Types of studies

We included randomized controlled trials (RCTs), with at least 10 participants randomly allocated to each treatment group. We only included trials that conducted a double‐blind assessment of participant outcomes. We included multiple‐dose studies if appropriate data from the first dose were available, and cross‐over studies provided that data from the first phase were presented separately or can be obtained.

We excluded:

• non‐randomized studies;

• review articles, case reports, and clinical observations;

• studies of experimental pain;

• studies of less than 4 hours' duration or studies that do not present data over 4 to 6 hours postdose;

• studies where ibuprofen was administered preoperatively or intraoperatively;

• studies where pain was not patient‐reported.

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

We required full journal publication, with the exception of online clinical trial results, summaries of otherwise unpublished clinical trials, and abstracts with sufficient data for analysis. For an abstract with insufficient data, we assumed that if the study was valid, the investigators would publish its data in full within 3 years. If not, we excluded it without attempting to contact authors.

Types of participants

We included studies of adults (aged 18 years and above) with established postoperative pain of moderate‐to‐severe intensity following day surgery or inpatient surgery. For studies using a visual analog scale (VAS) (see Glossary: Appendix 1), we considered that pain intensity of greater than 30 mm equates to pain of at least moderate intensity (Collins 1997). We excluded studies that included participants with mild pain, unless they presented data for those with moderate‐to‐severe pain separately.

Types of interventions

We included studies that delivered ibuprofen, administered as a single intravenous (IV) dose, for the relief of acute postoperative pain, compared to placebo or any active comparator. The minimum dose studied was 200 mg with primary analysis on the dose most commonly studied. We planned to assess separate doses if there were enough studies/participants to justify meaningful analysis.

Types of outcome measures

Electronic searches

We searched the following databases without language restrictions.

• The Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library, Issue 4 of 12, 2020.

• MEDLINE & MEDLINE in Process (via Ovid) 1946 to 6 April 2020.

• Embase (via Ovid) 1974 to 2020 week 14.

• LILACS (ilacs.bvsalud.org/en/) to April 2020.

We used medical subject headings (MeSH) or equivalent and text word terms. We tailored searches to individual databases. The search strategies used can be found in Appendix 2. We updated the search (same search strategy) on 10 June 2021. 

Searching other resources

We attempted to mitigate the potential for publication bias by searching clinical trial websites, ClinicalTrials.gov (www.clinicaltrials.gov), and the World Health Organization International Clinical Trials Registry Platform (ICTRP) (apps.who.int/trialsearch/) 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 contacted the manufacturer of parenteral ibuprofen for an internal reference list of completed studies. We also contacted experts in the field for unpublished and ongoing trials. We contacted study authors for additional information where necessary. If a published protocol was not available, we did not contact study authors if the outcomes listed in their Methods section were those that we would expect from similar studies and if these outcomes were reported in full in the Results section.

Selection of studies

Two review authors (a combination of MF, SG, EM, and RS) independently determined eligibility by reading the abstract of each study identified by the search. We eliminated studies that clearly did not satisfy inclusion criteria, and obtained full copies of the remaining studies. Two review authors (a combination of MF, SG, EM, and RS) independently read these studies to select relevant studies, and, in the event of disagreement, the third review author adjudicated. We did not anonymize the studies before assessment.

We included a PRISMA flow chart showing the status of identified studies (Moher 2009), as recommended in Section 14.1.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2021). We included studies in the review irrespective of whether measured outcome data were reported in a 'usable' way.

Data extraction and management

Two review authors (MF, EM) independently extracted data using a previously piloted standard form and checked for agreement before entry into RevMan Web (RevMan Web 2020). In the event of disagreement, a third review author could adjudicate (SG or RS). We extracted:

• study methods;

• study population (e.g. baseline pain, concurrent medications, number of participants enrolled and completing);

• interventions;

• pain intensity scale used and baseline pain intensity;

• outcomes of interest. We extracted efficacy outcomes for the 6 hours postadministration of interventions. We extracted safety outcomes for the duration of the study.

We collated multiple reports of the same study, so that each study, rather than each report, is the unit of interest in the review. We collected information and sufficient detail to complete the Characteristics of included studies table.

Assessment of risk of bias in included studies

Two review authors (MF, EM) 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. We completed a risk of bias table for the included study (RevMan Web 2020).

We assessed the following for each study.

• 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, e.g. random number table; computer random number generator); unclear risk of bias (method used to generate sequence was not clearly stated). We excluded 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 assessed the methods as: low risk of bias (e.g. telephone or central randomization; consecutively numbered sealed opaque envelopes); unclear risk of bias (method not clearly stated). We excluded studies that did not conceal allocation (e.g. open list).

