Risk of acute myocardial infarction with NSAIDs in real world use: bayesian meta-analysis of individual patient data
BMJ 2017; 357 doi: https://doi.org/10.1136/bmj.j1909 (Published 09 May 2017) Cite this as: BMJ 2017;357:j1909
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We are puzzled by Moore’s affirmation that clinical trial meta-analyses have “shown risk only for use longer than 90 days and maximal approved dosing of NSAIDs” since the risk of acute myocardial infarction for various durations of use and doses of individual NSAIDs have not been reported. (1, 2) Moore asserts that “for the vast majority of NSAIDs users, no risk has actually been demonstrated and the present meta-analysis does not change this.” But maybe this absence of clinical trial evidence for risk of myocardial infarction is because trials were not powered for this outcome. Overall the statistical power to assess MI risk was very low in clinical trial meta-analyses as indicated by often wide confidence intervals, (1, 2) some of which are compatible with both a decrease and an increase in risk. Randomised trials would have had exceedingly small power to determine risk of MI with use of NSAIDs for one week.
Moore refers to meta-analyses of clinical trials as “serving as the foundation of the reality of the risk”. Of course, successful randomisation helps inferring that effects are causal because it produces treatment groups that are exchangeable. As such, randomised trials can be expected to be free from baseline confounding. But whereas various biases are always a concern with observational studies, the possibility that confounding and other biases might arise in a trial post-randomisation tends to be overlooked. (3 ) Partial non-adherence, non-persistence, contamination by an OTC NSAID or differential concomitant treatments affecting the risk of MI need to be considered irrespectively of the study design.
Aside from bias, many other factors can explain why randomised and non-randomised evidence do not always give the same answer. (4, 5 ) For NSAIDs, main reasons are the doses and the durations studied, whether or not MI events were pre-specified and how they were adjudicated, whether the indication studied was also an indication for use of NSAIDs in real life, the study setting, the exclusion of populations at risk or with established cardiovascular disease, and differences in the research question. (6, 7)
As a matter of fact, one key reasons for selecting NSAID non-users as the reference group in the IPD meta-analysis is that this was the research question of interest. Although non-users had not been prescribed an NSAID on index date they may or may not have been using non-pharmacological treatment or pharmacological therapies other than NSAIDs for pain or inflammation. Moreover, non-use of NSAID on index date neither rules in nor rules out the presence of musculoskeletal pain or inflammation on the day of the event. Also, non-use does not inform on the indication or any contraindication to NSAIDs on index date.
Moore’s assertion that “a user of NSAIDs is not the same as a non user, even if it is the same patient” is an oversimplication of the active-comparator design (8-10) in pharmacoepidemiology. Comparison with non-use of NSAIDs is useful for clinical decision-making because it allows assessing the risks associated with NSAIDs versus seeking non-NSAID therapeutic alternatives. Comparing risk of acute MI with paracetamol (acetaminophen), as suggested by Moore, addresses that comparison only and we disagree that paracetamol “has exactly the same indications and usage patterns as NSAIDs.” We do not believe that celecoxib is the active comparator of interest to all. Moreover, for the comparison of risk of traditional NSAIDs to celecoxib to be meaningful, one first needs to learn about the MI risk of celecoxib in various scenarios of dose and duration of use. This is what we did in the main analysis of our study. We then calculated the Bayesian posterior probability that risks of acute myocardial infarction associated with a given NSAID exceeded those for another NSAID to provide information on all active treatment comparisons (Figure 3 in web appendix 3) Note that in the clinical trial network meta-analysis the MI risk of ibuprofen and diclofenac were obtained by a similar indirect comparison approach since these two NSAIDs have not been directly compared to placebo in trials. (2)
Moore has inferred that the immediate onset of a notably increased risk could be confounding. Because NSAID use in real life typically consists in treatment episodes with drug switching and off-drug periods, (11) patients studied in these large cohorts likely were not first time users or new users. This large patient sample had enough power to show that an NSAID prescribed for one to seven days is associated with an increased risk of acute myocardial infarction. Certainly our findings are not immune to residual confounding despite matching on demographics and calendar time and multivariable regression analysis. But there is a key reason why early risk of MI is not just confounding. This IPD meta-analysis minimised the possibility of confounding by indication (i.e. prescribing naproxen for cardioprotection) or by contraindication (i.e. not prescribing a COX-2 selective inhibitor to patients with pre-existing cardiovascular disease) by limiting the inclusion of studies to those before the withdrawal of rofecoxib, a timeframe during which the choice of NSAID drug by a typical prescriber was unrelated to a patient’s risk for myocardial infarction. As for the effect of unmeasured and incompletely measured confounders we think, as reported, (12) that these are likely to have slightly underestimated MI risk.
