Types of studies

We only included randomised controlled trials, with or without blinding, and participant‐ or observer‐reported outcomes.

Full journal publication was required, with the exception of online clinical trial results, summaries of otherwise unpublished clinical trials, and abstracts with sufficient data for analysis. We included studies published in any language. We excluded abstracts (usually meeting reports) or unpublished data, non‐randomised studies, studies of experimental pain, case reports, and clinical observations.

Types of participants

We included studies of infants, children, and adolescents, aged from birth to 17 years old, with chronic or recurrent pain (lasting for three months or longer), arising from genetic conditions, neuropathy, or other conditions. These included but were not limited to chronic musculoskeletal pain and chronic abdominal pain.

We excluded studies of perioperative pain, acute pain, cancer pain, and pain associated with primary disease or its treatment. We excluded headache and migraine (particularly prophylaxis), as these are addressed in separate Cochrane reviews.

We included studies of participants with more than one type of chronic pain, and then analysed results according to the primary condition.

Types of interventions

We included studies reporting interventions prescribing NSAIDs for the relief of chronic pain, by any route, in any dose, with comparison to placebo or any active comparator.

Types of outcome measures

In order to be eligible for inclusion in this review, studies had to report pain assessment, as well as meeting the other selection criteria.

We included trials measuring pain intensity and pain relief assessed using validated tools such as numerical rating scale (NRS), visual analogue scale (VAS), Faces Pain Scale ‐ Revised (FPS‐R), Colour Analogue Scale (CAS), or any other validated numerical rating scale.

We were particularly interested in Pediatric Initiative on Methods, Measurement, and Pain Assessment in Clinical Trials (PedIMMPACT) definitions for moderate and substantial benefit in chronic pain studies (PedIMMPACT 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) scale (moderate); very much improved on PGIC (substantial).

These outcomes differ 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 2013a; O'Brien 2010).

We also recorded any reported adverse events. We reported the timing of outcome assessments.

Electronic searches

We searched the following databases:

• Cochrane Central Register of Controlled Trials (CENTRAL) (via the Cochrane Register of Studies Online), searched 6 September 2016;

• MEDLINE (via Ovid) 1946 to September week 2 2016, searched 6 September 2016;

• Embase (via Ovid) 1974 to 2016 week 38, searched 6 September 2016..

We used medical subject headings (MeSH) or equivalent and text word terms. We restricted our search to randomised controlled trials and clinical trials. There were no language or date restrictions. The focus of the keywords in our search terms was on chronic pain and NSAIDs. We tailored searches to individual databases. The search strategies for MEDLINE, Embase, and CENTRAL are in Appendix 3, Appendix 4, and Appendix 5, respectively.

Searching other resources

We searched ClinicalTrials.gov (www.clinicaltrials.gov) and the World Health Organization International Clinical Trials Registry Platform (WHO ICTRP) (apps.who.int/trialsearch/) on 6 September 2016 for ongoing trials. In addition, we checked reference lists of reviews and retrieved articles for additional studies, and performed citation searches on key articles. We planned to contact experts in the field for unpublished and ongoing trials. We planned to contact study authors for additional information where necessary.

Selection of studies

Two review authors independently determined study eligibility by reading the abstract of each study identified by the search. Review authors independently eliminated studies that clearly did not satisfy the inclusion criteria, and obtained full copies of the remaining studies. Two review authors independently read these studies to select those that met the inclusion criteria, a third review author adjudicating in the event of disagreement. We did not anonymise the studies in any way before assessment. We included a PRISMA flow chart in Figure 1 to illustrate the results of the search and the process of screening and selecting studies for inclusion in the review (Moher 2009), as recommended in section 11.2.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We included studies in the review irrespective of whether measured outcome data were reported in a ‘usable’ way.

Figure 1

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Study flow diagram.

Data extraction and management

We obtained full copies of the studies, and two review authors independently carried out data extraction. Where this information was available, we extracted data on pain condition, 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). We collated multiple reports of the same study, so that each study rather than each report was the unit of interest in the review. We collected characteristics of the included studies in sufficient detail to populate a ‘Characteristics of included studies’ table.

We used a template data extraction form and checked for agreement before entry into Cochrane's statistical software Review Manager 5 (RevMan 2014).

If a study had more than two intervention arms, we only included the data from the intervention and control groups that met the eligibility criteria. If we included multi‐arm studies, we planned to analyse multiple intervention groups in an appropriate way that avoided arbitrary omission of relevant groups and double‐counting of participants.

Assessment of risk of bias in included studies

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 2011).

We completed a 'Risk of bias' table for each included study using the Cochrane 'Risk of bias' tool in Review Manager 5 (RevMan 2014).

We assessed the following for each study. Any disagreements were resolved by discussion between review authors or by consulting a third review author when necessary.

