Types of studies

We will include studies if they are randomised, double-blind controlled trials (RCTs) of at least two weeks’ duration (drug titration and maintenance or withdrawal). We will include studies with a parallel, cross-over, and enriched enrolment randomised withdrawal (EERW) design. Trials should have at least 10 participants per treatment arm. We require full journal publication, with the exception of online clinical trial results summaries of otherwise unpublished clinical trials, and abstracts with sufficient data for analysis.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 will not include short abstracts. We will exclude studies that are non-randomised, studies of experimental pain, case reports, and clinical observations. We will include studies that report at least one outcome of efficacy and safety as defined below.

Types of participants

Studies will include adults aged 18 years and above with one or more chronic (three months and more) neuropathic pain condition including (but not limited to):

1. cancer-related neuropathy;
2. central neuropathic pain (e.g. multiple sclerosis);
3. complex regional pain syndrome (CRPS) Type II;
4. human immunodeficiency virus (HIV) neuropathy;
5. painful diabetic neuropathy;
6. peripheral polyneuropathy of other aetiologies, for example toxic (alcohol, drugs);
7. phantom limb pain;
8. postherpetic neuralgia;
9. postoperative or traumatic peripheral nerve lesions;
10. spinal cord injury;
11. nerve plexus injury;
12. trigeminal neuralgia.

Where we include studies of participants with more than one type of neuropathic pain, we will analyse results according to the primary condition. Studies will have to state explicitly that they included people with neuropathic pain (by title). We will exclude studies that assessed pain in people with neurological diseases without specifying that the pain assessed was of neuropathic nature. We will exclude studies with fibromyalgia because the nature (neuropathic or not?) of fibromyalgia is under debate (Clauw 2015), and cannabinoids in fibromyalgia are the subject of another Cochrane review (Häuser 2015). We will exclude studies with ‘mixed pain’ (Baron 2004), because the concept is neither internationally accepted nor sufficiently validated and the focus of this review is only neuropathic pain.

Types of interventions

Cannabinoids (either phytocannabinoids, such as herbal cannabis (hashish, marihuana), plant-based cannabinoids (nabiximols), or pharmacological (synthetic) cannabinoids (e.g. cannabidiol, dronabinol, levonantradol, nabilone)), at any dose, by any route, administered for the relief of neuropathic pain and compared to placebo or any active comparator. We will not include studies with drugs under development that manipulate the endocannabinoid system by inhibiting enzymes that hydrolyse endocannabinoids and thereby boost the levels of the endogenous molecules (e.g. blockade of the catabolic enzyme fatty acid amide hydrolase (FAAH)) (Long 2009).

Types of outcome measures

The standards used to assess evidence in chronic pain trials have changed substantially in recent years, with particular attention being paid to trial duration, withdrawals, and statistical imputation following withdrawal, all of which can substantially alter estimates of efficacy. The most important change is the move from using mean pain scores, or mean change in pain scores, to the number of people who have a large decrease in pain (by at least 50%) and who continue in treatment, ideally in trials of eight to 12 weeks’ duration or longer. These standards are set out in the PaPaS Author and Referee Guidance for pain studies of the Cochrane Pain, Palliative and Supportive Care Group (Cochrane PaPaS 2012). This Cochrane review will assess evidence using methods that make both statistical and clinical sense, and will use criteria for what constitutes reliable evidence in chronic pain (Moore 2010a).
We anticipate that studies will 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 are 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). We will prefer neuropathic pain measures over generic pain measures.

Electronic searches

We will search the following databases, without language restrictions:

1. the Cochrane Central Register of Controlled Trials (CENTRAL);
2. MEDLINE (via Ovid);
3. EMBASE (via Ovid).

Appendix 2 shows the search strategy for MEDLINE. We will adapt the MEDLINE search strategy for CENTRAL and EMBASE.

Searching other resources

We will review the bibliographies of any RCTs identified and review articles, and search the following clinical trial databases: ClinicalTrials.gov (ClinicalTrials.gov), World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (apps.who.int/trialsearch/)), and International Association for Cannabinoid Medicines (IACM) databank (www.cannabis-med.org/studies/study.php to identify additional published or unpublished data. We will contact trial investigators to request missing data.

Selection of studies

Two review authors (WH, FP) will determine eligibility by reading the abstract of each study identified by the search. We will eliminate studies that clearly do not satisfy the inclusion criteria, and obtain full copies of the remaining studies. Two review authors (WH, FP) will independently read these studies and reach agreement by discussion. We will not anonymise the studies before assessment. We will create a PRISMA flow chart if appropriate.

