Diclofenac for acute postoperative pain in children

Objectives

This is a protocol for a Cochrane Review (intervention). The objectives are as follows:

To assess the efficacy and safety of diclofenac (any dose) for acute postoperative pain management in children compared with placebo, other active comparators, or diclofenac administered by either different routes (e.g. oral, rectal, etc.) or strategies (e.g. as needed versus as scheduled).

Background

Description of the condition

Surgery is common in children. It is known that a large number of hospitalised children experience pain, and children who undergo surgery frequently report more pain than children going through other medical treatments (Kozlowski 2014). In the US alone, approximately 5% of children below the age of 18 years have a surgical procedure each year, which accounts for approximately 3.9 million surgeries annually (Rabbitts 2020). Surgical procedures might be required for musculoskeletal traumas, wounds, injuries (e.g. burns), congenital anomalies (e.g. cleft palate), or diseases related to the throat (e.g. infection of the tonsils), abdomen (e.g. hernia), eye (e.g. strabismus), ear (e.g. otitis media), or teeth (e.g. dental implant) (Ostlie 2010).

For example, one study found all children reported pain after tonsillectomy one day after the procedure, and over 50% of the children reported pain at some point seven days after surgery. In addition, most children's return to and performance in usual activities were limited during the seven days after surgery (Stewart 2012). Studies measuring postoperative pain in children across various surgical procedures reported moderate to severe pain in 25% (Avian 2016) and 40.5% (95% confidence interval (CI) 32.7% to 48.4%) (Mekonnen 2021) within the first day after surgery.

The pain reported after surgery may be related to the presurgical condition or to perioperative practice (e.g. physical position and anaesthesia), or both. Tissue damage resulting from surgery may cause pain, which can be acute or develop into long‐term pain. Acute pain is defined by the ACTTION‐APS AAPT (Analgesic, Anesthetic, and Addiction Clinical Trial Translations Innovations Opportunities and Networks American Pain Society Pain Taxonomy) as pain lasting up to seven days, with the following qualifications: 1. the duration will reflect the mechanisms and severity of the underlying event; 2. lengthening of pain from seven to 30 days is common; 3. lengthening beyond the duration of acute pain but not extending past 90 days; and 4. the understanding of pain mechanisms is currently insufficient to link these durations to specific physiological mechanisms (Kent 2017). Acute postoperative pain can occur due to inflammation, tissue damage or nerve injury or a combination of these as a result of the surgery. Acute pain after a surgical procedure can influence recovery and quality of life. Uncontrolled acute pain could also lead to sensitisation of pain and increase the risk of developing long‐term pain (Fletcher 2015).

Acute postoperative pain management is a critical part of patient care to reduce pain and ensure optimal recovery. To manage postoperative pain effectively and diminish the consequences of pain following surgery, it is essential to be able to measure pain. Self‐report of pain severity is considered the best available approach to measuring pain in children over six years of age, but children below six years of age will often express the pain in non‐verbal ways and, therefore, it is recommended to assess pain through behavioural pain scales (e.g. observer‐reported pain) in younger children (Stinson 2006). 

Postoperative pain management includes different strategies such as pharmacological and non‐pharmacological approaches. Examples of non‐pharmacological interventions recommended in guidelines include rest, distraction, physical activity, heat‐pads or cold compresses. Furthermore, a wide range of medicines can be recommended, including opioids (e.g. codeine, morphine, tramadol and fentanyl), non‐steroidal anti‐inflammatory drugs (NSAIDs) (e.g. naproxen, ibuprofen and diclofenac) or paracetamol (Gai 2020). It is common to combine different pain management strategies, which allows reduction of the dose thus possibly reducing the risk of harm (Verghese 2010).

Description of the intervention

NSAIDs are a well‐established class of medicines used since 1966 to treat symptoms such as pain and swelling (Sallmann 1986). Globally, diclofenac is one of the most widely used NSAIDs (McGettigan 2013). Diclofenac is used as an analgesic and anti‐inflammatory treatment, and is recommended for both long‐ and short‐term use in a variety of conditions, for example after tonsillectomy (Warltier 2003) or hernia repair (Riad 2007) in children. 

As NSAIDs may cause gastric irritation and can affect platelet aggregation, their use may increase the risk of bleeding, ulceration, nausea and vomiting (Odom 2014). In adults, diclofenac has also been associated with a higher risk of cardiovascular events than non‐use and use of other NSAIDs (Schmidt 2018), and is associated with kidney injury (Forrest 2002); these potential effects in children are not very well reported. 

