Types of studies

We included studies if they were randomised controlled trials (RCTs) with double‐blind assessment of participant outcomes following two weeks of treatment or longer, although the emphasis of the review was on studies 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 We required full journal publication, with the exception of online clinical trial results summaries of otherwise unpublished clinical trials and abstracts with sufficient data for analysis.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.

Types of participants

Participants were aged 18 years and above and could have one or more of a wide range of chronic neuropathic pain conditions including (but not limited to):

• cancer‐related neuropathy;

• complex regional pain syndrome (CRPS) Type II;

• human immunodeficiency virus (HIV) neuropathy;

• painful diabetic neuropathy;

• phantom limb pain;

• postherpetic neuralgia;

• postoperative or traumatic neuropathic pain;

• spinal cord injury;

• trigeminal neuralgia;

and

• CRPS Type I.

We would include studies of participants with more than one type of neuropathic pain; in such cases we would analyse results according to the primary condition. Migraine and headache studies were excluded.

Types of interventions

Oral desipramine at any dose, administered for the relief of neuropathic pain and compared to placebo or any active comparator.

Types of outcome measures

Studies used a variety of outcome measures, with the majority using subjective scales (numerical rating scale (NRS) or visual analogue scale (VAS)) 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 the Patient Global Impression of Change (PGIC) (moderate), and very much improved on the PGIC (substantial). These outcomes 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 with pain not worse than mild (O'Brien 2010).

We have included a 'Summary of findings' table as set out in the author guide (AUREF 2012), which includes outcomes of at least 50% and at least 30% pain intensity reduction, PGIC, adverse event withdrawals, serious adverse events and death (summary of findings Table for the main comparison).

Electronic searches

We searched the following databases:

• the Cochrane Central Register of Controlled Trials (CENTRAL) (The Cochrane Library 2014, Issue 4 of 12);

• MEDLINE (via Ovid) (1946 to 29 April 2014);

• EMBASE (via Ovid) (1974 to 29 April 2014).

Search strategies for CENTRAL, MEDLINE, and EMBASE are in Appendix 2, Appendix 3, and Appendix 4. There were no language restrictions.

Searching other resources

We reviewed the bibliographies of any randomised trials identified and review articles, and searched clinical trial databases (ClinicalTrials.gov (http://clinicaltrials.gov/) and the World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) search portal (http://apps.who.int/trialsearch/)) to identify additional published or unpublished data. We did not contact investigators or study sponsors because of the age of the studies identified and because this is not an area of active research.

Selection of studies

We determined eligibility by reading the abstract of each study identified by the search. We eliminated studies that clearly did not satisfy the inclusion criteria, and we obtained full copies of the remaining studies; decisions were made by two review authors. Two review authors then read these studies independently and reached agreement by discussion. We did not anonymise the studies in any way before assessment. A Preferred Reporting Items for Systematic Reviews and Meta‐Analyses (PRISMA) flow chart shows the selection process (Moher 2009).

Data extraction and management

Two review authors independently extracted data using a standard form and checked for agreement before entry into the Cochrane Collaboration's statistical software (Review Manager 2013) 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 authors independently assessed 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 the Cochrane Pregnancy and Childbirth Group, with any disagreements resolved 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, for example random number table; computer random number generator); unclear risk of bias (method used to generate sequence not clearly stated). We excluded studies using 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: low risk of bias (for example, 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 (for example, 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, for example, 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 (< 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 of study (checking for possible biases confounded by small size). We assessed studies as being at low risk of bias (≥ 200 participants per treatment arm); unclear risk of bias (50 to 199 participants per treatment arm); high risk of bias (< 50 participants per treatment arm).

Measures of treatment effect

We planned to calculate numbers needed to treat (NNTs) as the reciprocal of the absolute risk reduction (ARR) (McQuay 1998). For unwanted effects, the NNT becomes the number needed to treat to harm (NNH) and is calculated in the same manner. We planned to use dichotomous data to calculate risk ratio (RR) with 95% CI using a fixed‐effect model unless significant statistical heterogeneity was found (Assessment of heterogeneity). Continuous data were not used in the analyses.

Unit of analysis issues

The control treatment arm would be split between active treatment arms in a single study if the active treatment arms were not combined for analysis.

For cross‐over studies we planned to use first period data only wherever possible. Where this was not reported we analysed the data as if the treatment periods were parallel, drawing attention to the potential bias this may introduce, and interpreting the results accordingly.

Dealing with missing data

Where possible 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. Missing participants were assigned zero improvement. Where this was not possible we have used the results as reported, but drawn attention to the potential bias this may introduce. These data were not used in any analyses.

Assessment of heterogeneity

We planned to deal with clinical heterogeneity by combining studies that examined similar conditions. We would have assessed statistical heterogeneity visually (L'Abbé 1987), and with the use of the I² statistic.

Assessment of reporting biases

The aim of this review was to use dichotomous data of known utility (Moore 2010c). The review did not depend on what authors of the original studies chose to report or not, though clearly difficulties arose in studies failing to report any dichotomous results. We have extracted and reported continuous data, which probably poorly reflect efficacy and utility, 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 an NNT of 10 or higher) (Moore 2008).

Data synthesis

We planned to use a fixed‐effect model for meta‐analysis or use a random‐effects model for meta‐analysis if there was significant clinical heterogeneity and it was considered 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 uses 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 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 2010a; Moore 2012b). These top tier results are reported first.

• The second tier uses data from at least 200 participants but where one or more of the above conditions is 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 relates to data from fewer than 200 participants, or where there are expected to be significant problems because, for example, of very short duration studies of less than four weeks, where there is major heterogeneity between studies, or where there are 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 all analyses to be according to individual painful conditions, because placebo response rates with the same outcome can vary between conditions, as can the drug‐specific effects (Moore 2009). If there had been sufficient data we would have carried out subgroup analysis for dose of desipramine and duration of study.

Sensitivity analysis

If there had been sufficient data we would have examined details of dose escalation schedules to investigate if this could provide some basis for a sensitivity analysis.