Types of studies

We included studies if they were randomised controlled trials (RCTs) with at least 10 participants per treatment arm and reported 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 We required full journal publication, with the exception of online clinical trial results, summaries of otherwise unpublished clinical trials, and abstracts with sufficient data for analysis.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

Studies had to include adults aged 18 years and older with one or more chronic neuropathic pain condition including (but not limited to):

• cancer‐related neuropathy;

• central neuropathic pain;

• complex regional pain syndrome (CRPS) Type ll;

• 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.

We would have included studies of participants with more than one type of neuropathic pain, with analysis according to the primary condition, but the included studies each enrolled participants with only one pain condition.

Types of interventions

Oxycodone at any dose, by any route, administered for the relief of neuropathic pain and compared with placebo or any active comparator. In this update, we included studies using oxycodone combined with naloxone (to reduce abuse potential and constipation) and also studies using oxycodone as an add‐on to stable, but inadequate, treatment with another class of drug (see Differences between protocol and review).

Types of outcome measures

We anticipated that studies would use a variety of outcome measures, with the majority 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:

• 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 scale (PGIC; moderate);

• very much improved on PGIC (substantial).

These outcomes are different from those used in many 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 2013a; O'Brien 2010).

Electronic searches

For this update we searched the following databases, without language restrictions.

• Cochrane Central Register of Controlled Trials (CENTRAL, via the Cochrane Register of Studies Online database (CRSO)) to 21 December 2015.

• MEDLINE (via Ovid) from January 2013 to 21 December 2015.

• EMBASE (via Ovid) from January 2013 to 21 December 2015.

The search strategies for CENTRAL, MEDLINE, and EMBASE are listed in Appendix 2, Appendix 3, and Appendix 4, respectively.

We carried out additional searches for studies using oxycodone plus naloxone, published before January 2013, since these would not have been included in the earlier review.

Searching other resources

We reviewed the bibliographies of any RCTs identified and review articles, and searched clinical trial databases (ClinicalTrials.gov) and World Health Organization International Clinical Trials Registry Platform (ICTRP) (apps.who.int/trialsearch/) to identify additional published or unpublished data. We did not contact study sponsors, but did write to the authors of one study, identified in Clinicaltrials.gov and as a meeting abstract, to ask when results are likely to be available.

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 obtained full copies of the remaining studies. Two review authors read these studies independently and reached agreement about inclusion by discussion. We did not anonymise the studies in any way before assessment. We included a Preferred Reporting Items for Systematic Reviews and Meta‐Analyses (PRISMA) flow chart (Figure 1).

Figure 1

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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 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 (Jadad 1996) as the basis for inclusion, limiting inclusion to studies that, as a minimum, were randomised and double‐blind.

Two review authors independently assessed risk of bias for each study, using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a), 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.

• 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 (method used to generate sequence was not clearly stated). We excluded studies using a non‐random process, which were therefore at high risk of bias (eg odd or even date of birth; hospital or clinic record number).

• Allocation concealment (checking for possible selection bias). The method used to conceal allocation to interventions before 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 (method was not clearly stated). We excluded studies that did not conceal allocation and were therefore at high risk of bias (eg open list).

• 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 tubes containing gel, or identical plasters; matched in appearance and smell); unclear risk of bias (study stated that it was blinded but did not provide an adequate description of how blinding was achieved). We excluded studies that were not double‐blind and therefore at high risk of bias.

• 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 (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 LOCF analysis); or high risk of bias (used 'completer' analysis).

• Size (checking for possible biases confounded by small size). Small studies have been shown to overestimate treatment effects, probably due to methodological weaknesses (Dechartres 2013; Nüesch 2010). We assessed studies as at low risk of bias if they had at least 200 participants per treatment arm, at unclear risk if they had 50 to 200 participants per treatment arm, and at high risk if they had fewer than 50 participants per treatment arm.

Measures of treatment effect

We calculated NNTs as the reciprocal of the absolute risk reduction (McQuay 1998). For unwanted effects, the NNT becomes the NNH and is calculated in the same manner. We used dichotomous data to calculate risk ratio (RR) with 95% confidence intervals (CI) using a fixed‐effect model. In the event of significant statistical heterogeneity, we would consider using a random‐effects model (see Assessment of heterogeneity). We did not plan to use continuous data in analyses.

Unit of analysis issues

We accepted randomisation to individual participant only. In the event of a study having more than one active treatment arm, in which data were not combined for analysis, we planned to split the control treatment arm between active treatment arms. For cross‐over studies, we planned to use only the first period, if this was available. Where only combined data for both periods were reported, we treated the study as if it was a parallel study, drawing attention to the potential bias that this confers, and interpreting the results accordingly.

Dealing with missing data

We used 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 zero improvement to missing participants wherever possible. We have commented where ITT data were not available.

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 with the use of the I² statistic. When the I² value was greater than 50%, we considered possible reasons for this.

Assessment of reporting biases

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

We assessed publication bias using a method designed to detect the amount of unpublished data with a null effect that would be required to make the result of any efficacy analysis clinically irrelevant (usually taken to mean an NNT of 10 or more in these conditions) (Moore 2008).

Data synthesis

We planned to analyse individual painful conditions separately because placebo response rates with the same outcome can vary between conditions, as can the drug‐specific effects (Moore 2009). This was not possible because there were very limited data. We used a fixed‐effect model for meta‐analysis, and analysed data 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 methods for drop‐outs, report an ITT analysis, last eight weeks or more, have a parallel group design, and have at least 200 participants (preferably at least 400) in the comparison (Moore 1998; Moore 2010a; Moore 2012b).

• The second tier uses data from at least 200 participants but where one or more of the above conditions is not met (eg 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.

In the event, because there were so few data, we chose to pool results for different conditions in exploratory analyses for efficacy, adverse events, and withdrawals.

Subgroup analysis and investigation of heterogeneity

We planned to analyse separately data for different pain conditions and dosing regimens, but this was not possible.

For this update, we included studies using oxycodone as an add‐on therapy and studies using oxycodone in combination with naloxone, and chose to analyse these studies as a separate subgroup to investigate potential heterogeneity.

Sensitivity analysis

No sensitivity analyses were planned, but because we combined data from the study in PHN with those in diabetic neuropathy for this update, we carried out sensitivity analyses (where there were sufficient data) to determine the effect of excluding PHN. In addition, because one study used an 'active' placebo, we carried out sensitivity analyses (where there were sufficient data) to determine whether this had any effect on the incidence of adverse events.