Nonsteroidal antiinflammatory drugs (NSAIDs) are an attractive alternative to opioids for the control of postoperative pain. They are effective analgesics (1), and they lack opioid-related adverse effects such as sedation, emesis, pruritus, or respiratory depression. However, NSAIDs inhibit platelet function, and this feature may limit their usefulness in patients who are prone to postoperative bleeding. Prospectively collected data on the risk of operative site bleeding associated with the perioperative use of NSAIDs are sparse. The evidence for a causative association is weak (2,3), and the magnitude of any deleterious effect remains unknown.
The aim of this systematic review was to critically appraise the existing data on the incidence of perioperative bleeding complications caused by NSAIDs and to quantify the potential impact of NSAIDs on bleeding. As a clinical setting, we have chosen tonsillectomy for two reasons: first, tonsillectomy is a very common and well-defined surgical procedure. Second, bleeding is a serious complication after tonsillectomy, which may contribute to postoperative morbidity (4,5). Thus, for this setting, we found it important to evaluate the risk-benefit ratio of NSAIDs.
To perform this systematic review, we followed the recommendations of the QUOROM statement (6). A systematic search of the literature was performed without language restriction. We searched in Medline (from 1966), Embase (from 1989), and the Cochrane Controlled Trials Register (2001) using the words NSAID, nonsteroidal antiinflammatory drug, tonsillectomy, and individual drug names (diclofenac, ketorolac, fenbufen, flurbiprofen, ibuprofen, indomethacin, ketoprofen, naproxen, piroxicam, meloxicam, tenoxicam, nimesulide, rofecoxib, celecoxib, tolmetin, fenoprofen, sulindac, etodolac, nabumetone, tiaprofenic acid, meclofenamic acid, acemetacin, mefenamic acid, aceclofenac, tolfenamic acid, lornoxicam, parecoxib, fentiazac, suprofen, benzydamine, and niflumic acid). The last electronic search was done in December 2001. Additional studies were identified from reference lists of retrieved reports and of relevant review articles. Abstracts or unpublished data were not considered.
Reports were considered if they were randomized, controlled trials of a NSAID (experimental intervention) compared with a non-NSAID treatment (control intervention) in adults or children undergoing tonsillectomy with or without adenoidectomy. Patients in the control group could receive a non-NSAID analgesic (for instance, an opioid), a placebo, or no treatment. Only trials in which the NSAID was administered systemically (i.e., orally, rectally, IV, or IM) and that reported data on one of three end points (intra- or postoperative bleeding, postoperative pain, or postoperative nausea and vomiting [PONV]) were considered.
Retrieved reports were screened by two authors (SM and JR). Each report that met the inclusion criteria was read independently by all authors to assess adequacy of randomization and blinding and to assess description of withdrawals (7). Discrepancies were resolved by discussion. Because there was an a priori agreement that reports without randomization would be excluded, the minimum score of an included trial was 1, and the maximum score was 5.
Information about NSAID regimens (drug, dose, and route of administration), comparators, number of patients enrolled and analyzed, study design, observation periods, surgical technique, and primary and secondary outcome measures were entered on standard collection sheets. This was performed by one investigator (JR) and checked by another (SM). Our primary outcome measures were bleeding complications. These included the volume of intraoperative blood loss, the incidence of postoperative bleeding, the rate of readmission because of bleeding, and the incidence of reoperation because of bleeding. Definitions of intraoperative blood loss were taken as reported in the original trials. Reoperation because of bleeding was regarded as the most relevant end point in this context. Secondary outcomes of interest were quality of pain relief and the incidence of PONV.
To estimate the frequency of rare events (postoperative bleeding, reoperation, and admission), we calculated odds ratios with 95% confidence intervals (CI) using two different models. First, we used the Peto-modified Mantel-Haenszel method (Peto-OR) that ignores trials without events (8). Second, if both cells of a sample were 0, we added 0.5 to all cells of that sample; we shall refer to this as the method described by Shadish and Haddock (9) (OR). Results were challenged with further sensitivity analyses, for instance, by comparing different NSAID regimens. For binary data of frequent events (PONV), we calculated relative risks (RR) with 95% CI. When the OR, Peto-OR, or RR indicated a statistically significant result (i.e., the 95% CI did not include 1), we calculated numbers-needed-to-treat (NNT) with 95% CI using the weighted means of the pooled experimental and control event rates (10). For continuous data, we calculated weighted mean differences (WMD), taking into account study size and sd as reported in the individual trials (ReviewManager software, version 4.0, Cochrane Collaboration, The Nordic Cochrane Center, Copenhagen). We used a fixed effect model throughout because we combined data only when they were clinically homogenous and because heterogeneity tests lack sensitivity (11).