Moore has also suggested that the increased risk of MI documented in the first week of NSAID use may be reverse causation (protopathic bias). Of course it is possible that some patients who did not seek contact with the healthcare system might have taken an NSAID (either purchased OTC or previously dispensed for another problem) to try alleviating chest pain. Those ‘silent MIs’ could not be included in our analysis but we do not expect that documented MIs, silent MIs or out-of-hospital fatal MIs would differ by exposure to NSAID. It should be emphasized that this rapid onset of MI risk was shown for prescription NSAIDs. We do not believe that physicians customarily fail to identify the prodromal symptoms of myocardial infarction. Also, we posit that patients with chest pain who seek medical help and are subsequently diagnosed with acute MI, did not self-medicate with NSAIDs. Thus reverse causality bias is not the reason for the increased risk of acute MI documented with NSAIDs for one to seven days.
Moore interprets the risks of MI with use for longer than one month as “decreasing risk with time”. However this is not what the paper is saying. What we do report is that risks of acute MI associated with longer-term use do not appear to exceed those associated with shorter durations. This in no way means that risks are decreasing over time but rather that they do not seem to continue to increase further. However, our study does not allow an estimate for the risk of second heart attacks since follow-up stopped once a patient had experienced a first acute myocardial infarction.
Moore argues that pathophysiological changes arising from acute pain, the indication for the use of NSAIDs, might be a cause for myocardial infarction but then how would that explain differences in MI risk between the various NSAIDs and between NSAIDs and placebo? He also expressed concern for “the role of the ‘MI risk’ of NSAIDs on the prescription opiate epidemic…” One would wish for a simple solution to curb this multifaceted problem.
Michèle Bally, BPharm, MSc, PhD
Epidemiologist and researcher, University of Montreal Hospital Research Center (CRCHUM), Montreal, Canada
James M Brophy, MD, FRCP(c), FACC, FCCS, PhD
Professor of Medicine and Epidemiology, McGill University, Montreal, Canada
1. Coxib and traditional NSAID Trialists' (CNT) Collaboration, Bhala N, Emberson J, et al. Vascular and upper gastrointestinal effects of non-steroidal anti-inflammatory drugs: meta-analyses of individual participant data from randomised trials. Lancet. 2013;382(9894):769-79.
2. Trelle S, Reichenbach S, Wandel S, et al. Cardiovascular safety of non-steroidal anti-inflammatory drugs: network meta-analysis. BMJ. 2011;342:c7086.
3. Hernán MA, Hernandez-Diaz S, Robins JM. Randomized trials analyzed as observational studies. Ann Intern Med. 2013 Oct 15;159(8):560-2.
4. Anglemyer A, Horvath HT, Bero L. Healthcare outcomes assessed with observational study designs compared with those assessed in randomized trials. Cochrane Database Syst Rev. 2014;4:MR000034.
5. Naci H, Ioannidis JP. How good is "evidence" from clinical studies of drug effects and why might such evidence fail in the prediction of the clinical utility of drugs? Annu Rev Pharmacol Toxicol. 2015;55:169-89.
