The Cholesterol Hypothesis on the Beam: Dalcetrapib, PCSK9 inhibitors, and "off-target" effects of statins

The last month has witnessed the publication of three lines of research that could tip the balance of the evidence for the cholesterol hypothesis depending how things play out.  Followers of this blog know that I have a healthy degree of skepticism for the cholesterol hypothesis which was emboldened by studies of torcetrapib (blogged here and here) and anacetrapib that have come to light along with the failures of vytorin (ezetimibe; blogged here and here and here) and the addition of niacin to statins to improve cardiovascular outcomes in parallel with improvements in cholesterol numbers.

I think it's finally time to bury the CETP inhibitors. The November 29th NEJM (published online on November 5th) reports the results of the dal-OUTCOMES trial of dalcetrapib in patients with a recent acute coronary syndrome. Almost 16,000 patients were enrolled in this study of high risk patients, providing the study with ample power to detect meaningful improvements in cardiovascular outcomes - but alas, none were detected. The target is HDL, so the LDL hypothesis is not debunked by these data, but I think it is challenged nonetheless.

Luck that Looks Like Logic? Statins (Rosuvastatin), the Cholesterol Hypothesis, and Causal Pathways

The Cholesterol Hypothesis (CH), namely that the association between elevated cholesterol (LDL) and cardiovascular disease and events is a CAUSAL one, and thus that intervening to lower cholesterol prevents these diseases has seduced mainstream medicine for decades. However, much if not most of the evidence for the causality of cholesterol in atherogenesis and its reversal by lowering cholesterol derives from studies of "Statins" or HMG-CoA-reductase inhibitors; indeed the evidence that lowering LDL cholesterol (or raising HDL) through other pathways has salutary effects on cardiovascular outcomes is scant at best as has been chronicled on this blog (see posts on torcetrapib and ezetimibe/Vytorin). Not myself immune to the beguiling allure of the CH, I admit that I take Niacin, in spite of normal HDL levels and scant to no trustworthy evidence that, in addition to raising HDL and lowering LDL, it will have any primary (or secondary or tertiary) preventative effects for me.

In yesterday's NEJM, Glynn et al report the results of analysis of data on a secondary endpoint from the JUPITER trial of Rosuvastatin. (http://content.nejm.org/cgi/content/abstract/360/18/1851 .) The primary aim of the trial was to determine if Rosuvastatin was effective for primary prevention of cardiovascular events in people with normal cholesterol levels and elevated CRP levels. The secondary endpoint described in the article was the occurrence of venothromboembolism during the study period. Because I see no obvious evidence of foul play, and because this study was simply impeccably designed, conducted, and reported, I'm going to hereafter ignore the fact that it was industry sponsored, and that there is probably some motive of "off-label promotion by proxy" (http://medicalevidence.blogspot.com/2008/06/off-label-promotion-by-proxy-how-nejm.html .) here...

Lo and behold: Rosuvastatin lowered venothromboembolism rates. The difficulties posed by ascertainment of this outcome notwithstanding, this trial has convincing evidence of a statistically significant reduction in DVT and PE event rates (which were very low - ~0.2%/100 persons/year) during the four year period of study. And this does not make a whole lot of sense from the standpoint of the CH. There's something more going on. Like an anti-inflammatory property of Statins. Which is very interesting and noteworthy and worthwhile in its own right. But I'm more interested in what kind of light this sheds on the validity of the CH.

Because of my interest in the fraility of the normalization hypothesis/heuristic (the notion that you just measure something and then raise or lower it to the normal range and make things ALL better) I am obviously a reserved skeptic of the Cholesterol Hypothesis, which was bolstered by if not altogether reared by data from trials of statins. And these new data, combined with emerging evidence that statins may have salutary effects on lung inflammation in ARDS and COPD, among perhaps others, make me wonder - was it just pure LUCK rather than a triumph of LOGIC that the first widely tested and marketed drug for cholesterol happened to both reduce cardiovascular endpoints AND lower cholesterol, even though not necessarily as part of the same causal pathway? Is it just "true, true, and unrelated?" Are they the anti-inflammatory properties or some other piece of the complex biochemical effects of these drugs on the body that leads to their clinical benefits? Other examples come to mind: Is blood pressure lowering just an epiphenomenon of another primary ACE-inhibitor effect on heart failure? Because these effects appear to be superficially and intuitively related does not mean that they are an obvious causal pathway.

