We read with great interest the article by Myles et al. ,1“Avoidance of Nitrous Oxide for Patients Undergoing Major Surgery,” and the accompanying editorial.2We commend the extraordinary efforts by the authors in the execution of this large multicenter trial. As neuroanesthesiologists, we were particularly intrigued by the evaluation of this anesthetic gas, because it remains in common use in our specialty area and the safety and efficacy of nitrous oxide are periodically debated at national meetings and within the literature. Our concerns are directed at how this study, given the limitations of the trial, may inappropriately impact clinical practice.

Several specific negative impressions regarding the use of nitrous oxide that are conveyed but not substantiated by the study include the following:

First, the time to emergence recorded in the study calls into question one of the major benefits of nitrous oxide as an anesthetic. Its ability to facilitate a brisk and timely emergence has been well documented3and remains an attractive property to neuroanesthesiologists and others. Therefore, we were surprised by the 11-min time to eye-opening in the nitrous oxide group, which was both longer than expected and equal to that of the nitrous oxide–free group. We are accustomed to the very dependable less-than-3-min time to emergence that is largely independent of the duration of the surgical procedure and shorter than that observed with volatile agents alone. We suspect that the lack of blinding of those actually delivering the anesthetic and the use of Bispectral Index monitoring may have contributed to the similarity of the groups. Bispectral Index monitoring was more frequently used in the nitrous oxide–free group, but no data regarding Bispectral Index targets, use of muscle relaxants, or frequency of spontaneous ventilation were presented.

Second, in the introduction, the authors allude to the inactivation of vitamin B12and elevation of homocysteine by nitrous oxide as major concerns, despite millions of uncomplicated anesthetics and literature that has never substantiated a causal relation. For example, in the cited study by Deleu et al. ,4the investigators in their analysis noted no change in cobalamin or red cell folate levels between nitrous oxide and nitrous oxide–free patients. The three patients with postoperative neurologic symptoms had documented folate deficiency preoperatively, and no preoperative neurologic examination had been performed to establish a perioperative etiology for their condition.

Third, in the Discussion, the authors linked the use of nitrous oxide to a greater risk of myocardial infarction and death without statistical support. It is disconcerting to read that a causal association exists between an independent variable and outcome, but that it “lacked statistical significance.” Either a finding is significant or the null hypothesis must carry the day.

Fourth, in the introduction, the authors expressed concern about the detrimental effects of nitrous oxide on cerebral blood flow but failed to report any evidence to substantiate this claim in the Results or Discussion. In their study, no neurologic complications were ascribed to nitrous oxide use, although 15% of all cases were neurosurgical procedures. The use of nitrous oxide in neurosurgery has been criticized before, fueled by experimental studies suggesting a worsening of infarction in ischemic rat models. Such data have been elegantly countered by more recent work, demonstrating that the previous findings were likely a matter of experimental methodology rather than a distinct toxic effect of the gas.5Recently, the N -methyl-d-aspartic acid antagonist action of nitrous oxide has been shown to be neuroprotective in a number of models, similar in potency to xenon.6Hence, the neurotoxic claims on nitrous oxide seem to have been countered.

Fifth, the authors focus much of their attention on the topic of postoperative nausea and vomiting (PONV). In fact, the principal outcome data (fig. 4) prominently displays PONV outcomes first, highlighting the meaningful odds ratio. The data, however, are not new, surprising, or of much consequence. The literature generally supports that nitrous oxide and volatile anesthetics have a similar risk for PONV, whereas total intravenous anesthesia is associated with a reduced incidence.7As important, prophylactic therapy has been shown to greatly decrease the incidence of PONV. In the current study, only one third of the patients received prophylaxis; hence, the investigators’ priority to minimize PONV was low. Therefore, the data on PONV become less interesting. We subscribe, with excellent results, to the International Anesthesia Research Society Consensus Guidelines whereby patients with a 10% risk of emesis deserve cost-effective prophylaxis.8 

More generally, we must emphasize the importance of interpreting data clearly if we are to improve on evidence-based practice. In the above article, a significant finding in favor of the avoidance of nitrous oxide as part of a balanced anesthetic was the predominant claim. The clinical trial, however, prospectively defined the primary outcome measure as “duration of hospital stay.” Presumably this metric was a collective endpoint serving to capture the variety of “ill effects” from the use of the gas and their net impact on hospital stay. The clinical results for this primary endpoint satisfied the null hypothesis between the nitrous oxide and nitrous oxide–free groups. Although this was chiefly a negative study, both the abstract and Discussion present the principal outcome as a minor result after presentation of the secondary data, thereby minimizing the significance of this null effect. It could be argued this criticism is but a minor point. But all who manage spinal cord injury patients know very well that anesthesiologists, emergency physicians, and intensivists continue fighting to correct the false conclusion proliferated 16 yr ago when a prominent medical journal published trial results regarding infusion steroid therapy.9That trial was fundamentally negative (no clinical outcome difference between methylprednisolone vs.  placebo), but that point was obscured by the manner in which the article was published. Secondary, statistically flawed post hoc  analysis in that trial led the authors to further argue for a meager, functionally meaningless effect. Since then, thousands of patients have been treated with a therapy that, although not overtly toxic, is not benign. Worse yet, the treatment may have led to complacency by some acute care physicians, believing they had “done all they could” by administering steroids while possibly not being compulsive about spinal cord perfusion and other management strategies that do offer medical benefit. Although the results of that trial have been successfully refuted,10this treatment continues to have a life of its own. More recently, the controversy over tight glucose control for perioperative and intensive care unit patients rages, and numerous studies have recently been published, many with poorly designed methodology, with improperly drawn conclusions, and without appropriately emphasizing the risks of such therapy. In these studies, there was also a relative failure to properly recognize the numerous trials that have demonstrated toxicity without overt benefit.11,12 

In conclusion, studies that are largely negative in their primary outcome should not have a dramatic impact on practice. In this instance, more should be necessary before discarding the only anesthetic drug that has withstood the test of time. In contrast to the conclusion reached in the accompanying editorial, we view this study as additional evidence of the remarkable safety of nitrous oxide over the past 150 yr. Indeed, were nitrous oxide a new proprietary drug and marketed as a reliably short-acting, well-tolerated, inexpensive analgesic–anesthetic gas, it would be likely hailed as one of the most valuable adjuncts to the practice of anesthesiology.

*Johns Hopkins Medicine, Baltimore, Maryland. mmirski@jhmi.edu

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