6. Dieppe P, Bartlett C, Davey P, et al. Balancing benefits and harms: the example of non-steroidal anti-inflammatory drugs. BMJ. 2004;329(7456):31-4.
7. Horwitz RI, Abell JE, Christian JB, et al. Right answers, wrong questions in clinical research. Sci Transl Med. 2014 Jan 29;6(221):221fs5.
8. Yoshida K, Solomon DH, Kim SC. Active-comparator design and new-user design in observational studies. Nat Rev Rheumatol. 2015 Jul;11(7):437-41.
9. Velentgas P, Dreyer NA, Nourjah P, et al. Developing a Protocol for Observational Comparative Effectiveness Research: A User’s Guide. AHRQ Publication No. 12(13)-EHC099. Rockville, MD: Agency for Healthcare Research and Quality; January 2013.
10. Lund JL, Richardson DB, Sturmer T. The active comparator, new user study design in pharmacoepidemiology: historical foundations and contemporary application. Curr Epidemiol Rep. 2015 Dec;2(4):221-8.
11. Langman M, Kahler KH, Kong SX, et al. Drug switching patterns among patients taking non-steroidal anti-inflammatory drugs: a retrospective cohort study of a general practitioners database in the United Kingdom. Pharmacoepidemiol Drug Saf. 2001;10(6):517-24.
12. Schneeweiss S, Glynn RJ, Tsai EH, et al. Adjusting for unmeasured confounders in pharmacoepidemiologic claims data using external information: the example of COX2 inhibitors and myocardial infarction. Epidemiology. 2005;16(1):17-24.
Competing interests: Author JMB reports serving on the Data Monitoring Committee for the PRECISION trial, which was sponsored by Pfizer, during the conduct of the study
We thank Wicks for his insightful comments. The IPD meta-analysis of NSAIDs and risk of acute myocardial infarction (MI) required accessing deidentified data that are coded to prevent a person's identity from being connected with personal health information.
Permission to access data held in healthcare repositories was very difficult to obtain, taking years or being denied altogether. In part because of the many hurdles in getting access to data, the study took considerable time, a total of 10 years from the original idea to completion.
Had we obtained the patient data for four additional studies that qualified for our analysis, we would have had 25% more MI cases. The improved precision and ability to study the effect of NSAID dose in the first week of use might have provided further guidance to health providers and patients. Incidentally we believe that much of the residual confounding in our study might have been mitigated by linking IPD from healthcare databases with other existing patient-level data collected during routine clinical encounters.
Unfolding world events and, perhaps, evolution of views and attitudes warrant revisiting the barriers to access and linkage of individual health data for the purpose of research. We submit that the need for personal data protection and the common good of data sharing should be equally highly valued.
Michèle Bally, BPharm, MSc, PhD
Epidemiologist and researcher, University of Montreal Hospital Research Center (CRCHUM), Montreal, Canada
James M Brophy, MD, FRCP(c), FACC, FCCS, PhD
Professor of Medicine and Epidemiology, McGill University, Montreal, Canada
Competing interests: Author JMB reports serving on the Data Monitoring Committee for the PRECISION trial, which was sponsored by Pfizer, during the conduct of the study
Lääketilasto and colleagues voiced their concern about bias due to over-the-counter (OTC) use of NSAIDs. Of the common NSAIDs, only ibuprofen had OTC status during the time period studied in the IPD meta-analysis. OTC ibuprofen use likely varied according to the jurisdiction. It was influenced by incentives for seeking a prescription such as reimbursement policies and co-payment, and by clinical factors including severity of pain and inflammation, and disease chronicity. Whereas exposure to ibuprofen may have been underestimated due to OTC use, particularly for short-term use of low doses, it may have been overestimated when ibuprofen was prescribed on an ‘as needed’ basis. This further illustrates that the extent and direction of information bias are difficult to establish because sources of misclassification may not be independent and biasing effects may cancel. Overall, it is possible that the combined influence of various sources of exposure measurement error, which are inherent to database studies, have biased results towards the null.
