Types of studies

We included studies of double‐blind trials of single dose oral ibuprofen plus paracetamol compared with placebo or the same dose of ibuprofen alone, for the treatment of moderate to severe postoperative pain in adults, with at least 10 participants randomly allocated to each treatment group. We included multiple dose studies if appropriate data from the first dose were available, and cross‐over studies provided that data from the first arm were presented separately.

We excluded the following:

• review articles, case reports, and clinical observations;

• studies of experimental pain;

• studies where pain relief is assessed only by clinicians, nurses, or carers (i.e. not patient‐reported);

• studies of less than four hours duration or studies that fail to present data over four to six hours post dose.

For postpartum pain, we included studies if the pain investigated was due to episiotomy or Caesarean section irrespective of the presence of uterine cramps; we excluded studies investigating pain due to uterine cramps alone.

Types of participants

We included studies of adult participants (> 15 years) with established postoperative pain of moderate to severe intensity following day surgery or in‐patient surgery. For studies using a visual analogue scale (VAS), we considered that pain intensity of greater than 30/100 mm equates to pain of at least moderate intensity (Collins 1997).

Types of interventions

Ibuprofen plus paracetamol, administered as a single oral dose, compared with matched placebo or the same dose of ibuprofen alone for postoperative pain. The ibuprofen and paracetamol had to be administered as separate tablets taken together, or in a combined tablet. We included all dose combinations.

Types of outcome measures

We collected the following data where available:

• participant characteristics;

• patient reported pain at baseline (physician, nurse, or carer reported pain was not included in the analysis);

• patient reported pain relief expressed at least hourly over four to six hours using validated pain scales (pain intensity and pain relief in the form of VAS or categorical scales, or both);

• patient global assessment of efficacy (PGE), using a standard categorical scale;

• time to use of rescue medication;

• number of participants using rescue medication;

• number of participants with one or more adverse events;

• number of participants with serious adverse events;

• number of withdrawals (all‐cause, adverse events).

Electronic searches

We searched the following databases:

• The Cochrane Central Register of Controlled Trials (CENTRAL) on The Cochrane Library, (Issue 4 of 12, 2013);

• MEDLINE (via OVID) (1950 to 21 May 2013);

• EMBASE (via OVID) (1974 to 21 May 2013);

• Oxford Pain Relief Database (Jadad 1996a).

See Appendix 1 for the MEDLINE search strategy, Appendix 2 for the EMBASE search strategy, and Appendix 3 for the CENTRAL search strategy. We did not limit the searches by language.

Searching other resources

We searched for additional studies in reference lists of retrieved articles and reviews, and in clinicaltrials.gov. The manufacturers of the combination formulation (Reckitt Benckiser) had already supplied information on published and unpublished studies.

Selection of studies

Two review authors independently assessed and agreed the search results for studies to be included in the review. Disagreements would be resolved by consensus or referral to a third review author.

Data extraction and management

Two review authors extracted data and recorded them on a standard data extraction form. One review author entered data suitable for pooling into RevMan 5.1 (RevMan 2011).

Assessment of risk of bias in included studies

Two review authors independently assessed each study for methodological quality using a three‐item, five‐point scale (Jadad 1996b), and agreed a consensus score.

The scale used is as follows.

• Is the study randomised? If yes ‐ one point.

• Is the randomisation procedure reported and is it appropriate? If yes add one point, if no deduct one point.

• Is the study double‐blind? If yes add one point.

• Is the double‐blind method reported and is it appropriate? If yes add one point, if no deduct one point.

• Are the reasons for patient withdrawals and dropouts described? If yes add one point.

We also completed a 'Risk of bias' table, using methods adapted from those described by the Cochrane Pregnancy and Childbirth Group. Two authors independently assessed risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) with any disagreements resolved by discussion.  The following were assessed for each study.

• Random sequence generation (checking for possible selection bias). The method used to generate the allocation sequence was assessed as: low risk of bias (any truly random process, e.g. random number table; computer random number generator);  high risk of bias (any non‐random process, e.g. odd or even date of birth; hospital or clinic record number) ‐ these studies would be excluded; unclear risk of bias.

• Allocation concealment (checking for possible selection bias).  The method used to conceal allocation to interventions prior to assignment assessed whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment. The methods were assessed as: low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes); high risk of bias (open random allocation; unsealed or non‐opaque envelopes, alternation; date of birth) ‐ theses studies would be excluded; unclear risk of bias.