• Blinding of participants and personnel (checking for possible performance bias). We assessed the methods used to blind study participants and personnel from knowledge of which intervention a participant received. We assessed methods as: low risk of bias (study stated that it was blinded and described 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 stated that it was blinded but did not provide an adequate description of how it was achieved). We excluded studies that were not double‐blind due to the high risk of bias.

• Blinding of outcome assessment (checking for possible detection bias). In this review, pain‐related outcomes were self‐assessed, so that the same considerations apply to detection bias as performance bias.

• Selective reporting (checking for reporting bias). We assessed whether primary and secondary outcome measures were prespecified and whether these were consistent with those reported. We assessed reporting of results as having low risk of bias (e.g. the study protocol was available and all of the study's prespecified outcomes of interest in the review were reported in the prespecified way; the study protocol was not available, but it is clear that published reports included all expected outcomes, including those that were prespecified); high risk of bias (e.g. not all of the study's prespecified primary outcomes were reported; one or more primary outcome(s) were reported using measurements, analysis methods, or subsets of data that were not prespecified); or unclear risk of bias (information insufficient to permit judgment of 'low risk' or 'high risk').

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

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

Measures of treatment effect

We planned to use risk ratio (RR) to establish statistical differences, and number needed to treat for one additional beneficial outcome (NNTB) with 95% confidence intervals (95% CIs), and pooled percentages as absolute measures of effect.

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

• When fewer adverse outcomes occurred with treatment than with control (placebo or active), we used the term 'number needed to treat to prevent one additional harmful event' (NNTp).

• When more adverse outcomes occurred with treatment compared with control (placebo or active), we used the term 'number needed for one additional harmful event' (NNTH).

Unit of analysis issues

We accepted only randomization of individual participants. If two or more active treatment arms were compared with a placebo arm within the same meta‐analysis, we planned to avoid double‐counting of participants in the placebo arm by splitting the total number between the active arms. If we identified multiple‐dose studies, we planned to use data for the most commonly used dose only; and for cross‐over studies, we planned to use data from the first treatment phase.

Dealing with missing data

One anticipated issue with missing data in these studies was imputation using LOCF when a participant requested rescue medication. It has been shown that this does not affect results for up to 6 hours after taking study medication (Moore 2005). If large amounts of data were missing, we planned to report this in our review and assess such results with caution. We consulted the Cochrane Handbook for Systematic Reviews of Interventions for guidance (Higgins 2021b). Where papers reported results using more than one method of imputation, we planned to analyze data using the primary method reported and perform sensitivity analysis by entering data from secondary methods. We also planned to assess differences between intervention groups in reasons for missing data and how these differences might bias results.

Assessment of heterogeneity

We planned to assess statistical heterogeneity by visually examining forest plots and quantifying it by using the I² statistic. The I² statistic is a reliable and robust test to quantify heterogeneity, since it does not depend on the number of trials or on the between‐study variance. The I² statistic measures the extent of inconsistency among studies' results, and can be interpreted as the proportion of total variation in study estimates that is due to heterogeneity rather than sampling error. An I² value of greater than 50% is considered to indicate substantial heterogeneity (Deeks 2021). If heterogeneity was high (I² greater than 50%), we planned to consider possible reasons including the influence of small studies.

Assessment of reporting biases

To assess the impact of reporting bias, we planned to consider the number of additional participants needed in studies with zero effect (relative benefit of 1) required to change the number needed to treat (NNT) for all statistically significant outcomes to an unacceptably high level (in this case the arbitrary NNT of 10) (Moore 2008). If this number was less than 400 (equivalent to 4 studies with 100 participants per comparison, or 50 participants per group), we would consider the results to be susceptible to publication bias and therefore unreliable (low‐certainty evidence).

We also planned to mitigate the potential for publication bias by searching clinical trial websites, and by contacting the manufacturers of parenteral ibuprofen for an internal reference list of completed studies (see Searching other resources).

Data synthesis

For efficacy analyses, we planned to use the number of participants in each treatment group who were randomized, received medication, and provided at least one postbaseline assessment. For safety analyses, we planned to use the number of participants randomized to each treatment group who took the study medication.

For the primary outcome (number of participants achieving at least 50% pain relief over a 4‐hour period and over a 6‐hour period), if numbers were not reported directly, we planned to convert the mean total pain relief (TOTPAR), or summed pain intensity difference (SPID), VAS TOTPAR, or VAS SPID (see Glossary: Appendix 1) values for the active and placebo groups in each study to %maxTOTPAR or %maxSPID by division into the calculated maximum value (Cooper 1991). We planned to then calculate the proportion of participants in each treatment group who achieved at least 50%maxTOTPAR using verified equations, and convert these proportions into the number of participants achieving at least 50%maxTOTPAR by multiplying by the total number of participants in the treatment group (Moore 1996; Moore 1997a; Moore 1997b). We planned to use this information on the number of participants with at least 50%maxTOTPAR for active and placebo groups to calculate RR and NNT.

