Is There a Baby in That Bathwater? Status Quo Bias in Evidence Appraisal in Critical Care

"But we are not here concerned with hopes and fears, only the truth so far as our reason allows us to discover it."  -  Charles Darwin, The Descent of Man

Status quo bias is a cognitive decision making bias that leads to decision makers' preference for the choice represented by the current status quo, even when the status quo is arbitrary or irrelevant.  Decision makers tend to perceive a change from the status quo as a loss and therefore their decisions are biased toward the status quo.  This can lead to preference reversals when the status quo reference frame is changed.  The status quo can be debiased using a reversal test, i.e., manipulating the status quo either experimentally or via thought experiment to consider a change in the opposite direction.  If reluctance to change from the status quo exists in both directions, status quo bias is likely to exist.

My collaborators Peter Terry, Hal Arkes and I reported in a study published in 2006 that physicians were far more likely to abandon a therapy that was status quo or standard therapy based on new evidence of harm than they were to adopt an identical therapy based on the same evidence of benefit from a fictitious RCT (randomized controlled trial) presented in the vignette.  These results suggested that there was an asymmetric status quo bias - physicians showed a strong preference for the status quo in the adoption of new therapies, but a strong preference for abandoning the status quo when a standard of care was shown to be harmful.  Two characteristics of the vignettes used in this intersubject study deserve attention.  First, the vignettes described a standard or status quo therapy that had no support from RCTs prior to the fictitious one described in the vignette.  Second, this study was driven in part by what I perceived at the time was a curious lack of adoption of drotrecogin-alfa (Xigris), with its then purported mortality benefit and associated bleeding risk.  Thus, our vignettes had very significant trade-offs in terms of side effects in both the adopt and abandon reference frames.  Our results seemed to explain s/low uptake of Xigris, and were also consistent with the relatively rapid abandonment of hormone replacement therapy (HRT) after publication of the WHI, the first RCT of HRT.

The Intensivist Giveth Then the Intensivist Taketh Away: Esmolol in Septic Patients Receiving High Dose Norepinephrine

Two studies in the October 23/30 issue of JAMA serve as fodder for reflection on the history and direction of critical care research and the hypotheses that drive it.   Morelli et all report the results of a study of Esmolol in septic shock.  To quickly summarize, this was a single center dose ranging study the primary aim of which was to determine if esmolol could be titrated to a heart rate goal (primary outcome), presumably with the later goal of performing a phase 3 clinical trial to see if esmolol, titrated in such a fashion, could favorably influence clinical outcomes of interest.  154 patients with septic shock on high dose norepinephrine with a heart rate greater than 95 were enrolled, and heart rate was indeed lower in the esmolol group (P less than 0.001).  Perhaps surprisingly, hemodynamic parameters, lactate clearance, and pressor and fluid requirements were (statistically significantly) improved in the esmolol group.  Most surprising (and probably the reason why we find this published in JAMA rather than Critical Care Medicine - consider that outlier results such as this may get disproportionate attention), mortality in the esmolol group was 50% compared to 80% in the control group (P less than 0.001).  The usual caveats apply here:  a small study, a single center, lack of blinding.  And regular readers will guess that I won't swallow the mortality difference.  I'm a Bayesian (click here for a nice easy-to-use Bayesian calcluator), there's no biological precedent for such a finding and it's too big a bite for me to swallow. So I will go on the record here as stating that I'm betting against similar results in a larger trial.

