Tuesday, February 9, 2010

Post hoc non ergo propter hoc extended: A is associated with B therefore A causes B and removal of A removes B

From Annane et al, JAMA, January 27th, 2010 (see: http://jama.ama-assn.org/cgi/content/abstract/303/4/341 ):

"...patients whose septic shock is treated with hydrocortisone commonly have blood glucose levels higher than 180. These levels have clearly been associated with marked increase in the risk of dying...Thus, we hypothesized that normalization of blood glucose levels with intensive insulin treatment may improve the outcome of adults with septic shock who are treated with hydrocortisone."

The normalization heuristic is at work again.

Endocrine interventions as adjunctive treatments in critical care medicine have a sordid history. Here are some landmarks. Rewind 25 years, and as Angus has recently described (http://jama.ama-assn.org/cgi/content/extract/301/22/2388 ) we had the heroic administration of high dose corticosteroids (e.g. gram doses of methylprednisolone) for septic shock, which therapy was later abandoned. In the 1990s, we had two concurrent trials of human growth hormone in critical illness, showing the largest statistically significant harms (increased mortality of ~20%) from a therapy in critical illness that I'm aware of (see http://content.nejm.org/cgi/content/abstract/341/11/785 ). Early in the new millennium, based on two studies that should by now be largely discredited by their successors, we had intensive insulin therapy for patients with hyperglycemia and low dose corticosteroid therapy for septic shock. It is fitting then, and at least a little ironic, that this new decade should start with publication of a study combining these latter two therapies of dubious benefit: The aptly named COIITSS study.

I know this sounds overly pessimistic, but some of these therapies, these two in particular, just need to die, but are being kept alive by the hope, optimism, and proselytizing of those few individuals whose careers were made on them or continue to depend upon them. And I lament the fact that, as a result of the promotional efforts of these wayward souls, we have been distracted from the actual data. Allow me to summarize these briefly:

1.) The original Annane study of steroids in septic shock (see: http://jama.ama-assn.org/cgi/content/abstract/288/7/862 ) utilized an adjusted analysis of a subgroup of patients not identifiable at the outset of the trial (responders versus non-responders). The entire ITT (intention to treat) population had an ADJUSTED P-value of 0.09. I calculated an unadjusted P-value of 0.29 for the overall cohort. Since you cannot know at the outset who's a responder and who's not, for a practitioner, the group of interest is the ITT population, and there was NO EFFECT in this population. Somehow, the enthusiasm for this therapy was so great that we lost sight of the reasons that I assume the NEJM rejected this article - an adjusted analysis of a subgroup. Seriously! How did we lose sight of this? Blinded by hope and excitement, and the simplicity of the hypothesis - if it's low, make it high, and everything will be better. Then Sprung and the CORTICUS folks came along (see: http://content.nejm.org/cgi/content/abstract/358/2/111 ), and, as far as I'm concerned, blew the whole thing out of the water.

2.) I remember my attending raving about the Van den Berghe article (see: http://content.nejm.org/cgi/content/abstract/345/19/1359 ) as a first year fellow at Johns Hopkins in late 2001. He said "this is either the greatest therapy ever to come to critical care medicine, or these data are faked!" That got me interested. And I still distinctly remember circling something in the methods section, which was in small print in those days, on the left hand column of the left page back almost 9 years ago - that little detail about the dextrose infusions. This therapy appeared to work in post-cardiac surgery patients on dextrose infusions at a single center. I was always skeptical about it, and then the follow-up study came out, and lo and behold, NO EFFECT! But that study is still touted by the author as a positive one! Because again, like in Annane, if you remove those pesky patients who didn't stay in the MICU for 3 days (again, like Annane, not identifiable at the outset), you have a SUBGROUP analysis in which IIT (intensive insulin therapy - NOT intention to treat, ITT is inimical to IIT) works. Then you had NICE-SUGAR (see: http://content.nejm.org/cgi/content/abstract/360/13/1283 ) AND Brunkhorst et al (see: http://content.nejm.org/cgi/content/abstract/358/2/125 ) showing that IIT doesn't work. How much more data do we need? Why are we still doing this?

Because old habits die hard and so do true believers. Thus it was perhaps inevitable that we would have COITSS combine these two therapies into a single trial. Note that this trial does nothing to address whether hydrocortisone for septic shock is efficacious (it probably is NOT), but rather assumes that it is. I note also that it was started in 2006 just shortly before the second Van den Berghe study was published and well after the data from that study were known. Annane et al make no comments about whether those data impacted the conduct of their study, and whether participants were informed that a repeat of the trial upon which the Annane trail was predicated, had failed.

Annane did not use blinding for fludrocortisone in the current study, but this is minor. It is difficult to blind IIT, but usually what you do when you can't blind things adequately is you protocolize care. That was not obviously done in this trial; instead we are reassured that "everybody should have been following the Surviving Sepsis Campaign guidelines". (I'm paraphrasing.)

As astutely pointed out by Van den Berghe in the accompanying editorial, this trial was underpowered. It was just plain silly to assume (or play dumb) that a 3% ARR which is a ~25% RRR (since the baseline was under 10%) would translate into a 12.5% ARR with a baseline mortality of near 50%. Indeed, I don't know why we even talk about RRRs anymore, they're a ruse to inflate small numbers and rouse our emotions. (Her other comments, about "separation", which would be facilitated by having a very very intensive treatment and a very very lax control is reminiscent of what folks were saying about ARMA low/high Vt - namely that the trial was ungeneralizable because the "control" 12 cc/kg was unrealistic. Then you get into the Eichacker and Natanson arguments about U-shaped curves [to which there may be some truth] and how too much is bad, not enough is bad, but somewhere in the middle is the "sweet spot". And this is key. Would that I could know the sweet spot for blood sugar - and coax patients to remain there.)

Because retrospective power calculations are uncouth, I elected to calculate the 95% confidence interval (CI) for delta (the difference between the two groups) in this trial. The point estimate for delta is -2.96% (negative delta means the therapy was WORSE than control!) with a 95% confidence interval of -11.6% to +5.65%. It is most likely between 11% worse and 5% better, and any good betting man would wager that it's worse than control! But in either case, this confidence interval is uncomfortably wide and contains values for harm and benefit which should be meaningful to us, so in essence the data do not help us decide what to do with this therapy.

(And look at table 2, the main results, look they are still shamelessly reporting adjusted P-values! Isn't that why we randomize? So we don't have to adjust?)

TTo bring this saga full circle, I note that, as we saw in NICE-SUGAR, Brunkhorst, and Van den Berghe, severe hypoglycemia (<40!) was far more common in the IIT group. And severe hypoglycemia is associated with death (in most studies, but curiously not in this one). So, consistent with the hypothesis which was the impetus for this study (A is associated with B, thus A causes B and removal of A removes B), one conclusion from all these data is that hypoglycemia causes death, and should be avoided through avoidance of IIT.

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