• Blinding of outcome assessment (checking for possible detection bias). The methods used to blind study participants and outcome assessors from knowledge of which intervention a participant received were assessed. Studies were considered to be at low risk of bias if they stated that they were blinded and described the method used to achieve blinding (e.g. identical tablets; matched in appearance and smell), or at unknown risk if they stated that they were blinded, but did not provide an adequate description of how it was achieved. Single blind and open studies would be excluded.

• Size (checking for possible biases confounded by small size). Small studies have been shown to overestimate treatment effects, probably due to methodological weaknesses (Nuesch 2010). Studies were considered to be at low risk of bias if they had ≥ 200 participants, at unknown risk of they had 50 to 200 participants, and at high risk if they had < 50 participants.

Measures of treatment effect

We used relative risk (or 'risk ratio', RR) to establish statistical difference. We used numbers needed to treat (NNT) and pooled percentages as absolute measures of benefit or harm.

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

• When significantly fewer adverse outcomes occur with treatment than with control (placebo or active) we use the term the number needed to treat to prevent one event (NNTp).

• When significantly more adverse outcomes occur with treatment compared with control (placebo or active) we use the term the number needed to harm or cause one event (NNH).

Unit of analysis issues

We accepted only randomisation to the individual patient.

Dealing with missing data

The only likely issue with missing data in these studies is from imputation using last observation carried forward when a patient requests rescue medication. We have previously shown that this does not affect results for up to six hours after taking study medication (Barden 2004).

Assessment of heterogeneity

We examined heterogeneity visually using L'Abbé plots (L'Abbé 1987), a visual method for assessing differences in results of individual studies.

Data synthesis

We followed QUOROM guidelines (Moher 1999). For efficacy analyses we used the number of participants in each treatment group who were randomised, received medication, and provided at least one post‐baseline assessment. For safety analyses we used number of participants randomised to each treatment group who took the study medication. We planed to analyse for different doses separately.

For each study we converted the mean TOTPAR, SPID, VAS TOTPAR, or VAS SPID (Appendix 4) values for active and placebo to %maxTOTPAR or %maxSPID by division into the calculated maximum value (Cooper 1991), and calculated the proportion of participants in each treatment group who achieved at least 50%maxTOTPAR using verified equations (Moore 1996; Moore 1997a; Moore 1997b). We then converted these proportions into the number of participants achieving at least 50%maxTOTPAR by multiplying by the total number of participants in the treatment group. We used this information on the number of participants with at least 50%maxTOTPAR for active and placebo to calculate relative benefit or relative risk, and number needed to treat to benefit (NNT) or harm (NNH). Because adverse events with ibuprofen/paracetamol combinations were less frequent than with placebo, this is described as an NNTp, the number needed to treat to prevent an adverse event. NNTp was also used to describe differences in remedication rates, where remedication rates were lower with active treatment than control.

We accepted the following pain measures for the calculation of TOTPAR or SPID:

• five‐point categorical pain relief (PR) scales with comparable wording to 'none, slight, moderate, good or complete';

• four‐point categorical pain intensity (PI) scales with comparable wording to 'none, mild, moderate, severe';

• VAS for pain relief;

• VAS for pain intensity.

If none of these measures was available, we would use the number of participants reporting 'very good or excellent' on a five‐point categorical global scale with the wording 'poor, fair, good, very good, excellent' for the number of participants achieving at least 50% pain relief (Collins 2001).

For each treatment group we extracted the number of participants reporting treatment‐emergent adverse effects, and calculated relative benefit and risk estimates with 95% confidence intervals (CI) using a fixed‐effect model (Morris 1995). We calculated NNT and NNH with 95% CIs using the pooled number of events using the method devised by Cook and Sackett (Cook 1995). We assumed a statistically significant difference from control when the 95% CI of the relative risk or relative benefit did not include the number one.

Subgroup analysis and investigation of heterogeneity

We planned subgroup analyses to determine the effect of dose and presenting condition (pain model: dental versus other postoperative pain). A minimum of two studies and 200 participants had to be available in any subgroup or sensitivity analysis (Moore 1998), which was restricted to the primary outcome (50% of maximum pain relief over four to six hours) and the dose with the greatest amount of data. We determined significant differences between NNT, NNTp, or NNH for different groups in subgroup and sensitivity analyses using the z test (Tramèr 1997).

Sensitivity analysis

We planned sensitivity analyses for quality score (two versus three or more) and trial size (39 or fewer versus 40 or more per treatment arm).