Data extraction and management

Two review authors (WH, FP) will extract data independently using a standard form and check for agreement before entering data into Review Manager 5 (RevMan 2014), or any other analysis tool. We will include information about the pain condition and number of participants treated, study setting, inclusion and exclusion criteria, demographic and clinical characteristics of the study samples (age, gender, race, pain baseline), prior recreational cannabis use, drug and dosing regimen, co-therapies allowed, rescue medication, 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

Two review authors (WH, FP) will independently assess 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 Musculoskeletal Group for recent reviews on drug therapy in fibromyalgia, with any disagreements resolved by discussion. We will assess the following for each study.

1. Random sequence generation (checking for possible selection bias). We will assess the method used to generate the allocation sequence as: low risk of bias (i.e. any truly random process, e.g. random number table; computer random number generator); unclear risk of bias (when the method used to generate the sequence is not clearly stated). We will exclude studies at a high risk of bias that use a non-random process (e.g. 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 will assess the methods as: low risk of bias (e.g. telephone or central randomisation; consecutively numbered, sealed, opaque envelopes); unclear risk of bias (when method is not clearly stated). We will exclude studies that do not conceal allocation and are therefore at a high risk of bias (e.g. open list).
3. Blinding of participants and personnel/treatment providers (systematic performance bias). We assessed the methods used to blind participants and personnel/treatment providers from knowledge of which intervention a participant received. We will assess the methods as: low risk of bias (study states that it was blinded and describes the method used to achieve blinding, e.g. identical tablets; matched in appearance and smell); unclear risk of bias (study states that it was blinded but does not provide an adequate description of how it was achieved); high risk of bias (blinding of participants was not ensured, e.g. tablets different in form or taste).
4. Blinding of outcome assessment (checking for possible detection bias). We will assess the methods used to blind study outcome assessors from knowledge of which intervention a participant received. We will assess the methods as: low risk of bias (study states that outcome assessors were blinded to the intervention or exposure status of participants); unclear risk of bias (study states that the outcome assessors were blinded but does not provide an adequate description of how it was achieved); high risk of bias (outcome assessors knew the intervention or exposure status of participants).
5. Incomplete outcome data (checking for possible attrition bias due to the amount, nature, and handling of incomplete outcome data). We will assess the methods used to deal with incomplete data as: low risk of bias (i.e. 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); or high risk of bias (used ‘completer’ analysis).
6. Reporting bias due to selective outcome reporting (reporting bias). We will check if an a priori study protocol is available and if all outcomes of the study protocol are reported in the publications of the study. There is low risk of reporting bias if the study protocol is available and all of the study’s pre-specified (primary and secondary) outcomes that are of interest in the review are reported in the pre-specified way, or if the study protocol is not available but it is clear that the published reports include all expected outcomes, including those that are pre-specified (convincing text of this nature may be uncommon). There is a high risk of reporting bias if not all of the study’s pre-specified primary outcomes are reported; one or more primary outcomes is reported using measurements, analysis methods or subsets of the data (e.g. subscales) that are not pre-specified; one or more reported primary outcomes are not pre-specified (unless clear justification for their reporting is provided, such as an unexpected adverse effect); one or more outcomes of interest in the review are reported incompletely so that they cannot be entered in a meta-analysis; the study report did not include results for a key outcome that would be expected to have been reported for such a study.
7. Group similarity at baseline (selection bias). We will assess similarity of the study groups at baseline for the most important prognostic clinical and demographic indicators. There is low risk of bias if groups are similar at baseline for demographic factors, value of main outcome measure(s), and important prognostic factors. There is an unclear rsik of bias if important prognostic clinical and demographic indicators are not reported. There is high risk of bias if groups are not similar at baseline for demographic factors, value of main outcome measure(s), and important prognostic factor
8. Size of study (checking for possible biases confounded by small size). We will assess 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).

Two review authors (WH, MM) will make quality ratings separately for each of the eight methodology quality indicators as defined by the Cochrane ‘Risk of bias’ tool. We will define a study to be of high quality when it fulfils six to eight of the indicators, moderate quality when it fulfils three to five of the indicators, and low quality when it fulfils zero to two of the quality indicators (Schaefert 2015).
We will use the Grading of Recommendations Assessment, Development and Evaluation (GRADE) to assess the overall quality of evidence (Balshem 2011), defined as the extent of confidence in the estimates of treatment benefits and harms. We will downgrade the quality of evidence by one level for each of the following factors that we encounter.

1. Limitations of study design: less than 50% of the participants in low quality studies.
2. Inconsistency of effect size: I2 statistic greater than 50%.
3. Indirectness: we will assess whether the question being addressed in this systematic review was different from the available evidence regarding the population in routine clinical care, if people with inflammatory rheumatic diseases or depressive disorders (or both) were excluded in more than 50% of participants.
4. Imprecision: there was only one trial or when there was more than one trial, the total number was fewer than 400 participants or when 95% confidence intervals (CI) of the effect size included zero.

