NEJM letter and cardiac arrest trial

I recently had a letter in the New England Journal of Medicine, about a trial they had published that compared continuous versus interrupted chest compressions during resuscitation after cardiac arrest. Interrupted compressions are standard care – the interruptions are for ventilations to oxygenate the blood, prior to resuming chest compressions to keep it circulating. The issue was that the result of the trial was 0.7% better survival in the interrupted-compression group, with 95% CI from -1.5% to 0.1%. So the data are suggesting a probable benefit to interrupted compressions. However, on Twitter the NEJM announced this as “no difference”, no doubt because the difference was not “statistically significant”. So I wrote pointing out that this wasn’t a good interpretation, and the dichotomy into “significant” and “non-significant” is pretty unhelpful in situations where the results are close to “significance”. Bayesian methods have a huge advantage here, in that they can actually quantify the probability of benefit. An 80% probability that the treatment is beneficial is a lot more useful than “non-significance”, and might lead to very different actions.

The letter was published along with a very brief reply from the authors (they were probably constrained, as I was in the original letter, by a tiny word limit): “Bayesian analyses of trials are said to offer some advantages over traditional frequentist analyses. A limitation of the former is that different people have different prior beliefs about the effect of treatment. Alternative interpretations of our results offered by others show that there was not widespread clinical consensus on these prior beliefs. We are not responsible for how the trial results were interpreted on Twitter.”

Taking the last point first: no, the authors did not write the Twitter post. But they also did not object to it. I’m not accusing them of making the error that non-significance = no difference, but it is so common that it usually – as here – passes without comment. But it’s just wrong.

Their initial point about priors illustrates a common view, that Bayesian analysis is about incorporating individual prior beliefs into the analysis. While you can do this, it is neither necessary nor a primary aim. As Andrew Gelman has said (and I have repeated before); prior information not prior beliefs. We want to base a prior on the information that we have at the start of the trial, and if that is no information, then that’s fine. However, we almost always do have some information on what the treatment effect might plausibly be. For example, it’s very unusual to find an odds ratio of 10 in any trial, so an appropriate prior would make effects of this (implausible) size unlikely. More importantly, in this case, getting too hung up on priors is a bit irrelevant, because the trial was so huge (over 20,000 participants) that the data will completely swamp any reasonable prior.

It isn’t possible to re-create the analysis from the information in the paper, as it was a cluster-randomised trial with crossover, which needs to be taken into account. Just using the outcome data for survival to discharge in a quick and dirty Bayesian analysis, though, gives a 95% credible interval of something like from 0.84 to 1.00, with a probability of the odds ratio being less than 1 of about 98%. That probably isn’t too far away from the correct result, and suggests pretty strongly that survival may be a bit worse in the continuous compression group. “No difference” just doesn’t seem like an adequate summary to me.

My letter and the authors’ reply are here:

The original trial report is: Nichol G, Leroux B, Wang H, et al. Trial of continuous or interrupted chest compressions during CPR. N Engl J Med 2015;373:2203-2214

Original post 14 April 2016 http://blogs.warwick.ac.uk/simongates/entry/nejm_letter_and/

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