Lääketilasto and colleagues requested information on NSAID risk based on age. Further investigating the heterogeneity of NSAIDs MI risk according to demographics or comorbidites is undoubtedly interesting but it would not help “proving causation” as this group is suggesting. Matching of controls and MI cases on age is convenient for control of confounding because it circumvents the analytical challenge due to the effect of age on MI risk possibly not being linear. Unfortunately matching on age precludes further studying its effect. Lääketilasto and colleagues have argued that “if the (NSAID MI) risk does in fact vary by age, and younger people have reduced relative risk this would suggest the results may represent confounding rather than true causation.” Interaction between age and NSAID use would be an alternative explanation. If indeed there was an additive interaction between these two MI risk factors, the number of MI cases due to increasing age and those due to NSAID use would not add up such that their combined effect might plausibly be greater than additive in older patients. For inferring “true causation”, aside from measurement without error, the assumptions of treatment group exchangeability, exposure positivity, consistency, and non-interference must be met, (1) which is not easily “proven”.
Michèle Bally, BPharm, MSc, PhD
Epidemiologist and researcher, University of Montreal Hospital Research Center (CRCHUM), Montreal, Canada
James M Brophy, MD, FRCP(c), FACC, FCCS, PhD
Professor of Medicine and Epidemiology, McGill University, Montreal, Canada
1. Hernán MA, Robins JM. (2017). Causal Inference. Boca Raton: Chapman & Hall/CRC, forthcoming. Available at: https://www.hsph.harvard.edu/miguel-hernan/causal-inference-book/ Last accessed June 4, 2017.
Competing interests: Author JMB reports serving on the Data Monitoring Committee for the PRECISION trial, which was sponsored by Pfizer, during the conduct of the study
Evans stated that the immediate onset of a notably increased risk was compatible with a failure of adequate adjustment for confounding. Because NSAID use in real life typically consists in treatment episodes with drug switching and off-drug periods, (1) patients studied in these large cohorts likely were not first time users or new users. Certainly our findings are not immune to residual confounding despite matching on demographics and calendar time and multivariable regression analysis. But there is a key reason why early risk of MI is not just confounding. This IPD meta-analysis minimised the possibility of confounding by indication (i.e. prescribing naproxen for cardioprotection) or by contraindication (i.e. not prescribing a COX-2 selective inhibitor to patients with pre-existing cardiovascular disease) by limiting the inclusion of studies to those before the withdrawal of rofecoxib, a timeframe during which the choice of NSAID drug by a typical prescriber was unrelated to a patient’s risk for myocardial infarction. As for the effect of unmeasured and incompletely measured confounders we think, as reported, (2) that these are likely to have slightly underestimated MI risk.
Evans has also suggested that the increased risk of MI documented in the first week of NSAID use may be reverse causation (protopathic bias). Of course it is possible that some patients who did not seek contact with the healthcare system might have taken an NSAID (either purchased OTC or previously dispensed for another problem) to try alleviating chest pain. Those ‘silent MIs’ could not be included in our analysis but we do not expect that documented MIs, silent MIs or out-of-hospital fatal MIs would differ by exposure to NSAID. It should be emphasized that this rapid onset of MI risk was shown for prescription NSAIDs. We do not believe that physicians customarily fail to identify the prodromal symptoms of myocardial infarction. Also, we posit that patients with chest pain who seek medical help and are subsequently diagnosed with acute MI, did not self-medicate with NSAIDs. Thus reverse causality bias is not the reason for the increased risk of acute MI documented with NSAIDs for one to seven days.