What if things had happened another way. What if Statins had eluded discovery for another 20-30 years. What if study of the cholesterol hypothesis meanwhile proceeded through evaluation of Cholestyramine, Cholestipol, Niacin, and other drugs, and what if it had been "disconfirmed" by failure of these agents to reduce cardiovascular outcomes? These hypotheticals will be answerable only after more study of Statins and other drugs as well as their mechanisms. The data presented by the Harvard group as well as their other work with CRP are but one leg of a long journey toward elucidation of the biological mechanisms of atherogenesis, coagulation, and downstream clinical events.

What do erythropoetin, strict rate control, torcetrapib, and diagonal earfold creases have in common? The normalization heuristic

I was pleased to see the letters to the editor in the May 6th edition of the NEJM regarding the article on the use of synthetic erythropoetins (see http://content.nejm.org/cgi/content/extract/362/18/1742 ). The letter writers must have been reading our paper on the normalization heuristic (NH)! (Actually, I doubt it. It's in an obscure journal. But maybe they should.)

In our article (available here: http://www.medical-hypotheses.com/article/S0306-9877(09)00033-4/abstract ), we operationalized the definition of the NH and attributed it to 4 errors in reasoning that lead it to be fallible as a general clinical hypothesis. Here is the number one reasoning error:

Where the normalization hypothesis is based on the assumption that the abnormal value is causally related to downstream patient outcomes, but in reality the abnormal value is not part of the causal pathway and rather is an epiphenomenon of another underlying process.

The authors of some of the letters to the editor of the NEJM have the same concerns about normalizing hemoglobin values, and the assumptions that this practice involves about our understanding of causal pathways. Which is what I want to focus on. So please turn your attention to, yes, the picture of the billiards.

I wager that the pathophysiological processes that occur in the body are more complex than the 16 balls in the photo, but it serves as a great analogy for understanding the limitations of what we know about what's going on in the body. Suppose that every time (or a high percentage of the time - we can probability adjust and not lose the meaning of the analogy) the cue ball, launched from the same spot at the same speed and angle, hits the 1--2--4--7--11 balls. We know the 11 ball is, say, cholesterol. We have figured this out. And it falls in the corner pocket - it gets "lower". But we don't know what the other balls represent, or even how many of them there are, or where they fall. We needn't know all of this to make some inferences. We see that when the cue ball is launched at a certain speed and angle, the 11 ball, cholesterol, falls. So we think we understand cholesterol. But the playing field is way more complex than the initiating event and the one final thing that we happen to be watching or measuring - the corner pocket. In the whole body, we don't even know how many balls and how many pockets we're dealing with! We only can see what we know to look for!

Suppose also that as a consequence of this cascade, the 7 ball hits the 12 ball, which falls in another corner pocket. We happen to be watching that pocket also. We know what it does. For lack of a better term, let's call it the "reduced cardiovascular death pocket." Every time this sequence of balls is hit, cholesterol (number 11) falls in one corner pocket, and the 12 ball falls in another pocket, and we infer that cholesterol is part of the causal pathway to cardiovascular death. But look carefully at the diagram. We can remove the 11 ball altogether, the 7 ball will still hit the 12 and sink it thus reducing cardiovascular death. So it's not the cholesterol at all! We misunderstood the causal pathway! It's not cholesterol falling per se, but rather some epiphenomenon of the sequence.

By now, you've inferred who is breaking. His name is atorvastatin (which I fondly refer to as the Lipid-Torpedo). When a guy called torcetrapib breaks, all hell breaks loose. We learn that there's another pocket called "increased cardiovascular death pocket" and balls start falling into there.

(A necessary aside here - I am NOT challenging the cholesterol hypothesis here. It may or may not be correct, and I certainly am not the one to figure that out. I merely wish to emphasize how we COULD make incorrect inferences about causal pathways.)

So when I see an article like there was a couple of weeks ago in the NEJM (see http://content.nejm.org/cgi/content/abstract/362/15/1363 ) about "strict rate control" for atrial fibrillation (AF), I am not surprised that it doesn't work. I am not surprised that there are processes going on in a patient with AF that we can't even begin to understand. And the coincidental fact that we can measure heart rate and control it does not mean that we're interrupting the causal pathway that we wish to.

A new colleague of mine told me the other day of a joke he likes to make that causes this to all resonate harmoniously - "We don't go around trying to iron out diagonal earfold creases to reduce cardiovascular mortality." But show us a sexy sequence of molecular cascades that we think we understand, and the sirens begin to sing their irresistible song.