The main routes of administration for diclofenac are orally, rectally and by injection (Standing 2011). Another route of administration of diclofenac is by topical gels, lotions or patches (Banning 2008). The recommended dose of diclofenac depends on the delivery mode and the age and weight of the child. For example, for children aged 12 to 16 years (45 kg to 55 kg) orally administered diclofenac in doses of 25 mg can be recommended up to three or four times a day and for children aged nine to 11 years (35 kg to 44 kg) up to three times a day (FASS 2020a). In addition, diclofenac administered rectally in children over six years of age the recommended dose can be 25 mg up to three times a day (FASS 2020b), but, when administered in the form of an injection, approximately half the dose is usually recommended (Standing 2011). Bioavailability in children also may be higher when diclofenac is administered rectally compared with orally (Marel 2004).

Timing of administration of diclofenac might vary: it can be delivered preoperatively, during the operation (intraoperatively) or postoperatively to manage pain. Intraoperatively, diclofenac may be administered alone or together with local anaesthesia in circumstances when a child's pain may be detected through behaviour or talking with the child; or it may be delivered without assessing the presence of pain but when postoperative pain is anticipated. In addition, diclofenac can be administered on an as‐needed basis (i.e. based on individual pain scores) and 'as scheduled' (e.g. every eight hours). 

How the intervention might work

NSAIDs have antipyretic, antiplatelet, anti‐inflammatory and analgesic effects (Verghese 2010). They are considered clinically beneficial for minor postoperative pain control, but it is not yet clear which pharmacological agent is best for postoperative pain. After major surgery, NSAIDS may have an opioid‐sparing effect on pain (Grahame‐Smith 2002). One blinded randomised controlled trial (RCT) demonstrated that administering NSAIDs postoperatively reduced adults' opioid requirements, thus potentially reducing opioid‐induced adverse event (AE) incidence and severity; whether this applies to children needs further exploration (Cepeda 2005).

Pain may result from tissue damage or by inflammatory mediators that act on nerve endings (e.g. bradykinin, 5‐hydroxytryptamine). The hormone prostaglandin, sensitises the nerve endings to the inflammatory mediators heightening pain (Kokki 2003). The analgesic effects of NSAIDs are indirect and largely mediated by reducing prostaglandin synthesis, thus reducing sensitisation by the inflammatory mediators (FitzGerald 2004). NSAIDS inhibit the cyclo‐oxygenase (COX) isoenzymes 1 and 2, whose role is to produce prostaglandins and thromboxane A2 (Fineschi 1997). Thromboxane A2 is responsible for platelet aggregation and vasoconstriction (Kokki 2003). Prostaglandins play a protective role in the vascular system, kidneys and gastrointestinal tract. Consequently, inhibiting prostaglandins and thromboxane A2 by inhibiting COX may contribute to the AE profile of NSAIDs, particularly gastric ulceration and bleeding (McNicol 2018a).

Overall, the actions of NSAIDs of inhibiting prostaglandins and thromboxane A2 production may be effective for pain management, but can result in AEs involving the gastrointestinal, haematological, cardiovascular and renal systems. In addition, a postoperative patient with potential blood volume depletion depends on prostaglandins to support renal function and, therefore, are at increased risk of developing NSAID‐induced kidney injury (Patrono 2001). Older references suggest that NSAIDs, more than any other medicines, are mentioned in drug toxicity reports (Hawkey 2002). However, more recent overviews propose that the evidence base is uncertain and more trials to understand the benefits and harms are needed (Boric 2017). Toxicity risk factors are therapy dosage and duration, including pre‐existing renal impairment and the patient's age.

Diclofenac is classified as a benzene acetic acid derivative (Fineschi 1997). Diclofenac is plasma bound, in particular to albumin. It goes through considerable first‐pass metabolism (Todd 1988), predominantly through 4'‐hydroxylation by cytochrome P450 (CYP) 2C9. In addition, 5'‐hydroxylation by CYP3A4, CYP2C19, CYP2C8 and CYP2C18 occurs (Kirchheiner 2003). Furthermore, diclofenac is excreted in the bile and urine as sulphate and glucuronide conjugates (Todd 1988). Depending on the child's developmental stage, one may find differing capacities for metabolism, conjugation and elimination of drugs (Kearns 2003; Morselli 1980).

