Types of studies

We included 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 We required full journal publication, with the exception of online clinical trial results summaries of otherwise unpublished clinical trials and abstracts with sufficient data for analysis.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), or studies that were non‐randomised, studies of experimental pain, case reports, and clinical observations.

Types of participants

Studies included adults aged 18 years and above with one or more 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; and

10. trigeminal neuralgia.

If studies included participants with more than one type of neuropathic pain, we planned to analyse results according to the primary condition.

Types of interventions

Hydromorphone 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 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 scale (PGIC; moderate);

4. very much improved on PGIC (substantial).

These outcomes are different from those used in most earlier reviews, concentrating as they do on dichotomous outcomes where pain responses do not follow a normal (Gaussian) distribution. People with chronic pain desire high levels of pain relief, ideally more than 50% pain intensity reduction, and ideally having no worse than mild pain (Moore 2013b; 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 database (CRSO)) on 17 November 2015.

2. MEDLINE (via Ovid), 1946 to 17 November 2015.

3. EMBASE (via Ovid), 1974 to 17 November 2015.

Search strategies for CENTRAL, MEDLINE, and EMBASE are in Appendix 2, Appendix 3, and Appendix 4, respectively.

Searching other resources

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Clinical Trials Registry Platform (ICTRP) (apps.who.int/trialsearch/)) to identify additional published or unpublished data.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

Selection of studies

We determined eligibility by first 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. Two review authors made the decisions. Two review authors read these studies independently and reached agreement by discussion. We did not anonymise the studies in any way before assessment. We provided a PRISMA flow chart (Figure 1).

Figure 1

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Study flow diagram.

Data extraction and management

Two review authors extracted data independently using a standard form and checked for agreement before entry 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 independently assessed the 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, eg random number table; computer random number generator); unclear risk of bias (when the method used to generate the sequence was not clearly stated). We excluded studies at a high risk of bias that used a non‐random process (eg 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 (eg telephone or central randomisation; consecutively numbered, sealed, opaque envelopes); unclear risk of bias (when the method was not clearly stated). We excluded studies that did not conceal allocation and were therefore at a high risk of bias (eg 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, eg 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 at a 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: low risk of bias (fewer than 10% of participants did not complete the study or used 'baseline observation carried forward' analysis, or both); unclear risk of bias (used 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 planned 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 for an additional harmful outcome (NNH) and is calculated in the same manner. We planned to use dichotomous data to calculate risk ratio (RR) with 95% confidence intervals (CI) using a fixed‐effect model unless we found significant statistical heterogeneity (see below). We did not plan to use continuous data in analyses.

Unit of analysis issues

We planned to split the control treatment arm between active treatment arms in a single study if there was more than one active treatment arm, and they were not combined for analysis.

Dealing with missing data

We extracted data using 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 postbaseline assessment. We assigned zero improvement to missing participants wherever possible.

Assessment of heterogeneity

We planned to deal with clinical heterogeneity by combining studies that examined similar conditions, and assess statistical heterogeneity visually (L'Abbé 1987), and with the use of the I² statistic. If the I² value was greater than 50%, we planned to consider possible reasons for this. In the event, there was only one included study, so heterogeneity was not an issue.

Assessment of reporting biases

The aim of this review was to use dichotomous outcomes of known utility and of value to people with pain (Hoffman 2010; Moore 2010c; Moore 2010d; Moore 2010e; Moore 2013b). The review did not depend on what the authors of the original studies chose to report or not, though clearly difficulties arose because the included study did not report any dichotomous efficacy results. Therefore, we extracted mean data, which probably reflect efficacy and utility poorly, as a secondary outcome that could give some indication of efficacy.

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). In the event, this was not possible.

Data synthesis

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

We planned to analyse data for each painful condition 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 reported the outcome of at least 50% pain intensity reduction over baseline (or its equivalent), without the use of LOCF or other imputation method for drop‐outs, 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 1998; Moore 2010a; Moore 2012a; Moore 2012b).

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 (eg 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 would relate 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 neuropathic pain conditions, because placebo response rates for the same outcome can vary between conditions, as can the drug‐specific effects (Moore 2009).

We did not plan subgroup analyses since experience of previous reviews indicated that there would be too few data for any meaningful subgroup analysis (Gaskell 2014; McNicol 2013).

Sensitivity analysis

We did not plan specific sensitivity analysis because the evidence base is known to be too small to allow reliable analysis. We had hoped to examine details of dose‐escalation schedules to see if this could provide some basis for a sensitivity analysis.