If at first you don't succeed, try, try again: Anacetrapib picks up where Torcetrapib left off

I previously blogged on Torcetrapib because of my interest in causality and in a similar vein, the cholesterol hypothesis. And I was surprised and delighted when the ILLUMINATE trial showed that Torcetrapib, in spite of doubling HDL, failed miserably. Surprised because like so many others I couldn't really believe that if you double HDL that on balance wonderful things wouldn't happen; and delighted because of the possible insights this might give into the cholesterol hypothesis and causality. (See this post: http://medicalevidence.blogspot.com/2007/11/torcetrapib-torpedoed-sunk-by-surrogate.html )

I must have been too busy skiing when this article on Anacetrapib came out last year: http://www.nejm.org/doi/full/10.1056/NEJMoa1009744 . You may recall that after Torcetrapib was torpedoed, the race was on for apologists to find reasons it didn't work besides the obvious one, that it doesn't work. It raised blood pressure and does things to aldosterone synthesis, etc. Which I find preposterous. Here is an agent with profound effects on HDL and mild effects on other parameters (at least the parameters we can measure) and I am supposed to believe that the minor effects outweigh the major ones when it comes time to measure final outcomes? Heparin also affects aldosterone synthesis, but to my knowledge, when used appropriately to treat patients with clots, its major effects prevail over its minor effects and thus it doesn't kill people.


This is no matter to the true believers. Anacetrapib doesn't have these pesky minor effects, and it too doubles HDL, so the DEFINE investigators conducted a safety study to see if its lack of effects on aldosterone synthesis and the like might finally allow its robust effects on HDL to shine down favorably on cardiovascular outcomes (or at least not kill people.) The results are favorable, and there is no increase in blood pressure or changes in serum electrolytes, so their discussion focuses on all the reasons that this agent might be that Holy Grail of cholesterol lowering agents after all. All the while they continue to ignore the lack of any positive signal on cardiovascular outcomes at 72 weeks with this HDL-raising miracle agent, and what I think may be a secret player in this saga: CRP levels.

Only time and additional studies will tell, but I'd like to be on the record as saying that given the apocalyptic failure of Torcetrapib, the burden of evidence is great to demonstrate that this class will have positive effects on cardiovascular outcomes. I don't think it will. And the implications for the cholesterol hypothesis will perhaps be the CETP inhibitors' greatest contributions to science and medicine.

Torcetrapib Torpedoed: When the hypothesis is immune to the data

I have watched the torcetrapib saga with interest for some time now. This drug is a powerful non-HMG-CoA-reductase inhibitor raiser of HDL (up to a 100% increase) and effects modest decreases in LDL also (20%) as reported with great fanfare in the NEJM in 2004: http://content.nejm.org/cgi/content/abstract/350/15/1505.

Such was the enthusiasm for this drug that one editorialist in the same journal cried foul play in reference to Pfizer's intent to study the drug only with Lipitor, suggesting that such a move was intended to soften the blow to this blockbuster (read multibillion dollar) drug when it soon loses patent protection:
http://content.nejm.org/cgi/content/extract/352/25/2573.
The tone is one of serious concern - as this drug was expected to truly be spectacular at BOTH raising HDL and preventing cardiovascular morbidity and mortality - an assumption based on the well-established use of cholesterol lowering as a surrogate endpoint in trials of cardiovascular medications.

(I'm sure the Avandia analogy is banging like a clapper in your skull right now.)

But a perspicacious consumer of the literature on torcetrapib would have noted that there were precious few and conflicting data about its efficacy as an antiatherogenic agent - preclinical data from animal studies were neither consistent nor overwhelming regarding its effects on the vasculature (in spite of the use of VERY high doses of the drug yielding high degrees of CETP inhibition) and studies of patients with CETP mutations also were inconsistent regarding its influence on the development of cardiovascular disease. Certainly, one would expect a drug with such remarkable HDL raising abilities to do something substantial and consistent to sensitive measures of atherogenesis in preclinical studies or to have some consistent and perhaps dramatic effect in patients with mutations leading to high HDL levels. (For a good review of pre-clinical studies, see:
http://atvb.ahajournals.org/cgi/content/full/27/2/257?cookietest=yes and http://www.jlr.org/cgi/content/full/48/6/1263).
But alas, there was not consistent and robust evidence for anything but changes in surrogate markers. Of course this is all hindsight and it's easy for me to pontificate now that the horse was let out of the barn; first by Nissen et al: http://content.nejm.org/cgi/content/abstract/356/13/1304
and then today:
http://content.nejm.org/cgi/content/short/357/21/2109.
(In fact, I would say that the horse is galloping about the barnyard trammeling Lipitor's hopes of life after generic death.)