Data from individual trials were graphically displayed using both forest plots to show relative efficacy of treatment effects and event rate scatters (12) to explore variability in event rates.
Quantitative analysis of data on analgesic efficacy was considered inappropriate because a large variety of outcome measures were reported in these trials. Therefore, for each trial, we qualitatively evaluated if the analgesic efficacy of the NSAID treatment was inferior, superior, or equal to the comparator treatment. This assessment was based on reported statistical significance (P < 0.05) of standardized pain mea-sures (scores of pain intensity and pain relief or consumption of supplementary analgesics) in the original investigations.
We identified 63 potentially relevant trials of which 38 were subsequently excluded (13–50) (Fig. 1). Data from 25 randomized trials, including 33 comparisons, were included (51–75) (Table 1). In those, 1853 patients (970 received a NSAID) underwent tonsillectomy. The median number of patients included in the studies was 77 (range, 27–183 patients). The median quality score was 4 (range, 1–5; one trial scored 1, five scored 2, six scored 3, seven scored 4, and six scored 5). Twenty-one trials were double-blinded, of which 18 described an adequate method of blinding (for instance, identical ampoules). Eight NSAIDs were tested, all in analgesic doses (diclofenac, ketorolac, ibuprofen, indomethacin, ketoprofen, tenoxicam, naproxen, and nimesulide). Controls received a placebo or no treatment in 11 studies, an opioid (morphine, pethidine, papaveretum, tramadol, tilidine, and codeine) in 9 studies, and acetaminophen or acetaminophen plus codeine in 3 studies each (Table 1). The surgical technique was reported in 10 studies; tonsillectomy was performed by electrocautery dissection in 8 (52,54–56,61,62,64,67) and ad modum Boyle-Davis in 2 (53,59). Nine studies were in adults (51,56,57,59,60,63–65,70), 14 in children (54,55,58,61, 62,66–69,71–75), and 2 in both adults and children (52,53).
In 9 studies with 12 treatment arms, a NSAID was administered before tonsillectomy, and intraoperative blood loss was an end point (56,60–62,64–66,70,71). Blood loss was estimated by measuring the volume of blood in the suction bottles and in the swabs. Mean measured blood loss was 2.1 ± 0.9 mL/kg with a NSAID compared with 1.8 ± 0.9 mL/kg with the control. The WMD was not significantly different (WMD, 0.38 mL/kg; 95% CI, −0.06 to –0.81).
Dichotomous data on postoperative bleeding were reported in 16 studies with 19 treatment arms (51–59,62–64,66,67,69,71) (Fig. 2). With both NSAIDs and controls, there was a wide variability in event rates ranging from 0% to almost 30%. In 2 trials, no bleedings were reported (57,58). With NSAIDs, 73 of 685 patients (10.7%) had postoperative bleeding compared with 58 of 619 (9.4%) control patients, a difference that was not statistically significant and independent of the model used (Fig. 2).
Readmission or unanticipated admission because of bleeding was reported in 8 studies with 9 treatment arms (51,52,54–57,60,66) (Fig. 3). With NSAIDs, the range of admissions was 0% to approximately 15%, and with controls, the range was between 0% and <10%. In 2 trials, no admissions were reported (57,60). With NSAIDs, 14 of 275 (5.1%) patients required admission or readmission compared with six of 231 (2.6%) control patients. This difference was not statistically significant and independent of the model used (Fig. 3).
Presence or absence of reoperation was reported in 21 studies with 27 treatment arms (51–71) (Fig. 4). With NSAIDs, the range of reoperations was 0% to approximately 13%, and with controls, the range was 0%–10%. In 7 trials, no patients were reoperated on because of bleeding (52,56–58,60,61,69). With NSAIDs, 24 of 877 (2.7%) patients had a reoperation compared with eight of 749 (1.1%) control patients. The OR was statistically significant with the Peto method (2.33; 95% CI, 1.12–4.83) and was borderline significant with the method described by Shadish and Haddock (9) (OR, 1.92; 95% CI, 1.00–3.71); the NNT was 60 (95% CI, 34–277).