One key reasons for selecting NSAID non-users as the reference group in the IPD meta-analysis is that this was the research question of interest. Although non-users had not been prescribed an NSAID on index date they may or may not have been using non-pharmacological treatment or pharmacological therapies other than NSAIDs for pain or inflammation. Moreover, non-use of NSAID on index date neither rules in nor rules out the presence of musculoskeletal pain or inflammation on the day of the event. Also, non-use does not inform on the indication or any contraindication to NSAIDs on index date. Comparison with non-use of NSAIDs is useful for clinical decision-making because it allows assessing the risks associated with NSAIDs versus seeking non-NSAID therapeutic alternatives.
Could the early onset of increased MI risk be explained by the fact that source databases contain information about NSAID prescription or dispensing and not on dates of actual use? We submit the IPD meta-analysis does not systematically overestimate MI risks because this would mean that misclassification resulting from prescriptions being a proxy for actual intake affected cases and controls in a differential manner, which did not occur. Consider the large nested case-control dataset (RAMQ, N=233 816, 21 256 MI cases) prospectively created for the purpose of this IPD meta-analysis. Computer-recorded variables ascertained the supplied strength, quantity, and days covered. Prescriptions dates allowed determining continuous treatment episodes while characterising usage behaviours such as intermittent use, daily dose changes, and drug switches.
The fact that over-the-counter (OTC) use of NSAIDs is not captured in healthcare databases is a limitation. Of the common NSAIDs, only ibuprofen had OTC status during the time period studied in the IPD meta-analysis. OTC ibuprofen use likely varied according to the jurisdiction. It was influenced by incentives for seeking a prescription such as reimbursement policies and co-payment, and by clinical factors including severity of pain and inflammation, and disease chronicity. Whereas exposure to ibuprofen may have been underestimated due to OTC use, particularly for short-term use of low doses, it may have been overestimated when ibuprofen was prescribed on an ‘as needed’ basis. This further illustrates that the extent and direction of information bias are difficult to establish because sources of misclassification may not be independent and biasing effects may cancel.
Overall, it is possible that the combined influence of various sources of exposure measurement error, which are inherent to database studies, have biased results towards the null.
Evans raises an excellent point about the paper not discussing risk in absolute terms. This meta-analysis of patient-level data suggests that use of common NSAIDs increases a person’s relative risk of acute MI by about 20 to 50% overall and possibly by 75% with high-dose ibuprofen or naproxen used for one to four weeks. Our study does not allow an estimate for the risk of second heart attacks. Depending on the individual baseline heart attack risk, it seems reasonable to conclude that the absolute risk due to use of NSAIDs is on average increased by about 0.5-1% per year (for additional discussion of absolute risk please refer to Authors’ Rapid Response of 12 May 2017).
Michèle Bally, BPharm, MSc, PhD
Epidemiologist and researcher, University of Montreal Hospital Research Center (CRCHUM), Montreal, Canada
James M Brophy, MD, FRCP(c), FACC, FCCS, PhD
Professor of Medicine and Epidemiology, McGill University, Montreal, Canada
1. Langman M, Kahler KH, Kong SX, et al. Drug switching patterns among patients taking non-steroidal anti-inflammatory drugs: a retrospective cohort study of a general practitioners database in the United Kingdom. Pharmacoepidemiol Drug Saf. 2001;10(6):517-24.
2. Schneeweiss S, Glynn RJ, Tsai EH, et al. Adjusting for unmeasured confounders in pharmacoepidemiologic claims data using external information: the example of COX2 inhibitors and myocardial infarction. Epidemiology. 2005;16(1):17-24.
Competing interests: Author JMB reports serving on the Data Monitoring Committee for the PRECISION trial, which was sponsored by Pfizer, during the conduct of the study
The risk of acute myocardial infarction (MI) for nimesulide was not characterised. The IPD meta-analysis examined risk of a first acute MI after study entry only for rofecoxib, celecoxib, diclofenac, ibuprofen, and naproxen.