But what interests me now is not that the drug failed, and not that I have a new archetypal drug for failure of surrogate endpoints, but rather how difficult it is for the believers to let go. True believers die hard. How do the editors let a conclusion like this make it to print:


"In conclusion, our study neither validates nor invalidates the hypothesis that raising levels of HDL cholesterol by the inhibition of CETP may be cardioprotective. Thus, the possibility that the inhibition of CETP may be beneficial will remain hypothetical until it is put to the test in a trial with a CETP inhibitor that does not share the off-target pharmacologic effects of torcetrapib. "

Really?

Had the study been positive, would that have been the conclusion? No, the authors would have concluded that the hypothesis was validated.

So if the study is positive, the hypothesis is confirmed; but if it is negative (or shows harm), the hypothesis is immune to the data. The authors should not be allowed to have their cake and eat it too.

The above conclusion is tantamount to saying “our data do not bear on the hypothesis” which is tantamount to saying “our study was badly designed.”

Sure, another agent without that little BP problem may have more salutary effects on mortality, but I'd hate to be the guy trying to get that one through the IRB. Here we have a drug in a class that killed people in the last study. We'd better have more robust pre-clinical data the next time around. The other thing that fascinates me is the grasping for explanations. Here is a drug with ROBUST effects on HDL, and it causes an overall statistically significant increase in mortality. That's one helluva a hurdle for the next drug to jump even without the BP problem. Moreover, I refer the reader to the HOT trial:
(http://rss.sciencedirect.com/getMessage?registrationId=GHEIGIEIHNEJOHFJIHEPHIGKGJGPHHJQLZGQJNLMOE).
A 5 mmHg lowering of BP over a 3.8 year period reduced mortality by a mere 0.9% (p=0.32 - not significant). That's a small increase and it's not statistically significant. But lowering LDL with simvastatin (the 4S trial: Lancet. 1994 Nov 19;344(8934):1383-9.) for 3.3 years on average led 1.7% ARR in mortality (RR 0.70 (95% CI 0.58-0.85, p = 0.0003). So it would appear that on average, you get more bang for your buck in lowering cholesterol than you do in lowering BP. With an agent that is such a potent raiser of HDL, we would certainly expect at worst a null effect if the BP effect militated against the HDL/LDL effect. I have not done a meta-analysis of trials of BP lowering or cholesterol lowering, but I would be interested in the comparison. For now, I'm substantially convinced that the BP argument is abjectly insufficient to explain the failure of this agent to improve meaningful outcomes.

So the search will go on for a molecular variation of this agent which doesn't increase BP, with the hopes that another blockbuster cholesterol agent will be discovered. But in all likelihood, this mechanism of altering cholesterol metabolism is fatally flawed and I wouldn't volunteer any of my patients for the next trial. I'd give them 80mg of generic simvastatin or atorvastatin.

The Cardiologist Giveth, then the Cardiologist Taketh Away: Revision of the Cholesterol Guidelines

There has been quite a stir this week with the publication of the newest revision of the ACC/AHA guidelines for the treatment of cholesterol.  The New York Times is awash with articles summarizing or opining on the changes and many of the authors are perspicacious observers:

• 3 Things to Know About the New Cholesterol Guidelines by Harlan Krumholz of Yale
• Don’t Give More Patients Statins by authors from Harvard and UCSF
• Experts Reshape Treatment Guide for Cholesterol
• New Cholesterol Advice Startles Even Some Doctors
• Questions For A New Class of Cholesterol Drugs

As the old Spanish proverb states, "rio revuelto, ganancia de pescadores" - when the river is stirred up, the fishermen benefit.  I will admit that I'm gloating a bit since I consider the new guidelines to be a tacit affirmative nod to several posts on the topic of the cholesterol hypothesis (CH).  (More posts here and here and here, among several others - search for "cholesterol" or "causal pathways" on the Medical Evidence Blog search bar.)

Brief Updates on Hypothermia, Hyperglycemia, Cholesterol, Blood Pressure Lowering in Stroke and Testosterone

I've read a lot of interesting articles recently, but none that are sufficient fodder for a dedicated post.  So here I will update some themes from previous blog posts with recent articles from NEJM and JAMA that relate to them.

Prehospital Induction of Hypothermia After Cardiac Arrest
In this article in the January 1st issue of JAMA, investigators from King County Washington report the results of a trial which tested the hypothesis that earlier (prehospital) induction of hypothermia, by infusing cold saline, would augment the assumed benefit of hypothermia that is usually initiated in the hospital for patients with ventricular fibrillation.  Please guess what was the effect of this intervention on survival to hospital discharge and neurological outcomes.