The quantity of data and the quality of data reporting allowed us to perform four sensitivity analyses. Primary bleeding (within 24 h of tonsillectomy) was reported in 11 studies with 14 treatment arms (52–57,62–64,69,71). With NSAIDs, 44 of 494 (8.9%) patients had a primary bleed compared with 35 of 425 (8.2%) control patients. This difference was not statistically significant and independent of the model used (Peto-OR, 1.31; 95% CI, 0.80–2.13; OR, 1.27; 95% CI, 0.79–2.04). Secondary bleeding (beyond the initial 24-h period) was reported in 7 studies with 8 treatment arms (52–57,63). With NSAIDs, 14 of 237 (5.9%) patients had a secondary bleed compared with 15 of 246 (6.1%) control patients. This difference was not statistically significant and independent of the model used (Peto-OR, 0.86; 95% CI, 0.39–1.89; OR, 0.88; 95% CI, 0.41–1.89).
In five trials, NSAID treatment was started before surgery, and postoperative bleeding was an end point (56,62,64,66,71). With preoperative NSAIDs, 24 of 214 (11.2%) patients had a postoperative bleed compared with 22 of 189 (11.6%) control patients. This difference was not statistically significant and independent of the model used (Peto-OR and OR, 1.06; 95% CI, 0.57–1.98). In 13 trials, NSAID treatment was started after surgery, and postoperative bleeding was an end point (51–55,57–59,62–64,67,69). With postoperative NSAIDs, 49 of 471 (10.4%) patients had a bleed compared with 41 of 475 (8.6%) control patients. This difference was not statistically significant and independent of the model used (Peto-OR, 1.42; 95% CI, 0.90–2.24; OR, 1.41; 95% CI, 0.90–2.20).
In 10 trials, NSAID treatment was started before surgery, and reoperation was an end point (56,60–62,64–66,68,70,71). With preoperative NSAIDs, nine of 406 (2.2%) patients had a reoperation compared with five of 319 (1.6%) control patients. This difference was not statistically significant and independent of the model used (Peto-OR, 1.33; 95% CI, 0.45–3.94; OR, 1.20; 95% CI, 0.45–3.20). In 13 trials, NSAID treatment was started after surgery (51–55,57–59,62–64,67,69), and reoperation was an end point. With postoperative NSAIDs, 15 of 471 (3.2%) patients had a reoperation compared with three of 475 (0.7%) control patients. This difference was statistically significant (Peto-OR, 4.36, 95% CI, 1.69–11.26; OR, 3.27; 95% CI, 1.39–7.68), and the NNT was 40 (95% CI, 23–123).
In 11 trials, a single-dose NSAID regimen was given, and reoperation was an end point (54,56,60–63,65,66,68,69,71). With the single-dose NSAIDs, 13 of 448 (2.9%) patients had a reoperation compared with five of 421 (1.2%) control patients. This difference was not statistically significant and independent of the model used (Peto-OR, 2.42; 95% CI, 0.93–6.29; OR, 1.96; 95% CI, 0.83–4.64). In 10 trials, a multiple-dose NSAID regimen was given, and reoperation was an end point (51–53,55,57–59,64,67,70). With the multiple-dose NSAID regimen, 11 of 429 (2.6%) patients had a reoperation compared with three of 328 (1%) control patients. This difference was not statistically significant and independent of the model used (Peto-OR, 2.21; 95% CI, 0.72–6.84; OR, 1.87; 95% CI, 0.68–5.14).
There was a lack of data to evaluate the risk with individual NSAIDs, of different routes of administration, or to differentiate between adults and children.
Eleven studies compared a NSAID with placebo or no treatment and reported on pain outcomes (53,57,60,62,64,69,70,72–75) (Table 1). All studies except one (60) showed significantly improved pain relief with NSAIDs compared with control.
Eight studies compared a NSAID with an opioid and reported on pain outcomes (52,54,56,63,68,71, 72,75) (Table 1). Opioid regimens were IM or IV morphine 0.1–0.2 mg/kg (54,68), papaveretum 0.2–0.3 mg/kg (56,71,75), pethidine 1 mg/kg (63,72), tilidine 2.5 mg/kg (63), or oral tramadol approximately 1 mg/kg (52). In two studies (56,75), pain relief was significantly improved with a NSAID, in five studies, there was equivalence (52,54,63,71,72), and in one study, pain relief was significantly better with the opioid (68).