Why it is important to do this review

Existing systematic reviews focus on the general perioperative use of NSAIDs in children (Krishna 2003; Rømsing 1997). However, a review from 2018 evaluated the efficacy and safety of ketorolac for postoperative pain management in children (McNicol 2018b). Still, we have not identified any more‐recent published systematic reviews assessing the effects of diclofenac for managing acute postoperative pain in children. Promisingly, one Cochrane Review evaluating acute postoperative pain management in adults reported that single‐dose intravenous diclofenac may be over two times more effective in relieving pain over four hours (low‐certainty evidence) and nearly four times more effective in relieving pain over six hours (low‐certainty evidence) when compared with placebo (McNicol 2018a).

For postoperative analgesia in children, diclofenac may offer a low‐cost, accessible yet effective analgesic alternative and reduce opioid use. Of note, opioids are administered to newborn infants following surgery (Kinoshita 2021a; Kinoshita 2021b); however, they are less preferred to NSAIDs due to their potential harms. AEs of opioids in children include nausea, vomiting, skin itching, constipation and respiratory depression. As noted with NSAIDs, there are concerns about prolonged postoperative site bleeding, vomiting, impaired renal function and bronchospasm among other AEs. These are factors that healthcare providers may consider when weighing up the balance of benefits and harms of diclofenac use. In adults, one Cochrane Review assessed the incidence and severity of these AEs reporting little difference between diclofenac and placebo with low‐ to moderate‐certainty evidence (McNicol 2018a). This should be further explored and evaluated for children.

Diclofenac is widely used in children for acute pain (Conroy 2001; Turner 1998), but its utility for postoperative pain management is not well reported. Therefore, this Cochrane Review will aim to assess the safety and efficacy of diclofenac specifically in children and address the current knowledge gap comparing diclofenac to other options for pain management. 

This Cochrane Review will replace the withdrawn Cochrane Review published in 2015 (Standing 2015).

Objectives

To assess the efficacy and safety of diclofenac (any dose) for acute postoperative pain management in children compared with placebo, other active comparators, or diclofenac administered by either different routes (e.g. oral, rectal, etc.) or strategies (e.g. as needed versus as scheduled).

Methods

Criteria for considering studies for this review

Types of studies

We will include RCTs with blinding of outcome assessment and blinding of participants and personnel to minimise detection bias and performance bias for comparisons 1 and 2 (see Types of interventions). For comparisons 2 and 3, where blinding is difficult to attain, we will include all RCTs regardless of blinding. Randomised trials are the best design to minimise bias when evaluating the effectiveness of an intervention.

We will include individual, cluster and cross‐over trials (see Unit of analysis issues). 

We will include peer‐reviewed publications, online clinical trial results, summaries of otherwise unpublished clinical trials and abstracts; if there are insufficient data, we will attempt to locate the full study (e.g. by contacting the study authors). If the data from the full study are unavailable, we will add the abstract to the studies awaiting classification section.

We will exclude non‐randomised studies, experimental studies using pain induction, case reports and clinical observations.

Types of participants

We will include studies of children aged 17 years and below treated for acute postoperative pain. 

We will address studies including both children and adults by contacting study authors to obtain outcome data for the children. If unsuccessful, we will exclude the study if the mean age of the included participants is above 17 years. We will include any type of procedure or surgery (including dental and laparoscopy).

We will exclude studies on chronic pain, where diclofenac was primarily used for treating pain beyond seven days and pain that is not associated with surgery.

Types of interventions

We will include the following comparisons:

• comparison 1: diclofenac versus placebo;

• comparison 2: diclofenac versus active pharmacological comparator, that is, opioids (e.g. codeine, morphine, papaveretum, tramadol, nalbupine, pethidine), dexamethasone, betamethasone, fluorometholone, naproxen, ibuprofen, paracetamol, bupivacaine, lignocaine, pranoprofen, ketorolac, flurbiprofen, clonidine, dexmedetomidine and tenoxicam. We will not pool RCTs where diclofenac is compared with different drugs (e.g. diclofenac versus tramadol with diclofenac versus ibuprofen) in the same analysis;

• comparison 3: different routes of diclofenac administration (e.g. oral versus rectal);

• comparison 4: as needed diclofenac administration (e.g. based on pain scales) versus as scheduled (e.g. a predefined time interval). Route and dose have to be the same in both arms.

