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Reply to the Letter to the Editor: Editorial: The New AAOS Guidelines on Knee Arthroscopy for Degenerative Meniscus Tears Are a Step in the Wrong Direction

2022; Lippincott Williams & Wilkins; Volume: 480; Issue: 6 Linguagem: Inglês

10.1097/corr.0000000000002228

1528-1132

Seth S. Leopold,

Shoulder Injury and Treatment

I want to thank Getelman and colleagues for their thoughtful letter [4]. I appreciate the opportunity to continue a dialogue on this important topic. I also agree with the letter writers that the Clinical Practice Guidelines (CPGs) produced by the American Academy of Orthopaedic Surgeons (AAOS) are important. I've written in the past in this space promoting their CPGs when they've gotten it right; for example, regarding the Academy's CPG about viscosupplementation, I wrote: "One of my proudest moments as a member of the AAOS was when the Academy's clinical practice guideline on nonsurgical treatments of arthritis followed the evidence and gave a four-star (strong evidence) recommendation against viscosupplementation for knee arthritis despite what must have been tremendous pressure to do otherwise" [10]. In general, I'm a fan of AAOS CPGs, and I wouldn't want anyone to think otherwise. But the CPG-based recommendations regarding arthroscopic surgery for meniscal tears in patients with arthritis went from out of date [10] to out of touch, as I wrote in the editorial that Getelman and colleagues commented on [11]. I believe the newer Academy CPG on the topic [2] quotes selectively from the available evidence, misinterprets much of what it cites, and fails to engage with a substantial number of high-quality randomized trials on the topic. Getelman and colleagues [4] are correct that practicing high-quality orthopaedic surgery involves marrying experienced-based good judgment with a discerning eye for integrating the best-available evidence. And when it comes to the indications for some of the procedures we perform, must make decisions in the absence of strong evidence. Arthroscopic partial meniscectomy in patients with osteoarthritis is not one of those procedures. On that topic, we are blessed with a surfeit of well-done randomized trials [5-8, 12, 13, 15] that essentially all point in the same direction: This operation does not seem to be better than nonsurgical treatment (indeed, the latest AAOS CPG says as much, except that, bizarrely, it seems to use that as a justification to recommend surgery) and it's not even better than placebo surgery. High-quality studies of other designs likewise confirm the general inefficacy of this procedure for this indication [1, 14]. It would be different if there were substantial disagreements across randomized trials on the topic—in such a circumstance, perhaps justifying surgical choices in this context with hand-waving about "surgeon experience" could be rationalized—but there is not. I'm only aware of one randomized trial that concluded more favorably about arthroscopic surgery [3], and it had a host of problems that I've identified before [10]. When the balance of the evidence tips this heavily in one direction, we shouldn't use our "experience" to lay aside the findings of study after study after study. The bedrock principle of science that undergirds modern medicine is the falsifiable hypothesis. If the mountain of high-quality evidence on this topic is insufficient to convince surgeons that arthroscopic partial meniscectomy for this indication is ineffective, I am curious: What would it take? As for attending to the specific arguments in their letter [4], while it's true that randomized trials have shortcomings, vague concepts about how the patients in those studies might not look like yours or mine should not cause one to disqualify them. By contrast, "experience" has several disqualifying problems in this context. The most important of those are transfer bias (is the follow-up sufficiently long and complete to really know how something is working?) and assessment bias (how do we evaluate our results?). Typical surgeons follow patients for a few months after arthroscopic meniscectomy; most of the randomized trials I've mentioned evaluate patients at a year, 2 years, or longer. Typical surgeons' perceptions about our "experience" with a procedure derive from visits with patients we see in follow-up; our unhappy patients are more likely to go elsewhere. And in terms of assessment, grading our own patients' surgical results is not nearly as robust, realistic, or fair as using independent assessors, as was done in most of the randomized trials I've mentioned. Importantly, the effects of transfer and assessment bias don't offset one another; rather, they're augmentative. They make the treatment as evaluated by our "experience"—in this case, arthroscopic partial meniscectomy—seem much more effective than it really is. Getelman and colleagues [4] are right that intention-to-treat analyses result in more-conservative interpretations of datasets in clinical trials because of the effects of crossover from nonsurgical to surgical treatments. I'll share two thoughts on that. First, shouldn't we apply a more-conservative standard if we're going to recommend an invasive treatment? And, second, arthroscopic partial meniscectomy often doesn't even hold up when examined under the more-permissive standard that Getelman et al. seem to prefer. Results from as-treated analyses of the randomized trials I've mentioned, when they are available, often differ little from the results obtained by more-stringent intention-to-treat analyses [8]. In other words, even if someone crosses over from exercise therapy to arthroscopic treatment, and we give arthroscopic treatment the benefit of the doubt in the analysis, it's still no better. And in many of these trials, the number of patients who crossed over from nonsurgical to arthroscopic treatment was too small to make much of a difference, anyway [5, 13]. For those reasons, concerns about crossover and intention-to-treat analyses do not seem to hold much water in this specific body of evidence. Regarding their thoughts about the inappropriateness of placebo controls, I agree with the letter writers that placebos have real effects, especially on more subjective endpoints like pain, and we agree that patients' level of motivation (as well as the invasiveness of the treatment) do matter [9]. But if we're to look a patient in the eye and suggest that our surgical intervention works—an intervention that is associated with real risk, pain, cost, and downtime—shouldn't we expect our intervention not merely to outperform sham interventions, but to outperform them by a wide margin? As we learn more, we should refine our practices. The history of surgery, including modern orthopaedic surgery, includes many procedures that well-intentioned people performed under the mistaken belief that they were helpful. It seems to me that arthroscopic partial meniscectomy in patients with arthritis should, in most instances, be consigned to that group. At some point, we have to be open to the possibility that what we thought was true might not be.