Three studies compared a NSAID with rectal acetaminophen 13–35 mg/kg (61,65) or oral acetaminophen approximately 10–15 mg/kg (58) and reported on pain outcomes (Table 1). All three studies showed equivalence in terms of analgesic efficacy.
Three studies compared a NSAID with acetaminophen- codeine administered in doses of approximately 10 mg/kg of acetaminophen and 0.4–1 mg/kg of codeine and reported on pain outcomes (55,59,67) (Table 1). Results were inconsistent with one trial each showing significantly improved (59), equivalent (67), or inferior (55) pain relief with the NSAID.
Most studies that reported on PONV did not distinguish between nausea and vomiting, and they only rarely reported on the length of the observation period (Table 1). With placebo or no treatment (data from 10 trials), 77 of 279 patients (27.6%) had PONV symptoms, with NSAIDs (19 trials), there were 251 of 794 (31.6%), and with codeine, pethidine, morphine, papaverine, or tramadol (11 trials), 217 of 445 (48.8%) patients vomited or were nauseous (Table 1). When all opioid-controlled trials were analyzed, the risk with opioids was significantly increased compared with NSAIDs (RR 0.73; 95% CI, 0.63–0.85); the NNT was 9 (95% CI, 5–19).
These trials were of satisfactory methodological quality; the median Oxford score was 4. All studies were randomized; thus, selection bias should not have been a factor. At least 18 trials (72%) were properly blinded, minimizing the risk of observer bias. However, the results from this systematic review are ambiguous and should be interpreted carefully. Several issues contribute to this uncertainty.
First, of four bleeding end points (i.e., intraoperative blood loss, postoperative bleeding, admission because of bleeding, and reoperation because of bleeding), only one, reoperation, showed a statistically significant result in favor of the non-NSAID treatment. Furthermore, this statistical significance was dependent on the statistical model used (the Peto method). This, perhaps, reflects the difficulty in choosing the most relevant end point in this context. Posttonsillectomy bleeding, for instance, is difficult to determine. Numbers from the literature range from 0.28%–20%(5), and this large variability is most likely because of the uncertainty of investigators on how to define significant bleeding. Not surprisingly, we were unable to differentiate between minor and major bleeding episodes. Our ante hoc decision was that the incidence of reoperation because of bleeding was the most relevant primary outcome measure, both from a clinical and an economic point of view. Also, this end point is clearly dichotomous, and thus, there is a minor risk only of observation and interpretation bias. According to the literature, reoperation because of bleeding after tonsillectomy without NSAID exposure happens in approximately 0.3%–1.9%(4,76,77). In these trials, the reported incidence of reoperation without NSAID exposure (i.e., the control event rate) was in agreement with these figures.
Second, the risk-benefit ratio was not straightforward. If the NSAID-related absolute increase in the incidence of reoperation because of bleeding is about right, then we have to assume that of 100 patients undergoing tonsillectomy, less than 2 will require a reoperation (NNT, approximately 60) who would not have required one had they not received a NSAID. However, of the same 100 patients, 11 will not have PONV symptoms (NNT, 9) who would have had these symptoms had they received an opioid. This is a beneficial effect, although its magnitude is small compared with the efficacy of truly antiemetic interventions (78). Also, with NSAIDs, pain relief was significantly improved in 9 of 10 placebos or no treatment controlled trials and was of comparable efficacy in 12 of 14 comparisons with a non-NSAID analgesic. Thus, NSAIDs may be regarded as a rational choice for analgesia after tonsillectomy. However, the question is whether avoiding PONV in 11 patients is worth the potential risk and expense of bringing two patients back to the operation room.
Third, we were unable to identify any predictive factor for bleeding. The impact of single-dose versus multiple-dose regimens, for instance, could not be demonstrated. Data on children compared with adults, or on the individual NSAIDs, were too sparse to allow for subgroup analysis. One sensitivity analysis only provided a hint of information on an increased risk of reoperation (but not of bleeding per se) when NSAIDs were given after surgery compared with preoperative administration. The biological basis for this differential effect remains obscure. The lack of information on predictive factors for bleeding complications may have been due to the lack of relevant data or to poor reporting of relevant data. The surgical technique was not expected to be of major importance here because all these trials were strictly controlled. If a surgical technique had an impact on intra- or postoperative bleeding, then this would concern all patients, those who received a NSAID and those who did not, and thus, the RR would stay the same. Also, the reported surgical techniques represent widely used and accepted gold standard interventions for tonsillectomy.