We will include any dose, timing and route of administration, both systemically (e.g. oral, rectal, intramuscular, intravenous) and topically (e.g. gel).

We will include studies where co‐interventions are administered to both arms (e.g. diclofenac plus paracetamol versus placebo plus paracetamol). We will exclude studies where co‐interventions are administered to one arm only (e.g. diclofenac plus paracetamol versus placebo without paracetamol; diclofenac without paracetamol versus placebo plus paracetamol). 

Types of outcome measures

Primary outcomes

• Pain relief – as reported by the child – defined as the proportion of participants with 50% or greater postoperative pain relief in each treatment arm at specific time points (i.e. less than two hours; two to 24 hours; more than 24 hours and up to seven days) postintervention (dichotomous outcome).

• Pain intensity – as reported by the child – assessed with a validated pain scale (continuous outcome). We will report mean postoperative pain intensity over various time points (i.e. less than two hours; two to 24 hours; more than 24 hours and up to seven days) in each treatment arm and their corresponding standard deviations (SD).

• Adverse events (AE) (i.e. number of children experiencing any AEs or harms) (as reported by study authors).

• Serious adverse events (SAE), defined as events requiring a blood transfusion, hospitalisation or resulting in permanent damage (FDA 2016).

Secondary outcomes

• Pain relief – as reported by a third party (e.g. parents and carers) (continuous outcome) – assessed with a validated pain scale (i.e. less than two hours; two to 24 hours; more than 24 hours and up to seven days).

• Pain intensity – as reported by a third party (e.g. parents and carers) (continuous outcome) – assessed with a validated pain scale (i.e. less than two hours; two to 24 hours; more than 24 hours and up to seven days).

• Time‐to‐onset of meaningful (50%) pain relief. We will extract the mean time to achieve this degree of relief in each treatment arm and the corresponding SD.

• Number of participants who required rescue medication. We will extract the proportion of participants who received additional analgesic medication during various time points (i.e. less than two hours; two to 24 hours; more than 24 hours and up to seven days) after administering the study drugs in each treatment arm (dichotomous outcome).

• Opioid consumption. In studies that allowed co‐administration of opioids (including patient‐controlled analgesia (PCA)), we will extract the mean opioid consumption (in milligrams) over various time points (i.e. less than two hours; two to 24 hours; more than 24 hours and up to seven days) in each treatment arm and the corresponding SD. If opioid consumption is reported as milligrams per kilogram, we will convert this to milligrams by multiplying reported values by the mean weight of each study arm. We will convert opioid requirements into intravenous morphine‐equivalents, using commonly used and widely accepted opioid conversion tables.

• Time‐to‐rescue medication, as reported by the child. We will extract the mean time to requiring rescue medication in each treatment arm and the corresponding SD.

• Time‐to‐rescue medication, as reported by a third party (e.g. parents and carers). We will extract the mean time to requiring rescue medication in each treatment arm and the corresponding SD.

• Global judgement of satisfaction with treatment (either participant, using the Patients' Global Impression of Change (PGIC), or carer). We plan to extract dichotomous information from categorical global evaluations (number of participants who report the top two categories, e.g. good, satisfied, excellent or very satisfied). For visual analogue scale (VAS) ratings, we plan to extract the mean values of each intervention.

• Return to activities of daily living (ADL) (e.g. return to school and sports activities).

• Nausea or vomiting, or both (dichotomous outcome).

• Any bleeding (dichotomous outcome), including gastrointestinal bleeding and oral bleeding.

Search methods for identification of studies

Electronic searches

We will search the following databases from inception and without language restrictions. 

• Cochrane Central Register of Controlled Trials (CENTRAL) (in the Cochrane Library) (latest issue).

• MEDLINE (via Ovid).

• Embase (via Ovid).

We will tailor searches to individual databases. The search strategy for MEDLINE is in Appendix 1.

The Cochrane Pain, Palliative and Supportive Care Review Group's (PaPaS) Information Specialist will develop the search strategies, which will be independently peer‐reviewed. The Cochrane PaPaS Information Specialist will perform the searches.

Searching other resources

We will search 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 will search grey literature, 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. We will contact study authors for additional information where necessary.