You were right.  There was not even a signal, not a trend towards benefit, even though body temperature was lower by 1 degree Celcius and time to target hypothermia temperature in the hospital was one hour shorter.  However, the intervention group experienced re-arrest in the field significantly more often than the control group and had more pulmonary edema and diuretic use.  Readers interested in exploring this topic further are referred to this post on Homeopathic Hypothermia.

Hyperglycemic Control in Pediatric Intensive Care
In this article in the January 9th issue of NEJM, we are visited yet again by the zombie topic that refuses to die.  We keep looking for subgroups or populations that will benefit, and if we find one that appears to, it will be a Type I error, thinks the blogger with Bayesian inclinations.  In this trial, 1369 pediatric patients at 13 centers in England were randomized to tight versus conventional glycemic control.  Consistent with other trials in other populations, there was no benefit in the primary outcome, but tightly "controlled" children had much more and severe hypoglycemia.  The "cost effectiveness" analysis they report is irrelevant.  You can't have "cost effectiveness" of an ineffective therapy.  My, my, how we continue to grope.

Hope: The Mother of Bias in Research

I realized the other day that underlying every slanted report or overly-optimistic interpretation of a trial's results, every contorted post hoc analysis, every Big Pharma obfuscation, is hope.  And while hope is generally a good, positive emotion, it engenders great bias in the interpretation of medical research.  Consider this NYT article from last month:  "Dashing Hopes, Study Shows Cholesterol Drug Had No Effect on Heart Health."  The title itself reinforces my point, as do several quotes in the article.

“All of us would have put money on it,” said Dr. Peter Libby, a Harvard cardiologist. The drug, he said, “was the great hope.”

 Again, hope is wonderful, but it blinds people to the truth in everyday life and I'm afraid researchers are no more immune to its effects than the laity.  In my estimation, three main categories of hope creep into the evaluation of research and foments bias:

1. Hope for a cure, prevention, or treatment for a disease (on the part of patients, investigators, or both)
2. Hope for career advancement, funding, notoriety, being right (on the part of investigators) and related sunk cost bias
3. Hope for financial gain (usually on the part of Big Pharma and related industrial interests)

Consider prone positioning for ARDS.  For over 20 years, investigators have hoped that prone positioning improves not only oxygenation but also outcomes (mostly mortality).  So is it any wonder that after the most recent trial, in spite of the 4 or 5 previous failed trials, the community enthusiastically declared "success!"  "Prone Positioning works!"  Of course it is no wonder - this has been the hope for decades.

But consider what the most recent trial represents through the lens of replicability:  a failure to replicate previous results showing that prone positioning does not improve mortality.  The recent trial is the outlier.  It is the "false positive" rather than the previous trials being the "false negatives."

This way of interpreting the trials of prone positioning in the aggregate should be an obvious one, and it astonishes me that it took me so long to see the results this way - as a single failure to replicate previously replicable negative results.  But it hearkens to the underlying bias - we view results through the magnifying glass of hope, and it distorts our appraisal of the evidence.

Indeed, I have been accused of being a nihilist because of my views on this blog, which some see as derogating the work of others or an attempt to dash their hopes.  But these critics engage, or wish me to engage in a form of outcome bias - the value of the research lies in the integrity of its design, conduct, analysis, and reporting, not in its results.  One can do superlative research and get negative results, or shoddy research and get positive results.  My goal here is and always has been to judge the research on its merits, regardless of the results or the hopes that impel it.

(Aside:  Cholesterol researchers have a faith or hope in the cholesterol hypothesis - that cholesterol is a causal factor in pathways to cardiovascular outcomes.  Statin data corroborate this, and preliminary PCSK9 inhibitor data do, too.  But how quickly we engage in hopeful confirmation bias!  If cholesterol is a causal factor, it should not matter how you manipulate it - lower the cholesterol, lower cardiovascular events.  The fact that it does appear to matter how you lower it suggests that either there are multiplicity of agent effects (untoward and unknown effects of some agents negate some their beneficial effects in the cholesterol causal pathway) or that cholesterol levels are epiphenomena - markers of the effects of statins and PCSK9 inhibitors on the real, but as yet undelineated causal pathways.  Maybe the fact that we can easily measure cholesterol and that it is associated with outcomes in untreated individuals is a convenient accident of history that led us to trial statins which work in ways that we do not yet understand.)

