Types of studies

To be included, studies must:

• be randomised (described as 'randomised' anywhere in the manuscript);

• ideally be double‐blind, but we will include open studies;

• have placebo or active controls, or both;

• include a minimum of 10 participants per treatment arm.

We will exclude non‐randomised studies, studies of experimental pain, case reports and clinical observations. Studies have to be fully published or available as extended abstracts (e.g. from clinical trial websites); we will exclude short (usually conference) abstracts as these are often unreliable (PaPaS 2012).

Types of participants

Studies will include adults or children of any age who experience cancer pain.

Types of interventions

Tramadol with or without paracetamol for cancer pain. Tramadol may be administered at any dose and by any route, and compared to placebo or any active comparator.

Types of outcome measures

Pain has to be measured using a validated assessment tool. For pain intensity, for example, this could be a 100‐mm visual analogue scale (VAS) or 11‐point numerical rating scale (no pain to worst pain imaginable), or a 4‐point categorical scale (none, mild, moderate, severe), and for pain relief a 100 mm VAS (no relief to complete relief), or 5‐point categorical scale (none, a little, some, a lot, complete or words to that effect). Measures of 30% or greater (moderate) and 50% or greater (substantial) reduction of pain over baseline are recommended outcomes for chronic pain studies from the Initiative on Methods, Measurement, and Pain Assessment in Clinical Trials (IMMPACT) (Dworkin 2008). When considering Patient Global Impression of Change (PGIC), 30% or greater reduction of pain over baseline equates to much improved and very much improved, and 50% or greater reduction of pain over baseline equates to very much improved. We will also use results equivalent to no pain or mild pain, because these are also outcomes acceptable to people with various types of pain (Moore 2013).

Electronic searches

We will search the following databases without language or date restrictions.

• The Cochrane Central Register of Controlled Trials (CENTRAL) (via CRSO).

• MEDLINE (via Ovid).

• Embase (via Ovid).

We will use a combination of MeSH or equivalent and text word terms and tailor search strategies to individual databases. Searches will be tailored to individual databases. The search strategy for MEDLINE is in Appendix 1.

Searching other resources

We will search the metaRegister of controlled trials (mRCT) (www.controlled‐trials.com/mrct), ClinicalTrials.gov (www.clinicaltrials.gov) and the WHO International Clinical Trials Registry Platform (ICTRP) (http://apps.who.int/trialsearch/) for ongoing trials. In addition, we will check reference lists of reviews and retrieved articles for additional studies and perform citation searches on key articles. We will contact experts in the field for unpublished and ongoing trials and authors where necessary for additional information.

Selection of studies

Two review authors (PW, SD) will independently read the abstract of each study identified by the search, eliminate studies that clearly do not satisfy inclusion criteria, and obtain full copies of the remaining studies. Two review authors (PW, SD) will read these studies independently to select relevant studies for inclusion. In the event of disagreement, a third review author (RAM) will adjudicate. We will not anonymise the studies before assessment. We will include a PRISMA flow chart in the review which will show the status of identified studies as recommended in Section 11.2.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will include studies in the review irrespective of whether measured outcome data are reported in a 'usable' way.

Data extraction and management

Two review authors (PW, SD) will independently extract data using a standard form and check for agreement before entry into Review Manager 5 (RevMan 2014). We will include information about the number of participants treated and demographic details, type of cancer, drug and dosing regimen, study design (placebo or active control) and methods, study duration and follow‐up, analgesic outcome measures and results, withdrawals and adverse events. We will collate multiple reports of the same study, so that each study rather than each report is the unit of interest in the review. We will collect characteristics of the included studies in sufficient detail to complete a 'Characteristics of included studies' table.

Assessment of risk of bias in included studies

Two review authors (PW, SD) will independently assess risk of bias for each study, using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Chapter 8, Higgins 2011) and adapted from those used by the Cochrane Pregnancy and Childbirth Group, with any disagreements resolved by discussion. We will complete a 'Risk of bias' table for each included study using the Risk of bias tool in Review Manager 5 (RevMan 2014).