Data collection and analysis

We will collect information regarding the method of randomisation, blinding, intervention, stratification and whether the trial was single or multicentre for each included study. We will note information regarding trial participants, including bodyweight, age, number of participants, modality of administration and dose of diclofenac. We will analyse the clinical outcomes noted above in Types of outcome measures.

Selection of studies

We will use Cochrane's Screen4Me workflow to help assess the search results if the search yields more than 200 results. Screen4Me comprises three components: known assessments – a service that matches records in the search results to records that have already been screened in Cochrane Crowd and been labelled as an RCT or as Not an RCT; the RCT classifier – a machine learning model that distinguishes RCTs from non‐RCTs; and if appropriate, Cochrane Crowd (crowd.cochrane.org) – Cochrane's citizen science platform where the Crowd help to identify and describe health evidence.

For more information about Screen4Me, see: community.cochrane.org/organizational-info/resources/resources-groups/information-specialists-portal/crs-videos-and-quick-reference-guides#Screen4Me. Detailed information regarding evaluations of the Screen4Me components can be found in the following publications: Marshall 2018; Noel‐Storr 2020; Noel‐Storr 2021; Thomas 2020.

Two review authors (MR, AH) will independently determine the eligibility of each study identified by the search. Review authors will independently eliminate studies that clearly do not satisfy inclusion criteria and obtain full copies of the remaining studies. Two review authors (MR, AH) will independently read these studies to select relevant studies, and in the event of disagreements, a third review author will adjudicate (MB). We will not anonymise the studies before assessment. We will include a PRISMA flowchart in the full review (Moher 2009). 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 (MR, AH) will independently extract data using a standard piloted form and check for agreement before entry into Review Manager Web (Review Manager Web 2019). In the event of disagreements, a third review author will adjudicate (TK). 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 the characteristics of the included studies in sufficient detail to populate a characteristics of included studies table in the full review.

We will extract the following information. 

• Study design (including methods, location, funding sources, study author declarations of interest).

• Setting.

• Participants.

• Intervention(s).

• Comparator(s).

• Outcomes (including measures and time points).

• Numerical data for outcomes of interest.

• Type of analysis/analyses presented.

Assessment of risk of bias in included studies

Two review authors (MR, AH) will independently assess 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 will complete a risk of bias table for each included study using the RoB 1 in Review Manager Web (Review Manager Web 2019).

We will assess the following biases for each included 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 (insufficient detail about the method of randomisation to be able to judge the generation as 'low' or 'high' risk of bias);

  • 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 (insufficient detail about the method of randomisation to be able to judge the generation as 'low' or 'high' risk of bias);

  • 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 did not provide an adequate description of how it was achieved);

  • we will consider studies that do not have blinded participants and personnel to have high risk of bias. Studies rated at high risk of bias will be excluded from the final analysis for comparisons 1 and 2. 

• Blinding of outcome assessment (checking for possible detection bias). We will assess the methods used to blind study participants and outcome assessors from knowing 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);

  • we will exclude studies at high risk of bias (where outcome assessment was not blinded).

• 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 (no missing outcome data; reasons for missing outcome data unlikely to be related to true outcome (for survival data, censoring unlikely to be introducing bias); missing outcome data balanced in numbers across intervention groups, with similar reasons for missing data across groups; missing data have been imputed using 'baseline observation carried forward' analysis);

  • unclear risk of bias (insufficient reporting of attrition/exclusions to permit a judgement of 'low risk' or 'high risk' (e.g. number randomised not stated, no reasons for missing data provided or the study did not address this outcome));

  • high risk of bias (reason for missing outcome data is likely to be related to true outcome, with either imbalance in numbers or reasons for missing data across intervention groups; 'as‐treated' analysis done with substantial departure of the intervention received from that assigned at randomisation; potentially inappropriate application of simple imputation).

• Selective reporting (checking for reporting bias). We will assess reporting biases due to selective outcome reporting. We will judge studies as:

  • low risk of bias (the study protocol is available, and all the study's prespecified (primary and secondary) outcomes that are of interest in the review have been reported in a prespecified way);

  • unclear risk of bias (insufficient information available to permit a judgement of 'low risk' or 'high risk');

  • high risk of bias (not all the study's prespecified primary outcomes have been reported; one or more primary outcomes have been reported using measurements, analysis methods or subsets of the data (e.g. subscales) that were not prespecified; one or more reported primary outcomes were not prespecified (unless clear justification for their reporting is provided, such as an unexpected AE); one or more outcomes of interest in the review have been reported incompletely so that they cannot be entered in a meta‐analysis; the study report failed to include results for a key outcome that would be expected to have been reported for such a study).

