐blind assessment of outcomes, reported after eight weeks of treatment or longer. Full journal publication was required, with the exception of extended abstracts of otherwise unpublished clinical trials. Short abstracts (usually meeting reports) were not included. We excluded non‐randomised studies, studies of experimental pain, case reports, and clinical observations.

Types of participants

Studies enrolled adults aged 18 years and above with one or more of a wide range of chronic neuropathic pain conditions including (but not limited to):

1. cancer‐related neuropathy;

2. central neuropathic pain;

3. complex regional pain syndrome (CRPS) Type II;

4. human immunodeficiency virus (HIV) neuropathy;

5. painful diabetic neuropathy (PDN);

6. phantom limb pain;

7. postherpetic neuralgia (PHN);

8. postoperative or traumatic neuropathic pain;

9. spinal cord injury;

10. trigeminal neuralgia;

11. and CRPS Type 1.

We included studies of participants with more than one type of neuropathic pain; in such cases, we analysed results according to the primary condition.

Types of interventions

Milnacipran in any dose, by any route, administered for the relief of neuropathic pain, and compared to placebo, no intervention or any other active comparator. We excluded studies using milnacipran 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 of them 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 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 (PGIC; moderate);

4. very much improved on PGIC (substantial).

These outcomes are different from those used in most earlier reviews, and concentrate on dichotomous outcomes in circumstances 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 having no worse than mild pain (Moore 2013a; O'Brien 2010).

We have not included a 'Summary of findings' table because there was no useful information to include.

Electronic searches

We searched the following databases.

1. the Cochrane Central Register of Controlled Trials (CENTRAL) (via CRSO) to 23 February 2015.

2. MEDLINE (via Ovid) 1946 to 23 February 2015.

3. EMBASE (via Ovid) 1976 to 23 February 2015.

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

There was no language restriction.

Searching other resources

We reviewed the bibliographies of all identified RCTs and review articles, and searched clinical trial databases (ClinicalTrials.gov (ClinicalTrials.gov) and World Health Organization (WHO) ICTRP (apps.who.int/trialsearch/)) to identify additional published or unpublished data. We did not contact investigators (except to clarify the status of ongoing studies) or study sponsors.

Selection of studies

Two review authors independently determined eligibility by first reading the title and abstract of each study identified by the search. We eliminated studies that clearly did not satisfy the inclusion criteria, and obtained full copies of the remaining studies. Two review authors then independently read these studies to determine inclusion and reached agreement by discussion. We did not anonymise the studies before assessment.

Data extraction and management

Two review authors independently extracted data using a standard form and checked for agreement before entry into Review Manager 5 (RevMan 2014) and other analysis tools. We included information about the pain condition and number of participants treated, drug and dosing regimen, study design (for example, parallel‐group or cross‐over, placebo or active control, titration schedule), 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, limiting inclusion to studies that were randomised and double‐blind as a minimum (Jadad 1996).

Two review authors independently assessed the risk of bias for each study, using the criteria outlined in the 'Risk of bias' tool 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 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 such as random number table or computer random number generator); unclear risk of bias (method used to generate sequence not clearly stated). We excluded studies using a non‐random process (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: low risk of bias (telephone or central randomisation; consecutively numbered sealed opaque envelopes); unclear risk of bias (method not clearly stated). We excluded studies that did not conceal allocation (open list).

3. 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: low risk of bias (study stated that it was blinded and described the method used to achieve blinding, such as 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 it was achieved). We excluded studies 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: low risk (less than 10% of participants did not complete the study or used 'baseline observation carried forward' (BOCF) analysis, or both); unclear risk of bias (used 'last observation carried forward' (LOCF) analysis); high risk of bias (used 'completer' analysis).

5. Size (checking for possible biases confounded by small size). Small studies have been shown to overestimate treatment effects, probably because the conduct of small studies is more likely to be less rigorous, allowing critical criteria to be compromised (Dechartres 2013; Kjaergard 2001; Nüesch 2010). Studies were considered to be at low risk of bias if they had 200 participants or more, at unclear risk if they had 50 to 200 participants, and at high risk if they had fewer than 50 participants.

Measures of treatment effect

We planned to pool dichotomous data to calculate risk ratio (RR) with 95% CIs using a fixed‐effect model unless we found significant statistical heterogeneity (see Assessment of heterogeneity), and to calculate NNTs as the reciprocal of the absolute risk reduction (ARR) (McQuay 1998). For unwanted effects, the NNT becomes the number needed to treat to treat for an additional harmful outcome (NNH) and is calculated in the same manner. We did not plan to use continuous data in analyses. In the event, there were insufficient data and we were able only to present results descriptively.

Unit of analysis issues

The unit of analysis was the individual participant. For cross‐over studies we planned to use the first period data only, but we did not include any cross‐over studies.

Dealing with missing data

We planned to use intention‐to‐treat (ITT) analysis where the ITT population consisted 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 examined similar conditions, and to assess statistical heterogeneity visually (L'Abbé 1987) and using the I² statistic, but pooling of data was not possible.

Assessment of reporting biases

The aim of this review was to use dichotomous data of known utility and of value to people with neuropathic pain (Moore 2010b; Moore 2013a). The review did not depend on what authors of the original studies chose to report or not, although clearly difficulties arose in studies that did not report any dichotomous results. We planned to extract and use continuous data, which probably poorly reflect efficacy and utility, only where useful for illustrative purposes.

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 an NNT of 10 or higher) (Moore 2008). We were unable to do this because of a lack of data.

Data synthesis

We planned to use a fixed‐effect model for meta‐analysis unless there was significant clinical heterogeneity and it was still considered appropriate to combine studies, in which case we would have used a random‐effects model. However, there were insufficient data for any pooled analysis.

We assessed data for each painful condition in three tiers, according to outcome and freedom from known sources of bias.

1. The first tier used data meeting current best standards, where studies reported the outcome of at least 50% pain intensity reduction over baseline (or its equivalent), without the use of LOCF or other imputation method other than BOCF for dropouts, reported an ITT analysis, lasted eight or more weeks, had a parallel‐group design, and had at least 200 participants (preferably at least 400) in the comparison (Moore 2010a; Moore 2012b). We planned to report these first‐tier results first.

2. The second tier used data from at least 200 participants, but where one or more of the above conditions was not met (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 used 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 planned subgroup analysis for:

1. dose of milnacipran;

2. different painful conditions.

Sensitivity analysis

We planned no sensitivity analyses, because the evidence base was known to be too small to allow reliable analysis.