We planned to accept the following pain measures for the calculation of TOTPAR or SPID (in order of priority: see Appendix 1).

• 5‐point categorical pain relief scales with comparable wording to 'none', 'slight', 'moderate', 'good', and 'complete'

• 4‐point categorical pain intensity scales with comparable wording to 'none', 'mild', 'moderate', and 'severe'

• VAS for pain relief

• VAS for pain intensity

If none of these measures were available, we planned to use the number of participants experiencing 'very good or excellent' on a 5‐point categorical global scale with the wording 'poor', 'fair', 'good', 'very good', and 'excellent' for the number of participants achieving at least 50% pain relief (Collins 2001).

For dichotomous outcomes, we planned to calculate RR estimates with 95% CIs using the Mantel‐Haenszel method in RevMan Web (RevMan Web 2020). We planned to calculate NNTB and NNTH with 95% CIs using the pooled number of events and the method of Cook and Sackett (Cook 1995). We planned to assume a statistically significant difference from control when the 95% CI of the RR did not include the number 1.

For continuous outcomes, such as time to rescue medication, we planned to pool mean scores using the inverse variance method in RevMan Web (RevMan Web 2020). We planned to assume a statistically significant difference from control when the 95% CI of the mean difference between interventions did not include the number 1.

If a meta‐analysis had an I² score of greater than 50%, we reanalyzed data using a random‐effects model and presented the analysis using this model (Deeks 2021, see Sensitivity analysis).

Subgroup analysis and investigation of heterogeneity

We planned to analyze different doses (400 mg and 800 mg) separately. We also planned to analyze different surgeries, as postoperative pain levels and analgesic efficacy may differ (Sommer 2008). We planned to use the Z test to explore whether there were differences between subgroups (Tramèr 1997), if appropriate.

Sensitivity analysis

For meta‐analyses with an I² score greater than 50%, we planned to reanalyze data using a random‐effects model. We preferentially present the data for these reanalyses within the Effects of interventions section rather than presenting them initially as fixed‐effect analyses.

Summary of findings and assessment of the certainty of the evidence

Two review authors (MF, EM) independently rated the certainty of the outcomes. We used the GRADE system to rank the certainty of the evidence using the GRADEprofiler Guideline Development Tool, and the guidelines provided in the CochraneHandbook for Systematic Reviews of Interventions (GRADEpro GDT; Schünemann 2021). We reported our judgment on the certainty of evidence in the summary of findings table.

The GRADE approach uses five considerations (risk of bias, consistency of effect, imprecision, indirectness, and publication bias) to assess the certainty of the body of evidence for each outcome. The GRADE system uses the following criteria for assigning grade of evidence.

• High: we are very confident that the true effect lies close to that of the estimate of the effect.

• Moderate: we are moderately confident in the effect estimate; the true effect is likely to be close to the estimate of effect, but there is a possibility that it is substantially different.

• Low: our confidence in the effect estimate is limited; the true effect may be substantially different from the estimate of the effect.

• 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.

The GRADE system uses the following criteria for assigning a level of certainty to a body of evidence (Higgins 2021a).

• High: randomized trials; or double‐upgraded observational studies

• Moderate: downgraded randomized trials; or upgraded observational studies

• Low: double‐downgraded randomized trials; or observational studies

• Very low: triple‐downgraded randomized trials; or downgraded observational studies; or case series/case reports

Factors that may decrease the certainty of a body of evidence are:

• limitations in the design and implementation of available studies suggesting high likelihood of bias;

• indirectness of evidence (indirect population, intervention, control, outcomes);

• unexplained heterogeneity or inconsistency of results (including problems with subgroup analyses);

• imprecision of results (wide CIs);

• high probability of publication bias.

We decreased the grade rating by one (–1) or two (–2) (up to a maximum of –3 to 'very low') if we identified:

• serious (–1) or very serious (–2) limitation to study certainty;

• important inconsistency (–1);

• some (–1) or major (–2) uncertainty about directness;

• imprecise or sparse data (–1);

• high probability of reporting bias (–1).

We paid particular attention to:

• inconsistency, where point estimates vary widely across studies or CIs of studies show minimal or no overlap (Guyatt 2011);

• potential for publication bias, based on the amount of unpublished data required to make the result clinically irrelevant (Moore 2008).

In addition, there may be circumstances where the overall rating for a particular outcome needs to be adjusted as recommended by GRADE guidelines (Guyatt 2013a). For example, if there were so few data that the results were highly susceptible to the random play of chance, or if studies use LOCF imputation in circumstances where there were substantial differences in AE withdrawals, one would have no confidence in the result, and would need to downgrade the certainty of the evidence by three levels, to very low. In circumstances where there were no data reported for an outcome, we reported the level of evidence as very low (Guyatt 2013b).