Types of studies

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 We required full journal publication, with the exception of online clinical trial results summaries of otherwise unpublished clinical trials and abstracts with sufficient data for analysis.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

Our experience from previous reviews was that most studies would be older, small, and have methodological deficiencies according to present standards of evidence, and therefore we felt it appropriate to consider lower standards of evidence than those currently demanded for part of our analyses. This included reviewing data from studies of shorter duration, and studies where the outcome definition was poorly defined; all studies had to be both randomised and double‐blind as a minimum. We have reported the evidence available according to the current standards, and lower levels of evidence. It is important to recognise that the lower level evidence is likely to be subject to various positive biases, and that these lower levels of evidence cannot be used to make cross‐drug comparisons of efficacy with other drugs.

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):

• cancer‐related neuropathy;

• central neuropathic pain;

• complex regional pain syndrome (CRPS) Type II;

• human immunodeficiency virus (HIV) neuropathy;

• painful diabetic neuropathy (PDN);

• phantom limb pain;

• postherpetic neuralgia (PHN);

• postoperative or traumatic neuropathic pain;

• spinal cord injury;

• trigeminal neuralgia;

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. We excluded studies using nortriptyline for prevention of migraine and headache as they are the subject of another Cochrane review (Chronicle 2004).

Types of interventions

Nortriptyline at any dose, by any route, administered for the relief of neuropathic pain, and compared with placebo or any active comparator.

Types of outcome measures

We anticipated that studies would use a variety of outcome measures, with most of 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 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, without language restrictions.

• the Cochrane Central Register of Controlled Trials (CENTRAL) (via CRSO) to 7 January 2015

• MEDLINE (via Ovid) 1946 to 7 January 2015.

• EMBASE (via Ovid) 1976 to 7 January 2015.

Appendix 2, Appendix 3, and Appendix 4 show the search strategies for CENTRAL, MEDLINE, and EMBASE, respectively.

Searching other resources

We reviewed the bibliographies of all identified RCTs and review articles, and searched clinical trial databases (ClinicalTrials.gov (ClinicalTrials.gov) and 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. Figure 1 shows the PRISMA flow chart.

Figure 1

---

---

Study flow diagram.

Data extraction and management

Two review authors independently extracted data using a standard form and checked for agreement before entry into Review Manager (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 (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 (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); 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); high risk of bias (fewer than 50 participants per treatment arm).

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 harm (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

For cross‐over studies, we planned to use first period data only, wherever possible, but only one of the studies reported any results in this way. Most of the cross‐over studies reported only for participants completing more than one phase of treatment, so in the absence of any pooled analysis, we have used results as reported in the individual studies, but have drawn attention to the potential bias this may introduce.

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.

• 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 top‐tier results first.

• The second tier used data from at least 200 participants, but where one or more of the above conditions was 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 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 planned all analyses to be according to individual painful conditions, because placebo response rates for the same outcome can vary between conditions, as can the drug‐specific effects (Moore 2009). We also planned to examine details of dose escalation schedules to investigate if this could explain any observed heterogeneity, but there were insufficient data for any one condition for any combined efficacy analysis.

Sensitivity analysis

There were insufficient data to carry out sensitivity analyses for dose of nortriptyline and duration of study.