Michèle Bally, BPharm, MSc, PhD
Epidemiologist and researcher, University of Montreal Hospital Research Center (CRCHUM), Montreal, Canada
James M Brophy, MD, FRCP(c), FACC, FCCS, PhD
Professor of Medicine and Epidemiology, McGill University, Montreal, Canada
Competing interests: Author JMB reports serving on the Data Monitoring Committee for the PRECISION trial, which was sponsored by Pfizer, during the conduct of the study
I give an explanation of the fact that NSAIDS increase the risk of MI here:
Heitor Reis, A. “On the etiology of cardiovascular diseases: A new framework for understanding literature results”, Medical Hypotheses, 92, 94–99 (2016)
Heitor Reis, A. “Acidemia and blood free fatty acids: analysis of cardiovascular risk factors in a new context.” Discovery Medicine 23(126):183-188 (2017) (OPEN ACCESS)
Essentially, NSAIDs cause acidemia, which in the context of high concentrations of Free Fatty Acids increases the risk of MI
Competing interests: No competing interests
That antiinflammatory drugs increase the risk of coronary heart disease (CHD) is a strong argument against the idea that CHD is caused by inflammation. It is true that the coronary arteries in patients with CHD are inflamed, but if antiinflammatory drugs increase the risk of CHD, the inflammation is evidently protective, which is in accordance with our hypothesis, that the commonest cause of atherosclerosis and CHD is acute and chronic infections.1,2
1. Ravnskov U, McCully KS. Vulnerable plaque formation from obstruction of vasa vasorum by homocysteinylated and oxidized lipoprotein aggregates complexed with microbial remnants and LDL autoantibodies. Ann Clin Lab Sci 2009;39:3-16.
2. Ravnskov U, McCully KS. Infections may be causal in the pathogenesis of atherosclerosis. Am J Med Sci 2012;344:391-4. doi: 10.1097/MAJ.0b013e31824ba6e0.
Competing interests: No competing interests
In Italy, a wide range of NSAIDs is used, and most of it includes self-medication. It is known that NSAIDs increase cardiovascular risk, but it is also true that they are useful in reducing the local inflammatory component.
Systemic administration, high doses, and prolonged treatment periods can increase the disadvantages of this class of medications. Intra-dermic (mesotherapy) administration, for localized pain management, is a useful option for treating patients with systemic NSAID contraindications (1). With a series of microinjections in the surface layers of the skin, corresponding to localized pain, and with a smaller dose, a slower spread of the drug is obtained as compared to deeper or systemic administration (2). This technique has several advantages, including the drug-saving effect, a prolonged analgesic effect, and a lower risk of adverse events.
Mesotherapy can be applied to patients with several localized musculoskeletal types of pain and may synergize with other therapeutic strategies (3). The use of anti-inflammatory drugs should be regulated by medical staff, and the local administration route could be a useful tool to exploit the pros of NSAIDs and reduce systemic cons. It is the task of pharmacological research to take advantage of this opportunity for proper use of this class of medications. Regulatory authorities and pharmacompanies should consider this possibility. Of course, it is crucial to diagnose the type of pain and choice the appropriate therapeutic strategy in the individual patient and its involvement (informed consent) in the care plan (4). Can this strategy help to reduce the inappropriate use of systemic NSAIDs?
1. Mammucari M, Gatti A, Maggiori S, Bartoletti CA, Sabato AF. Mesotherapy, definition, rationale and clinical role: A consensus report from the Italian Society of Mesotherapy. Eur Rev Med Pharmacol Sci 2011; 15(6): 682-694
2. Mammucari M., Gatti A., Maggiori S., Sabato A.F. Role of mesotherapy in musculoskeletal pain: Opinions from the Italian Society of Mesotherapy. Evidence-based Complementary and Alternative Medicine 2012; Article N. 436959
3. Mammucari M, Maggiori E, Natoli S. Should the general practitioner consider mesotherapy (intradermal therapy) to manage localized pain? Pain Ther. 2016; 5:123–126
4. Mammucari M, Lazzari M, Maggiori E, Gafforio P, Tufaro G, Baffni S, Maggiori S, Sabato AF. Role of the informed consent, from mesotherapy to opioid therapy. Eur Rev Med Pharmacol Sci. 2014; 18(4):566-74.