Measures of treatment effect

We will perform statistical analyses using Review Manager Web (Review Manager Web 2019). We will summarise the data in a meta‐analysis if they are sufficiently homogeneous, both clinically and statistically.

Dichotomous data

We will present results for dichotomous data using risk ratios (RR) and risk differences (RD) with 95% CIs. We will calculate the number needed to treat for an additional beneficial outcome (NNTB) or the number needed to treat for an additional harmful outcome (NNTH) with 95% CIs if there is a statistically significant reduction (or increase) in RD.

Continuous data

We will use the mean difference (MD) for continuous data when outcomes are measured in the same way between trials. We will use the standardised mean difference (SMD) to combine trials that measured the same outcome but used different methods. We will convert median to mean and estimate the SD as interquartile range (IQR)/1.35, if the data passes the skewness test, when trials report continuous data as the median and IQR. 

Unit of analysis issues

The unit of analysis will be the participating child in individually randomised trials, and a child will be considered only once in the analysis. We will exclude studies where the child is its own control (e.g. diclofenac treatment to one eye and placebo to the other eye). The participating hospital will be the unit of analysis in cluster‐randomised trials. We will analyse them using an estimate of the intracluster correlation coefficient (ICC) derived from the trial (if possible), or from a similar trial or from a study with a similar population as described in Section 16.3.6 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2020). If we use ICCs from a similar trial or a study with a similar population, we will report this and conduct a sensitivity analysis to investigate the effect of variation in the ICC. If we identify both cluster‐randomised trials and individually randomised trials, we will only combine the results from both if there is little heterogeneity between the study designs and the interaction between the effect of the intervention and the choice of randomisation unit is considered to be unlikely.

If we identify cross‐over trials, in which the reporting of continuous outcome data precludes paired analysis, we will not include these data in a meta‐analysis, to avoid unit of analysis error; we will use only data from the first treatment phase. Where carry‐over effects are thought to exist and where sufficient data exist, we will only include data from the first period in the analysis (Higgins 2021).

If we identify multi‐arm trials, where two or more active treatment arms are compared with a placebo or control arm, we will avoid double‐counting of participants in the placebo/control arm by splitting the total number between the active arms. 

If we identify studies reporting the same outcome at multiple time points within our predefined time interval, we will use data for the most commonly used time point only within the prespecified time points we have chosen (i.e. less than two hours; two to 24 hours; more than 24 hours and up to seven days) postintervention of the first dose of analgesia.

We will acknowledge any possible heterogeneity in the randomisation unit and perform a sensitivity analysis to investigate the possible effects of the randomisation unit.

Dealing with missing data

Where feasible, we conduct analyses on an intention‐to‐treat basis for all outcomes. Whenever possible, we will analyse all participants in the treatment group to which they were randomised, regardless of the actual treatment received. If we identify important missing data (in the outcomes) or unclear data, we will request the missing data by contacting the original investigators. We will make explicit assumptions of any methods used to deal with missing data. We may perform sensitivity analyses to assess how sensitive results are to reasonable changes in the undertaken assumptions. We will address the potential impact of missing data on the review findings in the discussion section.

Assessment of heterogeneity

We will estimate the treatment effects of individual trials and examine heterogeneity among trials by inspecting the forest plots and quantifying the impact of heterogeneity using the I² statistic. We will grade the degree of heterogeneity as:

• 0% to 40%: might not be important;

• 30% to 60%: may represent moderate heterogeneity;

• 50% to 90%: may represent substantial heterogeneity;

• 75% to 100%: considerable heterogeneity.

If we note statistical heterogeneity (I² > 50%) (Deeks 2021), we will explore the possible causes (e.g. differences in study quality, participants, intervention regimens or outcome assessments).

Assessment of reporting biases

We intend to conduct a comprehensive search for eligible studies and will be alert for duplication of data. If we identify 10 or more trials for meta‐analysis, we will assess possible publication bias by inspection of a funnel plot. If we uncover reporting bias that could, in the opinion of the review authors, introduce serious bias, we will conduct a sensitivity analysis to determine the effect of including and excluding these studies in the analysis.