1. Random sequence generation (checking for possible selection bias). We assessed 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); or unclear risk of bias (when the method used to generate the sequence is not clearly stated). We excluded studies that used a non‐random process and were therefore at high risk of bias (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 assessed the methods as: low risk of bias (e.g. telephone or central randomisation; consecutively numbered, sealed, opaque envelopes); or unclear risk of bias (when the method is not clearly stated). We excluded studies that did not conceal allocation and were therefore at a high risk of bias (e.g. open list).

3. Blinding of participants and personnel (checking for possible performance bias). We assessed any methods used to blind the participants and personnel from knowledge of which intervention a participant received. We assessed the methods as: low risk of bias (study states that the participants and personnel involved were blinded to treatment groups); unclear risk of bias (study does not state whether or not participants and personnel were blinded to treatment groups); or high risk of bias (participants or personnel were not blinded) (as stated in Types of studies, we included trials with or without blinding, and participant‐ or observer‐reported outcomes).

4. Blinding of outcome assessment (checking for possible detection bias). We assessed any methods used to blind the outcome assessors from knowledge of which intervention a participant received. We assessed the methods as: low risk of bias (e.g. study states that it was single‐blinded and describes the method used to achieve blinding of the outcome assessor); unclear risk of bias (study states that outcome assessors were blinded but does not provide an adequate description of how this was achieved); or high risk of bias (outcome assessors were not blinded) (as stated in Types of studies, we included trials with or without blinding, and participant‐ or observer‐reported outcomes).

5. 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 (i.e. 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 'last observation carried forward' (LOCF) analysis); or high risk of bias (used 'completer' analysis).

6. Selective reporting (checking for possible reporting bias). We assessed the methods used to report the outcomes of the study as: low risk of bias (if all planned outcomes in the protocol or methods were reported in the results); unclear risk of bias (if there was not a clear distinction between planned outcomes and reported outcomes); or high risk of bias (if some planned outcomes from the protocol or methods were clearly not reported in the results).

7. Size of study (checking for possible biases confounded by small size) (Dechartres 2013; Dechartres 2014; McQuay 1998; Nüesch 2010; Thorlund 2011). 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).

8. Other bias, such as multiple publications, financial declarations, participants with conflicts of interest. We assessed studies for any additional sources of bias as low, unclear, or high risk of bias, and provided rationale.

Measures of treatment effect

Where dichotomous data were available, we calculated a risk ratio (RR) with 95% confidence interval (CI) and meta‐analysed the data as appropriate. We calculated numbers needed to treat for an additional beneficial outcome (NNTBs) where appropriate (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. Where continuous data were reported, we used appropriate methods to combine these data in the meta‐analysis.

Unit of analysis issues

We accepted randomisation to the individual participant only. We split the control treatment arm between active treatment arms in a single study if the active treatment arms were not combined for analysis. We only accepted studies with minimum 10 participants per treatment arm.

Dealing with missing data

We used intention‐to‐treat analysis where the intention‐to‐treat 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 identified and measured heterogeneity as recommended in Chapter 9 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We dealt with clinical heterogeneity by combining studies that examined similar conditions. We undertook and presented a meta‐analysis only if we judged participants, interventions, comparisons, and outcomes to be sufficiently similar to ensure a clinically meaningful answer. We assessed statistical heterogeneity visually and by using the I² statistic (L'Abbé 1987). When I² was greater than 50%, we considered the possible reasons.

Assessment of reporting biases

We assessed the risk of reporting bias, as recommended in chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).

The aim of this review was to use dichotomous outcomes of known utility and of value to patients (Hoffman 2010; Moore 2010b; Moore 2010c; Moore 2010d; Moore 2013a). The review did not depend on what the authors of the original studies chose to report or not, though clearly difficulties would arise in studies failing to report any dichotomous results. We extracted and used continuous data, which probably reflect efficacy and utility poorly, and may be useful for illustrative purposes only.

We assessed 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 a number needed to treat (NNT) of 10 or higher) (Moore 2008).

Data synthesis

We planned to use a fixed‐effect model for meta‐analysis. We used a random‐effects model for meta‐analysis if there was significant clinical heterogeneity and we considered it appropriate to combine studies. We conducted our analysis using the primary outcomes of pain and adverse events, and planned to calculate the NNTHs for adverse events. We used the Cochrane software program Review Manager 5 (RevMan 2014).

Subgroup analysis and investigation of heterogeneity

We planned to perform subgroup analyses where a minimum number of data were available (at least 200 participants per treatment arm). We planned to analyse according to age group; type of drug; geographical location or country; type of control group; baseline measures; frequency, dose, and duration of drugs; and nature of drug.

We planned to investigate whether the results of subgroups were significantly different by inspecting the overlap of confidence intervals and performing the test for subgroup differences available in Review Manager 5.

Sensitivity analysis

We did not plan to carry out any sensitivity analysis because the evidence base is known to be too small to allow reliable analysis; we did not plan to pool results from chronic pain of different origins in the primary analyses. We examined details of dose escalation schedules in the unlikely circumstance that this could provide some basis for a sensitivity analysis.