I'm more interested in how we formulate the hypothesis that esmolol will provide benefit in septic shock.  I was a second year medical student in 1995 when Gattinoni et al published the results of a trial of "goal-oriented hemodynamic therapy" in critically ill patients in the NEJM.  I realize that critical care research as we now recognize it was in its adolescence then, as a quick look at the methods section of that article demonstrates.  I also recognize that they enrolled a heterogenous patient population.  But it is worth reviewing the wording of the introduction to their article:

Recently, increasing attention has been directed to the hemodynamic treatment of critically ill patients, because it has been observed in several studies that patients who survived had values for the cardiac index and oxygen delivery that were higher than those of patients who died and, more important, higher than standard physiologic values.1-3 Cardiac-index values greater than 4.5 liters per minute per square meter of body-surface area and oxygen-delivery values greater than 650 ml per minute per square meter — derived empirically on the basis of the median values for patients who previously survived critical surgical illness — are commonly referred to as supranormal hemodynamic values.4

No Sham Needed in Sham Trials: Polymyxin B Hemoperfusion in Abdominal Septic Shock (Alternative Title: How Meddling Ethicists Ruin Everything)

This a superlative article to jab at to demonstrate some interesting points about randomized controlled trials that have more basis in hope than reason and whose very design threatens to invalidate their findings: http://jama.ama-assn.org/cgi/content/abstract/301/23/2445?maxtoshow=&HITS=10&hits=10&RESULTFORMAT=&fulltext=polymyxin&searchid=1&FIRSTINDEX=0&resourcetype=HWCIT . Because endotoxin has an important role in the pathogenesis of gram-negative sepsis, there has been interest in interfering with it or removing it in the hopes of abating the untoward effects of the sepsis inflammatory cascade. Learning from previous experiences/studies (e.g., http://content.nejm.org/cgi/content/abstract/324/7/429 ) that taking a poorly defined and heterogenous illness (namely sepsis) and using therapy that is expected to work in only a subset of patients with the illness (gram-negative source), the authors chose to study abdominal sepsis because they expected that the majority of patients will have gram-negatives as a causative or contributory source of infection. They randomized such patients to receive standard care (not well defined) or the insertion of a dialysis catheter with subsequent hemoperfusion over a Polymyxin B impregnated surface because this agent is known to adsorb endotoxin. The basic biological hypothesis is that removing the endotoxin in this fashion will cause amelioration of the untoward effects of the sepsis inflammatory cascade in such a way as to improve blood pressure, other phyisological parameters, and hopefully, mortality as well. There is reason to begin one's reading of this report with robust skepticism. The history of modern molecular medicine, for well over 25 years, has been polluted with the vast detritus of innumerable failed sepsis trials founded on hypotheses related to modulation of the sepsis cascade. During this period, only one agent has been shown to be efficacious, and even its efficacy remains highly doubtful to perhaps the majority of intensivists (myself excluded; see: http://content.nejm.org/cgi/content/abstract/344/10/699 ).


Mortality was not the primary endpoint in this trial, but rather was used for the early stopping rule. Even though I am currently writing an article suggesting that mortality may not be a good endpoint for trials of critical illness, this trial reminds me why the critical care community has selected this endpoint as the bona fide gold standard. Who cares if this invasive therapy increases your MAP from the already acceptable level of ~77mmHg to the supertarget level of 86? Who cares if it reduces your pressor requirements? Why would a patient, upon awakening from critical illness, thank his doctors for inserting a large dialysis catheter in him to keep his BP a little higher than it otherwise would have been? Why would he rather have a giant hole in his neck (or worse - GROIN!) than a little more levophed? If it doesn't save your life or make your life better when you recover, why do you care? We desperately need to begin to study concepts such as "return to full functionality at three (or six) months" or "recovery without persistent organ failures at x,y,z months". (This latter term I would define as not needing ongoing therapy for the support of any lingering organ failure after critical illness [that did not exist in the premorbid state], such as oxygen therapy, tracheostomy, dialysis, etc.). Should I be counted as a "save" if my existence after the interventions of the "saviors" is constituted by residence in a nursing home dependent on others for my care with waxing and waning lucidity? What does society think about these questions? We should begin to ask.