Competing interests: No competing interests
This result should not be at all surprising. Low dose aspirin has a beneficial effect on inhibiting COX-1 which produces prostaglandins, most of which are pro-inflammatory, and thromboxanes, which promote clotting. However in higher doses aspirin loses its anti-clotting activity effect by inhibiting COX-2 in endothelial cells resulting in lower levels of the anti-coagulant, prostacyclin thus increasing the risk of thrombus and associated heart attacks and other circulatory problems. This is why aspirin is given at the low dose of 75mg (or 100mg) as an antiplatelet agent. Aspirin at therapeutic analgesic doses like any other NSAID will have an effect on inhibiting prostacyclin that outweighs any beneficial effect on reducing COX-1. I wonder how many patients continue on 75mg of aspirin while taking therapeutic doses of an NSAID which totally negates its effect?
Competing interests: No competing interests
Re: Risk of acute myocardial infarction with NSAIDs in real world use: bayesian meta-analysis of individual patient data
The meta-analysis from Bally et al [1], about risk of acute infarction (AMI) following use of commonly prescribed NSAIDs, shows data which may be of great interest (and concern) to public health: celecoxib appears to bring no or minimal increase in AMI risk, despite having a boxed warning in its label about its cardiovascular (CV) risk. The other NSAIDs evaluated clearly show an increase in risk: particularly surprising are data on naproxen since, in previous studies, it had been consistently shown not to bring additional CV risk using either observational [2] or experimental [3] data.
Of course, in a meta-analysis of observational data residual confounding “by indication” remains a possibility, despite authors’ efforts to limit it. This may help explain inconsistent data about naproxen, especially if we consider another meta-analysis of individual patient data from RCTs, which clearly excludes CV risk for that drug [3]. In addition, it may help explain why there is an immediate increase in risk (drug use may be linked to CV symptoms).
On the other side, observational data may help elucidate drug use (and possibly, their effects) in real practice. For this reason, it would be particularly important to get details on drug exposure (how many patients have been exposed to which drug, for how long and at to which dose), as well as the absolute number of events for each group. Information about dose and duration is especially critical, as CV risk has been shown to be dose-dependent [3] and different effectiveness of NSAIDs may influence treatment maintenance (this seems to be clear for celecoxib) [4]
Showing absolute data from this meta-analysis would provide such relevant insight and allow regulatory authorities to consider whether further studies on NSAIDs cardiovascular risk should be performed.
[1] Bally M, Dendukuri N, Rich B, et al. Risk of acute myocardial infarction with NSAIDs in real world use: bayesian meta-analysis of individual patient data. BMJ. 2017;357:j1909
[2] Varas-Lorenzo C, Riera-Guardia N, Calingaert B, et al. Myocardial infarction and individual nonsteroidal anti-inflammatory drugs meta-analysis of observational studies. Pharmacoepidemiol Drug Saf 2013; 22: 559–570
[3] Coxib and traditional NSAID Trialists’ (CNT) Collaboration. Vascular and upper gastrointestinal eff ects of non-steroidal anti-infl ammatory drugs: meta-analyses of individual participant data from randomised trials. Lancet 2013; 382: 769–79
[4] MacDonald TM, Hawkey CJ, Ford I, et al. Randomized trial of switching from prescribed non-selective non-steroidal anti-inflammatory drugs to prescribed celecoxib: the Standard care vs. Celecoxib Outcome Trial (SCOT). European Heart Journal 2016 doi:10.1093/eurheartj/ehw387
Competing interests: No competing interests