Happy Anniversary to the Blog! Two Years Old!

The medical evidence blog has turned out to be a fruitful experience for me and hopefully for others. The idea was conceived while I was at OSU auditing a course on capital punishment in the law school taught by the wonderful Douglas Berman, JD, who used a blog as part of the course material and who created the prominent SLAP (Sentencing Law and Punishment) blog. That formative and enriching experience led me to create this blog to ruffle feathers in the medical evidence community, as an alternative to numerous and sundry letters to the editor of the NEJM which I had theretofore been writing. (Every now and again I lose the ability to restrain myself and submit a letter in spite of the blog.) The experiment has paid off, I hope, and hopefully this blog provides fodder for thoughtful clinicians and researchers, as well as physicians in training, and journal clubs. I hope that the tradition of the first two years will continue into perpetuity and we will beat the bushes of evidence on this blog as we strive to understand the truth and the limitations of what is currently known using our logic and our sense of reason to guide us. Thank all of you who have followed this blog for the encouragement to keep it going.

Cheers, Scott

Type rest of the post here

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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?

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Randomized controlled trial of an intervention to reduce gun-related violence: A Parody

I am incredibly disappointed that the journal that I consider to be the very pinnacle of medical evidence continues to print ideological propaganda without any regard whatever to evidence and logic when it suits the editorial agenda http://content.nejm.org/cgi/content/extract/360/22/2360. Unadulterated propaganda pieces related to capital punishment, abortion, and gun control are shamelessly and predictably aligned with a singular political stance, and evidence and logic are eschewed entirely in favor of dogmatic and sanctimonious deontology. Without slinging any more mud on my favorite journal, I will demonstrate this in the following parody:

ARTICLE TITLE:
Efficacy of a gun control policy in reducing gun-related violence: A multi-state, multi-center, randomized controlled trial.

BACKGROUND:
Gun related violence results in tens of thousands of deaths (mostly suicides and homicides) each year. Interventions to reduce the toll of gun-related violence are desperately needed.

METHODS:
We used CDC data on gun-related deaths over the last decade to identify populations at risk for gun-related violence. However, our inclusion criteria did not comport with NIH-funding guidelines about inclusion of women and minorities and vulnerable populations such as former prisoners and felons and people with mental disabilities, some of which were over-represented and some of which were under-represented in the at-risk group we identified. Therefore, we dropped inclusion and exclusion criteria altogether, and randomized the entire populations of several states to the intervention (moratorium on firearms ownership defined as a complete ban imposed by state legislatures coupled with Directly Observed Confiscation) versus control (no moratorium or ban). Causes of deaths in each group were tracked and adjudicated by medical examiners in each state.

RESULTS:
The two populations were well matched on baseline demographic characteristics. There was no difference in the gun-related fatality rate between the intervention and control groups (20.1 per 100,000 in the intervention group and 20.2 per 100,000 in the control group; P=0.98) based on an intention to treat analysis. There was considerable cross-over between groups and this potentially explains the failure of the intervention to produce the intended result. In subjects who crossed over from the intervention to the control group (hereafter called "criminals"), the odds of gun-related violence increased 1000.42 (p=0.00001). Many criminals were responsible for more than one gun-related death and crossed over multiple times from intervention to control. There was wide variability between the rates of gun related violence on the basis of geography and other factors, with fatality rates 10-100 times higher in Baltimore, MD than in Provo, UT.

CONCLUSIONS:
An intervention to reduce gun-related violence failed to achieve this goal, largely as a result of cross-over from the intervention to the control group by "criminals". These criminals undermined the efficacy of the intervention. Moreover, the high geographic variability in gun related violence suggests that factors unrelated to the availability of firearms may drive gun-related violence rates. Future studies in limiting gun-related violence should focus on at-risk groups identified through crime statistics, and should not be NIH funded. Moreover, recrudescent crossover in future studies should be limited by incarceration of criminals for life without parole. Future studies might also focus on more traditional ways of preventing recrudescent cross-over (such as capital punishment). The Personalized Healthcare movement might also provide guidance on how to deal with this challenging problem.

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Autism, Vaccines, and The Tragedy of the Commons: Whose Tragedy and Whose Commons?

In last week's NEJM, there is an article about the purported perils of foregoing vaccinations for your kids. The article is here: http://content.nejm.org/cgi/content/full/360/19/1981 .

There are a few points that I think deserve to be made about this issue. First, I digress to outline briefly the idea of "The Tragedy of the Commons."

The Tragedy of the Commons refers to the notion that "commons" such as parks or more traditionally "grazing areas" will be more fruitfully enjoyed by all if they are used responsibly. If everybody grazes as many sheep as s/he pleases on the commons, soon enough, there will be no grass for the sheep to eat. So it stands to reason that one should graze his sheep responsibly and sparingly on the commons. Paradoxically, there is little incentive to exercise such restraint. Because insomuch as you do, your neighbor does not, and the sparing of the commons effected by you is obliterated by your neighbor, or his neighbor, etc. As when passing a sign enjoining you to not walk on the grass and you are want to say "ah, but what difference will it make?", your neighbor might respond "yeah, but if we all did that....". The sign is there to regulate the commons that would be depradated were it not for some social policy forcing restraint. So long as the MAJORITY refrains from treading on the lush monocultured turf, it will remain lush. But after a certain threshold number of defectors trammels it, the commons is lost.