Data synthesis

If we identify multiple studies that we consider to be sufficiently similar, we will perform meta‐analysis using Review Manager Web (Review Manager Web 2019). For categorical outcomes, we will calculate the typical estimates of RR and RD, each with its 95% CI; for continuous outcomes, we will calculate the MD or the SMD, each with its 95% CI. We will use a fixed‐effect model for all initial meta‐analyses. If a meta‐analysis has an I² score of greater than 50%, we will reanalyse data using a random‐effects model and present the analysis using this model (Deeks 2021). If we judge meta‐analysis to be inappropriate, we will analyse and interpret individual trials separately. If there is evidence of clinical heterogeneity, we will explain this based on the different study characteristics and subgroup analyses.

Subgroup analysis and investigation of heterogeneity

We will explore high statistical heterogeneity in the outcomes by visually inspecting the forest plots (Higgins 2020).

Where statistical heterogeneity is significant, we will interpret the meta‐analyses' results accordingly; we will downgrade the certainty of evidence in the summary of findings tables, according to the GRADE recommendations (see Table 1 for an example of the summary of findings table).

1. Example of summary of findings table.

Diclofenac compared with placebo for acute postoperative pain in children
Patient or population: children aged ≤ 17 years with acute postoperative pain Settings: hospitals and other healthcare centres Intervention: diclofenac Comparison: placebo
Outcomes	Illustrative comparative risks* (95% CI)		Relative effect (95% CI)	No. of participants (studies)	Certainty of the evidence (GRADE)	Comments
	Assumed risk [control]	Corresponding risk [experimental]
Pain relief, defined as proportion of participants with ≥ 50% postoperative pain relief in each treatment arm, < 2 hours postintervention (dichotomous outcome)	—	—	—	—	—	—
Pain relief, defined as proportion of participants with ≥ 50% postoperative pain relief in each treatment arm, 2–24 hours postintervention (dichotomous outcome)	—	—	—	—	—	—
Pain intensity – as reported by the child – assessed with a validated pain scale, < 2 hours postintervention (continuous outcome). We will report mean postoperative pain intensity in each treatment arm and their corresponding SD	—	—	—	—	—	—
Pain intensity – as reported by the child – assessed with a validated pain scale, 2–24 hours postintervention (continuous outcome). We will report mean postoperative pain intensity in each treatment arm and their corresponding SD	—	—	—	—	—	—
Adverse events, i.e. number of children experiencing any adverse events or harms (as reported by study authors)	—	—	—	—	—	—
Serious adverse events, defined as events requiring a blood transfusion, hospitalisation or resulting in permanent damage (FDA 2016)	—	—	—	—	—	—
*The basis for the assumed risk (e.g. the median control group risk across studies) is provided in footnotes. The corresponding risk (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). CI: confidence interval; SD: standard deviation.
GRADE Working Group grades of evidence High certainty: we are very confident that the true effect lies close to that of the estimate of the effect. Moderate certainty: 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 certainty: our confidence in the effect estimate is limited; the true effect may be substantially different from the estimate of the effect. Very low certainty: we have very little confidence in the effect estimate; the true effect is likely to be substantially different from the estimate of effect.

We will consider the following groups for subgroup analysis where data are available:

• dose of diclofenac;

• route of administration of diclofenac (not for comparison 3);

• age of children: infant (aged less than one year); toddler (aged one to three years); older children (aged more than three years);

• type of surgery includes but are not limited to otolaryngological, urological, general, head and neck, thoracic, cardiovascular, or orthopaedic.

We will restrict these analyses to the primary outcomes.

• Pain relief – as reported by the child.

• Pain intensity – as reported by the child.

• AEs (i.e. number of children experiencing any AEs or harms) (as reported by study authors).

• SAEs.

Sensitivity analysis

Where we identify substantial heterogeneity, we will conduct sensitivity analysis to determine if the findings are affected by the inclusion of only those trials considered to have used adequate methodology with a low risk of bias. In addition, we will conduct a sensitivity analysis to explore if the findings are affected by the inclusion of only trials where the baseline pain levels are considered moderate and high. Furthermore, we will also conduct a sensitivity analysis for larger trials (with more than 49 participants in each treatment arm). We will report the results of sensitivity analyses for primary outcomes only.

Summary of findings and assessment of the certainty of the evidence

Two review authors will independently rate the certainty of the body of evidence for the outcomes. We will use the GRADE system to rank the certainty of the evidence using GRADEpro GDT software (GRADEpro GDT), and the guidelines provided in the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2020) and GRADEpro handbook (Schünemann 2013).