We will categorise the quality of evidence as follows.

1. High: we are very confident that the true effect lies close to that of the estimate of the effect.
2. Moderate: we are moderately confident in the effect estimate; the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different.
3. Low: our confidence in the effect estimate is limited; the true effect may be substantially different from the estimate of the effect.
4. Very low: we have very little confidence in the effect estimate; the true effect is likely to be substantially different from the estimate of effect; any estimate of effect is very uncertain.

Measures of treatment effect

We will calculate numbers needed to treat for an additional beneficial outcome (NNTB) as the reciprocal of the absolute risk reduction (ARR; McQuay 1998). For unwanted effects, the NNTB becomes the number needed to treat for an additional harmful outcome (NNTH) and is calculated in the same manner. We will use dichotomous data to calculate risk differences (RD) with 95% CI using a fixed-effect model unless we find significant statistical or clinical heterogeneity (see below).
We will to calculate standardised mean differences (SMD) with 95% CI for continuous variables using a fixed-effect model unless significant statistical or clinical heterogeneity will be found. We will calculate NNTBs for continuous variables (fatigue, sleep problems, psychological distress, health-related quality of life using the Wells calculator software available at the Cochrane Musculoskeletal Group editorial office, which estimates, from the SMD, the proportion of participants who will benefit from treatment (Norman 2001). We will use a minimal clinically important difference of 15% for the calculation of the NNTB from SMDs for all continuous outcomes. We will set the threshold for a clinically relevant benefit or a clinically relevant harm for categorical variables by an NNTB or NNTH less than 10 (Moore 2008).
We will use Cohen’s categories to evaluate the magnitude of the effect size, calculated by SMD, with Hedges’ g value of 0.2 = small, 0.5 = medium, and 0.8 = large (Cohen 1988). We will label a g value less than 0.2 to be a ‘not substantial’ effect size. We will assume a minimally important difference if the Hedges’ g value is 0.2 or greater (Fayers 2014).

Unit of analysis issues

We will split the control treatment arm between active treatment arms in a single study if the active treatment arms are not combined for analysis.
We will include studies with a cross-over design where separate data from the two periods are reported, data are presented that excluded a statistically significant carry-over effect, or statistical adjustments are carried out in case of a significant carry-over effect.

Dealing with missing data

We will use intention-to-treat (ITT) analysis where the ITT population consists of participants who are randomised, took at least one dose of the assigned study medication, and provided at least one post-baseline assessment.
Where means or standard deviations (SDs) are missing, we will attempt to obtain these data through contacting trial authors. Where SDs are not available from trial authors, we will calculate them from t values, P values, CIs, or standard errors, where reported in the articles (Higgins 2011). Where 30% and 50% pain reduction rates are not reported or provided on request, we will calculate them from means and SDs using a validated imputation method (Furukawa 2005).

Assessment of heterogeneity

We will deal with clinical heterogeneity by combining studies that examine similar conditions. We will assess statistical heterogeneity visually (L’Abbé 1987), and using the I2 statistic. When the I2 value is greater than 50%, we will consider possible reasons for this.

Assessment of reporting biases

We will 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 NNTB of 10 or higher; Moore 2008).

Data synthesis

We will use a fixed-effect model for meta-analysis. We will use a random-effects model using the inverse variance method in Review Manager 5 for meta-analysis if there is significant clinical or statistical (or both) heterogeneity and it is considered appropriate to combine studies (RevMan 2014).
We will analyse data for each painful condition in three tiers, according to outcome and freedom from known sources of bias.

1. The first tier will use 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 drop-outs, 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 1998; Moore 2010a; Moore 2012; Moore 2015). We will report these top-tier results first.
2. The second tier will use data from at least 200 participants but where one or more of the first-tier conditions above is not met (e.g. 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 will relate 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 plan subgroup analyses to be according to individual neuropathic pain syndromes, because placebo response rates for the same outcome can vary between conditions, as can the drug-specific effects (Moore 2013). We plan subgroup analyses (different cannabinoids; different routes of administration; very short (less than four weeks), short term (four to 12 weeks), intermediate term (13 to 26 weeks), and long-term (more than 26 weeks) study duration) if there are at least two studies available.

Sensitivity analysis

We plan no sensitivity analysis because the evidence base is known to be too small to allow reliable analysis. We will examine details of dose- escalation schedules in the unlikely situation that this could provide some basis for a sensitivity analysis.