And such, I will demonstrate, is the issue with refusing vaccinations. The threat that results is not so much to the unvaccinated child, but rather to the commons - to the herd immunity. So far, it seems to me, the medical and public health establishments have sought to appeal to the sensitivities of parents to their own children's welfare rather than to supplicate them to "do what's right for society." To me, this is a overtly disingenuous approach. The vaccination of any indivudual child, when the baseline vaccination rate is above some critical threshold is an act of social responsibility much more than it is something essential for the health of the individual child. I suspect that some vaccine-refusing parents (let's call them Refusniks, shall we?) recognize this, and this recognition, combined with a tendency for rebellion, creates an impetus for refusal, especially if they think that the vaccine may cause autism or some other untoward effect. Let's look at some numbers.

First let's start with an estimate of the incidence of Measles with and without vaccination (if you take issue with these estimates and the resulting conclusions, please furnish your own numbers with a reference):

Measles with vaccination:
0.0000010000000 per annum
Measles without vaccination:
0.0002500000000

Even though this is a 250x increase, it is still only an absolute increase of:
0.0002490000000

So, if you fail to vaccinate your child, you increase his/her risk of measles by only 0.024%.

But the case fataility rate for measles is only about 0.3%. So, you increase your child's risk of death from measles by only:
0.0000004230000

That's a very small number, my friends.

Now let's also say that you're concerned about the risk of autism, for whatever reason, even a specious one. And you ask your pediatrician who is skeptical, so s/he refers you to the most recent good quality epidemiological data, the Danish data from NEJM in 2002: http://content.nejm.org/cgi/content/abstract/347/19/1477 .

In this study, the upper 95% CI for an association of MMR with Autism was 1.24. Thus, a 24% increase in the risk of autism is certainly within the range of plausibility based on these data. The base rate of autism in this study was:

Base rate of autism:
0.0005880000000
Rate of autism with a 24% increase (assuming it may be as hight as the UCI):
0.0007290000000
Absolute increase in autism rate:
0.0001410000000

Now, I realise that autism may not be as bad as death for a child, but this POTENTIAL increase in autism, consistent with good data, far overshadows the risk of death from Measles attributable to failure to vaccinate your child.

So it stands to reason that, if a person has, for whatever reasons, a value system that makes autism a grave concern for them, they are NOT acting terribly far outside the bounds of rationality by refusing vaccination for their individual child.

Now if their child has siblings, and/or they live in a community where there is a high rate of vaccination refusal, these numbers are out the window and the individual child risk is much harder to calculate and probably much higher.

(I recognize also that I have used data on the ANNUAL measles risk which may be cumulative and this may sway the numbers in favor of vaccination since presumably the risk of autism from vaccine exposure is a one-time event.)

I do not mean to imply here that I am against vaccination (I am not), nor that I believe that autism is caused by MMR or other vaccines (I do not), but I think 4 points are germane to this conversation which may be emblematic of other issues in public health where officials are apt to take a paternalistic stance:

1.) The individual child's absolute risk of death from Measles is VERY small, as is the increase in risk from failure to be vaccinated.

2.) The risk of autism from MMR based on the Madsen data has a wide confidence interval which does not exclude what some parents may think is a meaningful increased risk of 24%. The meaningfulness of this risk may be especially important in the context of comparing it with another very small risk, such as that of death or diasbility from measles, or motor vehicle accidents.

3.) The refusal to vaccinate is more of a social responsibility issue, a Tragedy of the Commons, than it is an individual patient safety and health issue. (Such is also the case with PPDs, TB, and INH prophylaxis, but don't get me started on that.)

4.) The risks that parents take for their children through vaccination refusal is similar risks they take via motor vehicle travel. We are not encouraging parents to cut in half the number of miles they drive with their children per annum to reduce the risk of death from MVAs from 0.000145 to half of that, so why are we so adamant about their getting MMR? Because it's an issue of the commons, not the individual.

And if it is an issue of civic responsibilty, we should frame it as such, rather than guilt-tripping parents about exposing their children to risk via neglect. Just like driving a massive Ford Excursion, where your children may be safer but everybody else's are worse off (because of the size of your projectile or its impact on the environment), vaccination is better for the commons, if not for your own children.

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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.