We will assess the following for each study.

• Random sequence generation (checking for possible selection bias). We will assess the method used to generate the allocation sequence as: low risk of bias (any truly random process, e.g. random number table; computer random number generator); unclear risk of bias (method used to generate sequence not clearly stated). We will exclude studies using a non‐random process (e.g. 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 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 (method not clearly stated). We will exclude studies that do not conceal allocation (e.g. open list).

• Blinding of participants and personnel (checking for possible performance bias). We will assess the methods used to blind study participants and personnel from knowledge of which intervention a participant received. We will assess methods as: low risk of bias (study states that it was blinded and describes the method used to achieve blinding, such as identical tablets matched in appearance or smell, or a double‐dummy technique); unclear risk of bias (study states that it was blinded but does not provide an adequate description of how it was achieved).

• Blinding of outcome assessment (checking for possible detection bias). We will assess the methods used to blind study participants and outcome assessors from knowledge of which intervention a participant received. We will assess the methods as: low risk of bias (study has a clear statement that outcome assessors were unaware of treatment allocation, and ideally describes how this was achieved); unclear risk of bias (study states that outcome assessors were blind to treatment allocation but lacks a clear statement on how it was achieved).

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

• Size of study (checking for possible biases confounded by small size (Dechartres 2013; Nüesch 2010)). 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); high risk of bias (fewer than 50 participants per treatment arm).

Measures of treatment effect

We will use dichotomous data to calculate risk ratios (RR) with 95% confidence intervals (CI) using a fixed‐effect model, and calculate numbers needed to treat for one additional beneficial outcome (NNT) as the reciprocal of the absolute risk reduction (McQuay 1998). In the event of significant statistical heterogeneity, we will consider using a random‐effects model. For unwanted effects, the number needed to treat (NNT) becomes the number needed to treat for one additional harmful outcome (NNTH), and is calculated in the same manner.

We will use the following terms to describe adverse outcomes in terms of harm or prevention of harm.

• When significantly fewer adverse outcomes occur with tramadol with or without paracetamol than with control (placebo or active control), we will use the term number needed to treat to prevent one event (NNTp).

• When significantly more adverse outcomes occur with tramadol with or without paracetamol compared with control (placebo or active control) we will use the term number needed to treat for an additional harmful outcome or cause one event (NNH).

We do not plan to use continuous data for the primary outcome because it is inappropriate where there is an underlying skewed distribution, as is usually the case with analgesic response.

Unit of analysis issues

The unit of randomisation will be the individual participant.

Dealing with missing data

We plan to use intention‐to‐treat (ITT) analyses: participants who were randomised, took the study medication, and gave a minimum of one post‐baseline assessment. We will report per‐protocol data in the absence of anything else.

Assessment of heterogeneity

We will assess statistical heterogeneity using L'Abbé plots, a visual method for assessing differences in results of individual studies (L'Abbé 1987), and by use of the I² statistic. We anticipate that there may be an effect of differences between participants, environment (inpatient versus outpatient), and outcome measures. We plan to explore these with subgroup and sensitivity analyses where there are sufficient data.

Assessment of reporting biases

We aim to use dichotomous data of known utility (Moore 2010). The review will not depend on what authors of the original studies chose to report or not.

We will undertake an assessment of publication bias if there are sufficient data for meta‐analysis, 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).

Data synthesis

If data are sufficient, we will undertake a quantitative synthesis and present data in forest plots. We will analyse studies of tramadol alone separately from the tramadol plus paracetamol combination. In the event of substantial heterogeneity, we will switch off the totals in the forest plots.

• We will undertake a meta‐analysis only if participants, interventions, comparisons, and outcomes are judged to be sufficiently similar to ensure an answer that is clinically meaningful.

• We will use Review Manager 5 for meta‐analysis (RevMan 2014) and Excel for NNTs and NNHs.

Subgroup analysis and investigation of heterogeneity

We will analyse separately the data for tramadol alone and tramadol plus paracetamol. If data allow, we will carry out sensitivity analyses for age of participants (younger than 18 years versus 18 years or older).