Another excellent critical care article was published this week in NEJM, the SOAP II study: http://content.nejm.org/cgi/content/short/362/9/779 . In this RCT of norepinephrine (norepi, levophed, or "levo" for short) versus dopamine ("dopa" for short) for the treatment of shock, the authors tried to resolve the longstanding uncertainty and debate surrounding the treatment of patients in various shock states. Proponents of any agent in this debate have often hung their hats on extrapolations of physiological and pharmacological principles to intact humans, leading to colloquialisms such as "leave-em-dead" for levophed and "renal-dose dopamine". This blog has previously emphasized the frailty of pathophysiological reasoning, the same reasoning which has irresistibly drawn cardiologists and nephrologists to dopamine because of its presumed beneficial effects on cardiac and urine output, and, by association, outcomes.

Hopefully all docs with a horse in this race will take note of the outcome of this study. In its simplest and most straightforward and technically correct interpretation, levo was not superior to dopa in terms of an effect on mortality, but was indeed superior in terms of side effects, particularly cardiac arrhythmias (a secondary endpoint). The direction of the mortality trend was in favor of levo, consistent with observational data (the SOAP I study by many of the same authors) showing reduced mortality with levo compared with dopa in the treatment of shock. As followers of this blog also know, the interpretation of "negative" studies (that is, MOST studies in critical care medicine - more on that in a future post) can be more challenging than the interpretation of positive studies, because "absence of evidence is not evidence of absence".

We could go to the statistical analysis section, and I could harp on the choice of delta, the decision to base it on a relative risk reduction, the failure to predict a baseline mortality, etc. (I will note that at least the authors defended their delta based on prior data, something that is a rarity - again, a future post will focus on this.) But, let's just be practical and examine the 95% CI of the mortality difference (the primary endpoint) and try to determine whether it contains or excludes any clinically meaningful values that may allow us to compare these two treatments. First, we have to go to the raw data and find the 95% CI of the ARR, because the Odds Ratio can inflate small differences as you know. That is, if the baseline is 1%, then a statistically significant increase in odds of 1.4 is not meaningful because it represents only a 0.4% increase in the outcome - miniscule. With Stata, we find that the ARR is 4.0%, with a 95% CI of -0.76% (favors dopamine) to +8.8% (favors levo). Wowza! Suppose we say that a 3% difference in mortality in either direction is our threshold for CLINICAL significance. This 95% CI includes a whole swath of values between 3% and 8.8% that are of interest to us and they are all in favor of levo. (Recall that perhaps the most lauded trial in critical care medicine, the ARDSnet ARMA study, reduced mortality by just 9%.) On the other side of the spectrum, the range of values in favor of dopa is quite narrow indeed - from 0% to -0.76%, all well below our threshold for clinical significance (that is, the minimal clinically important difference or MCID) of 3%. So indeed, this study surely seems to suggest that if we ever choose between these two widely available and commonly used agents, the cake goes to levo, hands down. I hardly need a statistically significant result with a 95% CI like this one!

So, then, why was the study deemed "negative"? There are a few reasons. Firstly, the trial is probably guilty of "delta inflation" whereby investigators seek a pre-specified delta that is larger than is realistic. While they used, ostensibly, 7%, the value found in the observational SOAP I study, they did not account for regression to the mean, or allow any buffer for the finding of a smaller difference. However, one can hardly blame them. Had they looked instead for 6%, and had the 4% trend continued for additional enrollees, 300 additional patients in each group (or about 1150 in each arm) would have been required and the final P-value would have still fallen short at 0.06. Only if they had sought a 5% delta, which would have DOUBLED the sample size to 1600 per arm, would they have achieved a statistically significant result with 4% ARR, with P=0.024. Such is the magnitude of the necessary increase in sample size as you seek smaller and smaller deltas.

Which brings me to the second issue. If delta inflation leads to negative studies, and logistical and financial constraints prohibit the enrollment of massive numbers of patients, what is an investigator to do? Sadly, the poor investigator wishing to publish in the NEJM or indeed any peer reviewed journal is hamstrung by conventions that few these days even really understand anymore: namely, the mandatory use of 0.05 for alpha and "doubly significant" power calculations for hypothesis testing. I will not comment more on the latter other than to say that interested readers can google this and find some interesting, if arcane, material. As regards the former, a few comments.

The choice of 0.05 for the type 1 error rate, that is, the probability that we will reject the null hypothesis based on the data and falsely conclude that one therapy is superior to the other; and the choice of 10-20% for the type 2 error rate (power 80-90%), that is the probability that the alternative hypothesis is really true and we will reject it based on the data; derive from the traditional assumption, which is itself an omission bias, that it is better in the name of safety to keep new agents out of practice by having a more stringent requirement for accepting efficacy than the requirement for rejecting it. This asymmetry is the design of trials is of dubious rationality from the outset (because it is an omission bias), but it is especially nettlesome when the trial is comparing two agents already in widespread use. As opposed to the trial of a new drug compared to placebo, where we want to set the hurdle high for declaring efficacy, especially when the drug might have side effects - with levo versus dopa, the real risk is that we'll continue to consider them to be equivalent choices when there is strong reason to favor one over the other based either on previous or current data. This is NOT a trial of treatment versus no treatment of shock, this trial assumes that you're going to treat the shock with SOMETHING. In a trial such as this one, one could make a strong argument that a P-value of 0.10 should be the threshold for statistical significance. In my mind it should have been.

But as long as the perspicacious consumer of the literature and reader of this blog takes P-values with a grain of salt and pays careful attention to the confidence intervals and the MCID (whatever that may be for the individual), s/he will not be misled by the deeply entrenched convention of alpha at 0.05, power at 90%, and delta wildly inflated to keep the editors and funding agencies mollified.

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New reader here. Interesting perspective. Clearly, the statistical flaws in the many clinical studies range from the obvious to the relatively subtle and clinicians need to be aware of and consider these limitations when deciding to accept or reject the conclusions of the study.

ReplyDeleteI agree that this "one size fits all" statistical approach is unrealistic. However, I do question your suggestion that an individual interpretation of the 95% CI is a suitable substitute for a stastically significant result, the purpose of which is to give us some indication that the results obtained from this sample are not due to chance and can be extrapolated to the entire population. Statistically, dopamine is just as likely to be 0.76% better as norepi is to be 8.8% better. Without this mechanism, I don't think we're any better off than using physiological principles alone for clinical decisionmaking.

But Eric, if you're a WISE betting man, and you're going to bet, you oughta bet on the point estimate rather than one of those two extremes....

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ReplyDeleteI agree 100% with your opinion, but that's neither here nor there. The point is that we don't know any more or less than we did before this study was published. There is a concerning absence of statistical validity and reproducibility of results in critical care trials, which makes betting a bit more dicey. And THAT is the problem--uninterpretable literature. Misinformation is sometimes worse than no information...

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