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

Tipping the Scales of Noninferiority: Abbott's "Emboshield and Xact Carotid Stent System"

I just stumbled across this and think it's worth musing over it a bit.  The recently published ACT I trial by Rosenfield et al is a noninferiority trial of an already approved device, the "emboshield embolic protection system" used in conjunction with the "Xact carotid stent system" both proprietary devices from Abbott.  I'm scrutinizing this trial (and others) to determine if adequate justification is given for the noninferiority hypothesis around which the trial is designed.  One thing I'm looking for is  evidence that there are clear secondary advantages of the novel or experimental therapy that justify accepting some degree of worse efficacy, compared to the active control, which falls within the prespecified margin of noninferiority.  This is what the authors (or their ghosts) write in the introduction:

"Most carotid revascularization procedures in the United States are carotid endarterectomies performed for the treatment of asymptomatic atherosclerotic disease. Revascularization is also performed by means of stenting with devices to capture and remove emboli (“embolic protection” devices).3,4 In the Carotid Revascularization Endarterectomy versus Stenting Trial (CREST), no significant difference was found between carotid endarterectomy and stenting with embolic protection for the treatment of atherosclerotic carotid bifurcation stenosis with regard to the composite end point of stroke, death, or myocardial infarction.5 CREST included both symptomatic and asymptomatic patients, and it was not sufficiently powered to discern whether the carotid endarterectomy and stenting with embolic protection were equivalent according to symptomatic status. The primary aim of the Asymptomatic Carotid Trial (ACT) I was to compare the outcomes of carotid endarterectomy versus stenting with embolic protection in patients with asymptomatic severe carotid-artery stenosis who were at standard risk for surgical complications."

That's a mouthful, to say the least, and probably ought to be expectorated.

Fever, external cooling, biological precedent, and the epistemology of medical evidence

It is rare occasion that one article allows me to review so many aspects of the epistemology of medical evidence, but alas Schortgen et al afforded me that opportunity in the May 15th issue of AJRCCM.

The issues raised by this article are so numerous that I shall make subsections for each one. The authors of this RCT sought to determine the effect of external cooling of febrile septic patients on vasopressor requirements and mortality. Their conclusion was that "fever control using external cooling was safe and decreased vasopressor requirements and early mortality in septic shock." Let's explore the article and the issues it raises and see if this conclusion seems justified and how this study fits into current ICU practice.

PRIOR PROBABILITY, BIOLOGICAL PLAUSIBILITY, and BIOLOGICAL PRECEDENTS

These are related but distinct issues that are best considered both before a study is planned, and before its report is read. A clinical trial is in essence a diagnostic test of a hypothesis, and like a diagnostic test, its influence on what we already know depends not only on the characteristics of the test (sensitivity and specificity in a diagnostic test; alpha and power in the case of a clinical trial) but also on the strength of our prior beliefs. To quote Sagan [again], "extraordinary claims require extraordinary evidence." I like analogies of extremes: no trial result is sufficient to convince the skeptical observer that orange juice reduces mortality in sepsis by 30%; and no evidence, however cogently presented, is sufficient to convince him that the sun will not rise tomorrow. So when we read the title of this or any other study, we should pause to ask: What is my prior belief that external cooling will reduce mortality in septic shock? That it will reduce vasopressor requirements?

Overediagnosis and Mitigated Overdiagnosis: Ongoing problems with Breast and Lung Cancer Screening

I got to thinking about cancer screening (again) in the last week after reading in BMJ about the Canadian National Breast Screening Study (CNBSS).  That article piqued my interest because I immediately recalled the brouhaha that ensued after the U.S. Preventative Services Task Force (USPSTF) recommended that women not get mammograms until  age 50 rather than age 40.  That uproar was similar to the outcry by urologists when the USPSTF recommended against screening for prostate cancer with PSA testing.  Meanwhile, changes in the cholesterol guidelines have incited intellectual swashbuckling among experts in that field.  Without getting into the details, observers of these events might generate the following hypotheses:

1. People are comfortable with the status quo and uncomfortable with change
2. People get emotionally connected to good causes and this makes the truth blurry, or invisible.  After you've participated in the Race for the Cure, it's hard to swallow the possibility that the linchpin of the Race might not be as useful as we thought; and is no longer recommended for a whole swath of women. 
3. People are terrified of cancer
4. Screening costs money.  Somebody pockets that money.  Urologists and radiologists and gastroenterologists LOVE screening programs.  So do Porche dealers.