The GRADE approach uses five considerations (study limitations (risk of bias), unexplained heterogeneity and inconsistency 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 considers study design as a marker of quality. RCTs are considered high certainty evidence and can be downgraded for important limitations.

Factors that may decrease the certainty level of a body of evidence are as follows.

• Serious or very serious study limitations (risk of bias).

• Important or serious inconsistency of results.

• Some or major indirectness of evidence.

• Serious or very serious imprecision.

• Probability of publication bias.

We will include two summary of finding tables: comparison 1: diclofenac versus placebo; comparison 2: diclofenac vs active pharmacological comparator, in a transparent and simple tabular format. In particular, we will include key information concerning the certainty of the evidence, the magnitude of the effect of the interventions examined and the sum of available data on the outcomes.

• Pain relief – as reported by the child – defined as proportion of participants with 50% or greater postoperative pain relief in each treatment arm, less than two hours postintervention (dichotomous outcome).

• Pain relief – as reported by the child – defined as proportion of participants with 50% or greater postoperative pain relief in each treatment arm, two to 24 hours postintervention (dichotomous outcome).

• Pain intensity – as reported by the child – assessed with a validated pain scale, less than two hours postintervention (continuous outcome). We will report mean postoperative pain intensity in each treatment arm and their corresponding SDs.

• Pain intensity – as reported by the child – assessed with a validated pain scale, two to 24 hours postintervention (continuous outcome). We will report mean postoperative pain intensity in each treatment arm and their corresponding SD.

• AEs (i.e. number of children experiencing any AEs or harms) (as reported by study authors).

• SAEs, defined as events requiring a blood transfusion, hospitalisation or resulting in permanent damage (FDA 2016).

Appendices

Appendix 1. MEDLINE search strategy

1. Diclofenac/  

2. (diclofen* or diclonate or feloran or ort#ofen or orthophen or voltaren or voltarol).tw.  

3. 1 or 2  

4. adolescent/ or exp child/ or exp infant/  

5. (child* or boy* or girl* or baby or babies or infant* or neonat* or toddler* or teen* or adolescen* or juvenile*).tw.  

6. 4 or 5  

7. exp Pain, Postoperative/  

8. pain/ or acute pain/ or exp pain, postoperative/  

9. (pain* or analges*).tw.  

10. 8 or 9  

11. 3 and 6 and 10  

12. randomized controlled trial.pt.  

13. controlled clinical trial.pt.  

14. randomized.ab.  

15. placebo.ab.  

16. drug therapy.fs.  

17. randomly.ab.  

18. trial.ab.  

19. or/12‐18  

20. exp animals/ not humans.sh.  

21. 19 not 20  

22. 11 and 21

Contributions of authors

MB will oversee the project and is responsible for updating the review.

MR, TK, AH and MB contributed to the design and authoring of the protocol.

MR, TK, AH and MB will contribute to the enactment of the protocol, analysis and authoring of the final review.

Sources of support

Internal sources

• Institute for Clinical Sciences, Lund University, Lund, Sweden

  MB is employed by this organisation

• Department of Health Sciences,  Lund University, Sweden

  MR is employed by this organisation

• Cochrane South Africa, South African Medical Research Council, South Africa

  Host institution (T Kredo, A Hohlfeld)

External sources

• National Institute for Health Research (NIHR), UK

  Cochrane Infrastructure funding to the Cochrane Pain, Palliative and Supportive Care Review Group (PaPaS)

• Region Skåne, Skåne University Hospital, Lund University and Region Västra Götaland, Sweden, Sweden

  Cochrane Sweden is supported from Region Skåne, Skåne University Hospital Lund University and Region Västra Götaland

• Division of Clinical Pharmacology, Department of Medicine, Faculty of Medicine and Health Sciences, Stellenbosch University, South Africa

  Affiliated institution (T Kredo)

Declarations of interest

MR: none known. MR has previously been a practising clinician (physiotherapist), managing children with postoperative pain. 

TK: none known. TK is a medical officer in an Infectious Diseases Clinic at Tygerberg Hospital, Stellenbosch University, Stellenbosch, South Africa.

AH: none known. AH has previously been a practising clinician (physiotherapist), with no history of managing postoperative pain in children.

MB: none known. MB has previously been a practising clinician (paediatrician), managing children with postoperative pain. 

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