Fourth, the presence of zero-event trials was a methodological problem. Zero-event trials occur when the event is very rare or when the trials are of limited size. Indeed, perioperative bleeding complications are relatively rare, and these trials were small; group sizes rarely exceeded 40 patients. There is no general agreement on how to deal with zero cells in meta-analysis. In zero-event trials, it cannot be excluded if a particular event actually happened but was not reported. It may also be assumed that these trials were unable to identify an (rare) event (i.e., the trials were too small); there is then an argument to regard such trials as invalid essays and, therefore, to exclude them from a combined analysis. To overcome this methodological problem, we applied two statistical models to calculate the combined ORs for rare (bleeding) events. The Peto-method ignores trials with zero events (8). The disadvantage of this method is that potentially relevant data are censored. As a result, combined event rates increase artificially because the denominator decreases; both the underlying risk and the risk with drug exposure may then be overestimated. The advantage of the method described by Shadish and Haddock (9) is that all trials can be included in the analysis independent of whether they report or not on a particular end point. The disadvantage of that method is that the analysis may be flawed if the sum of the manipulated zero cells outweighs the number of true events. Finally, we calculated the NNT based on combined event rates that were weighted by trial size and not manipulated. The results of all analyses using these models were surprisingly consistent.
Finally, it is important to note that these meta-analyses had low power. For example, event rates of admission because of bleeding were very small (2.6% without and 5.1% with NSAIDs), and calculations were based on 506 patients. A post hoc power analysis using these numbers and a significance level of 5% reveals a statistical power of approximately 50% only. Thus, it cannot be excluded that some of the nonsignificant findings in the meta-analysis were caused by Type II errors.
Consequently, the agenda is one of further research rather than of clinical recommendations. The recently introduced cyclo-oxygenase type 2 (COX-2) inhibitors may have advantages compared with classic NSAIDs. They seem to be effective, safe, and well tolerated for treating postoperative pain (79), and their COX-2 selectivity produces minimal effect on platelet aggregation. Two studies have found that COX-2 inhibitors have analgesic efficacy equivalent to that of NSAIDs for dental pain (80,81). In contrast, a study of tonsillectomy in children has found that the addition of ibuprofen to acetaminophen significantly reduced the need for early analgesia, whereas the addition of a COX-2 inhibitor to acetaminophen did not (50). There were no differences between groups in perioperative bleeding episodes. Further studies are required to carefully evaluate the risk-benefit ratio of COX-2 inhibitors in tonsillectomy. However, if the risk of, for example, reoperation because of bleeding with classic NSAIDs was approximately 2.7% and with COX-2 inhibitors was as with placebo (1.1%), then 2400 patients would need to be randomized to ensure a statistically significant result in favor of the COX-2 antagonist. Finally, it remains unknown if these data from patients undergoing tonsillectomy can be extrapolated to other surgical settings. Further trials are required to evaluate the potential additional bleeding risk with NSAIDs for different surgeries. In future studies, the recording of the incidence of perioperative bleeding requires standard definitions.
In conclusion, the evidence for NSAIDs to increase the incidence of bleeding after tonsillectomy remains ambiguous. The cautious clinical message must be that there is some evidence from randomized, controlled trials that NSAIDs may increase the likelihood of reoperation because of bleeding, particularly when NSAIDs are given in the postoperative period. However, there is a lack of evidence for NSAIDs to increase intraoperative blood loss or to increase the incidence of postoperative bleeding or readmission because of bleeding. Likewise, there is a lack of evidence that the regimen per se (single- versus multiple-dose) has any impact on bleeding and that there is any difference in the risk profile between different NSAIDs or between adults and children. Compared with opioids, NSAIDs seem to be equianalgesic for this type of surgery, and they decrease the risk of PONV to some extent. Whether these data can be extrapolated to other surgical settings needs to be shown. Overall, these results may indicate that NSAIDs should be used cautiously in tonsillectomy until further data are available.
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