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 We required full journal publication, with the exception of online clinical trial results summaries of otherwise unpublished clinical trials and abstracts with sufficient data for analysis.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

Studies included adults aged 18 years and above. Participants could have one or more of a wide range of chronic neuropathic pain conditions but we specifically searched for and included:

• painful diabetic neuropathy;

• postherpetic neuralgia;

• trigeminal neuralgia;

• phantom limb pain;

• postoperative or traumatic neuropathic pain;

• complex regional pain syndrome (CRPS), Type I and Type II;

• cancer‐related neuropathy;

• human immunodeficiency virus (HIV) neuropathy;

• spinal cord injury.

If studies had included participants with more than one type of neuropathic pain we would have analysed results according to the primary condition.

Types of interventions

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

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 (PGIC) (moderate), and 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%, 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). The 'Summary of findings' table includes outcomes of at least 50% and at least 30% pain intensity reduction, PGIC, adverse event withdrawals, serious adverse events and death.

Electronic searches

We searched the following databases without language restrictions:

• the Cochrane Central Register of Controlled Trials (CENTRAL) (2014, Issue 6) (via the Cochrane Library);

• MEDLINE (via Ovid) from 1946 to 3 July 2014;

• EMBASE (via Ovid) from 1974 to 3 July 2014.

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

Searching other resources

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Clinical Trials Registry Platform (ICTRP) (http://apps.who.int/trialsearch/)) to identify additional published or unpublished data.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

Selection of studies

Two authors (PW and SD) independently determined eligibility by reading the abstract of each study identified by the search. Independent authors eliminated studies that clearly did not satisfy inclusion criteria, and we obtained full copies of the remaining studies. Two review authors (PW and SD) read these studies independently and reached agreement by discussion. In the event of disagreement, a third author would adjudicate. 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 status of identified studies (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 RevMan (RevMan 2012). 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 (PW and SD) 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, 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 describes 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 does 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 and/or used ‘baseline observation carried forward’ analysis); 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 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 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% confidence intervals (CI) using a fixed‐effect model unless significant statistical heterogeneity was found (see below). Continuous data were not used in analyses.

Dealing with missing data

We 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 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 with the use of the I² statistic. If I² was greater than 50%, we would consider possible reasons.

Assessment of reporting biases

The aim of this review was to use dichotomous data of known utility (Moore 2010d). The review does not depend on what authors of the original studies chose to report or not. We would extract and use continuous data, which probably poorly reflect efficacy and utility, if 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 NNT values of 10 or higher) (Moore 2008).

Data synthesis

We planned to use a fixed‐effect model for meta‐analysis. A random‐effects model for meta‐analysis would have been used if there was significant clinical heterogeneity and it was considered appropriate to combine studies.

We planned to analyse efficacy 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 last observation carried forward (LOCF) or other imputation method for dropouts, reported an intention‐to‐treat (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). These top‐tier results would be reported first.

• The second tier used data from at least 200 participants but where one or more of the above conditions were 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 studies including 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.

We pooled adverse event data from different neuropathic pain conditions because there was no reason to believe that adverse responses would differ, and to provide a larger data set for analysis.

Subgroup analysis and investigation of heterogeneity

We planned efficacy 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). Analysis that pooled data from different conditions was carried out where there were insufficient data to analyse conditions separately, and only to give an indication of direction of effect.

Sensitivity analysis

We planned no sensitivity analysis because the evidence base was known to be too small to allow reliable analysis. We would examine details of dose escalation schedules, if available, in the unlikely situation that this could provide some basis for a sensitivity analysis.