And we segue to the stopping issue which I find especially intriguing. Basing the stopping rule on a mortality difference seems to validate my points above, namely that the primary endpoint (MAP) is basically a worthless one - if it were not, or if it were not trumped by mortality, why would we not base stopping of the trial on MAP? (And if this is a Phase II or pilot trial, it should be named accordingly, methinks.) This small trial was stopped on the basis of a mortality difference significant at P=0.026 with the stopping boundary at P<0.029. I will point out again on this blog for those not familiar with it this pivotal article warning of the hazards of early stopping rules (http://jama.ama-assn.org/cgi/content/abstract/294/17/2203 ). But here's the real rub. When they got these results at the first and only planned interim analysis, (deep breath), they consulted with an ethicist. The ethicist said that it is unethical to continue the trial because to do so would be to deny this presumably effective therapy to the control group. But does ANYONE in his or her right state of mind agree that this therapy is effective on the basis of these data? And if these data are not conclusive, does not that condemn future participants in a future trial to the same unfair treatment, namely randomization to placebo? Does not stopping the trial early just shift the burden to other people? It does worse. It invalidates to large degree the altruistic motives of the participants (or their surrogates) in the current trial because stopping it early invalidated it scientifically (per the above referenced article) and because stopping it early necessitates the performance of yet another larger trial where participants will be randomized to placebo, and which, it is fair to suspect, will demonstrate this therapy to be useless, which is tantamount to harmful in the net because of the risk of catheters and wasted resources in performing yet another trial. Likewise, if we assume that this therapy IS beneficial, stopping it has reduced NET utility to current participants, because now NOBODY is receiving the therapy. So, from a consequentialist or utilitarian standpoint, overall utility is reduced and net harm has resulted from stopping the trial. What if the investigators of this trial had made it more scientifically valid from the outset by using a sham hemoperfusion device (an approach that itself would have caused an ethical maelstrom)? And what if the sham group proved superior in terms of mortality - would the ethicists have argued for stopping the trial because continuing it would mean depriving patients of sham therapy? Would there have been a call for providing sham therapy to all patients with surgically intervened abdominal sepsis? I write this with my tongue in my cheek, but the ludicrousness of it does seem to drive home the point that the premature stopping of this trial is neither ethically clear-cut nor obligatory, and that from a utilitarian standpoint, net negative utility (for society and for participants - for everyone!) has resulted from this move. And that segues me to the issue of sham procedures. It is abundantly obvious that patients with a dialysis catheter inserted for this trial (probably put in by an investigator, but not stated in the manuscript) will be likely to receive more vigilant care. This is the whole reason that protocols were developed in critical care research, as a result of the early ECMO trials (Morris et al 1994) where it was recognized that you would have all sorts of confounding by the inability to blind treating physicians in such a study. While it is not feasible to blind an ECMO study, the investigators of this study do little to convince us that blinding was not possible and feasible, and they make light of the differences in care that may have resulted from lack of blinding. Moreover, they do not report on the use of protocols for patient care that may/could have minimized the impact of lack of blinding, and in a GLARING omission, they do not describe fluid balance in these patients, a highly discretionary aspect of care that clearly could have influenced the primary outcome and which could have been differential between groups because of the lack of blinding and sham procedures. Unbelievable! (As an afterthought, even the mere increased stimulation [tactile, auditory, or visual] of patients in the intervention group, by more nursing presence or physician presence in the room may have led to increases in blood pressure.) There are also some smaller points, such as the fact that by my count 10 patients (not accounting for multiple organisms) in the intervention group had gram positive or fungal infections making it difficult to imagine how the therapy could have influenced these patients. What if patients without gram-negative organisms isolated are excluded from the analysis? Does the effect persist? What is the p-value for mortality then? And that point segues me to a final point - if our biologically plausible hypothesis is that reducing endotoxin levels with this therapy leads to improvements in parameters of interest, why, for the love of God, did we not measure and report endotoxin levels and perform secondary analyses of the effect of the therapy as a function of endotoxin levels and also report data on whether these levels were reduced by the therapy, thus supporting the most fundamental assumption of the biological hypothesis upon which the entire study is predicated?