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Judicial use of DNA "evidence" and Misuse of Statistics: The Prosecutor's Fallacy

A recent article in the NYT described the adoption by the judicial system of a technology that began as a biomedical research tool (I resist to some extent the notion that DNA technology has directly been a boon to clinical patient care.) (See: http://www.nytimes.com/2009/04/19/us/19DNA.html.) This powerful technology, when used appropriately in appropriate circumstances, provides damning evidence of guilt because of its high specificity - the probability of a coincidental match is stated to be as low as 1x10-9. Thus, in a case such as that of the infamous (and nefarious) OJ Sipmson, in which there is strong suspicion of guilt BEFORE the DNA evidence is evaluated, a positive match, in the absence of laboratory error or misconduct (neither of which can be routinely discounted - see: http://www.nytimes.com/2001/09/26/us/police-chemist-accused-of-shoddy-work-is-fired.html) essentially proves, beyond any reasonable doubt, the genetic identity of the person to whom the sample belongs. (Yes, that does indeed mean that OJ Simpson is the perpetrator of the heinous murder of Nicole Brown Simpson, he said unapologetically.)

In the case of old OJ, he was one among perhaps 10, let's say 100 suspects. Let's assume that the LAPD had their act together (this also requires a leap of faith) and that the perpetrator is among the suspects that have been rounded up, but we have no evidence to differentiate their respective probabilities of guilt. Thus, each of the 100 has a 1% probability of being guilty, on the basis of circumstantial evidence alone, or a relation to or relationship with the victim(s) or just being in the wrong place at the wrong time, whatever. Given that 1% probability of guilt, we can make a 2x2 table representing the the probability of guilt given a positive test, which is ultimately what we want to know. I don't know the sensitivity of DNA fingerprinting, but it doesn't really matter because the high specificity of the test drives the likelihood ratio. I will assume it's 50% for simplicity:


In this "population" of 100 suspects (by suspects, I mean persons whose probability of having committed the crime is enhanced over that of a random member of the overall population by virtue of other evidence), even if all 100 suspects have equiprobable guilt, a DNA "match" is damning indeed and all but assures the guilt of the matching suspect (with the caveats mentioned above.)

But consider a different situation, one in which there are no convincing suspects. Suppose that the law enforcement authorities compare a biological sample with a large DNA database to look for a match. Note that we do not use the term "suspect" here - because it implies that there is some suspicion that has limited this population from the overall population. When a database (of unsuspected persons) is canvassed, no such suspicion exists. Rather, a fishing expedition ensues, and the probabilities, when computed, come out quite different. Suppose there are DNA samples from 100 million individuals in the database, and the entire database is canvassed. Now our 2x2 table looks like this:


Whereas in our previous example of a population of "suspects" guilt was all but assured based on a "match", in this example of canvassing a database, guilt is dubious. But what do you suppose will happen in such an investigation? Who will suspend his judgment and conduct a fair investigation of this "matching" individual, who is now a "suspect" based only on "evidence" from this misused test? How tempting will it be for detectives to selectively gather information and see reality through the distorted lens of the "infallible" DNA testing? How can such a person hope to exonerate himself?

This is the Prosecutor's Fallacy. It bolsters arguments by the ACLU and others that the trend of snowballing DNA sample collection should be curtailed, and that limits should be placed on canvassing efforts to solve crimes.

One way to limit the impact of the Prosecutor's Fallacy and false positive "matches" from canvassing efforts would be to force investigators to assign certain profiles to the imaginary "suspect" whom they hope to find in the database and to canvas a subgroup of the database that matches those characteristics. For example, if the crime occurred in Seattle, the canvassing effort could be limited to a subset of the database that lived in or near Seattle, since it is unlikely that a person in Baltimore committed the crime. Other characteristics that are probabilistically associated with certain crimes could be used to limit broad canvassing efforts.

As the use of medical technology expands both inside and outside medicine, we have a responsibility to utilize it wisely and rationally. The strategy of database screening and canvassing is reckless, unwise, and unjust, and should be summarily and duly curtailed.

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The PSA Screening Quagmire - If Ignorance is Bliss then 'Tis Folly to be Wise?

The March 26th NEJM was a veritable treasure trove of interesting evidence so I can't stop after praising NICE-SUGAR and railing on intensive insulin therapy. If 6000 patients (40,000 screened) seemed like a commendable and daunting study to conduct, consider that the PLCO Project Team randomized over 76,000 US men to screening versus control (http://content.nejm.org/cgi/reprint/360/13/1310.pdf) and the ERSPC Investigators randomized over 162,000 European men in a "real-time meta-analysis" of sorts (wherein multiple simultaneous studies were conducted with similar but different enrollment requirements and combined; see: http://content.nejm.org/cgi/reprint/360/13/1320.pdf.)   This is, as the editorialist points out a "Hurculean effort" and that is fitting and poignant - because ongoing PSA screening efforts in current clinical practice represent a Hurculean effort to reduce morbidity and mortality of this disease and this reinforces the importance of the research question - are we wasting our time? Are we doing more harm than good?

The lay press was quick to start trumpeting the downfall of PSA screening with headlines such as "Prostate Test Found to Save Few Lives" . But for all their might, both of these studies give me, a longtime critic of cancer screening efforts, a good bit of pause. (Pulmonologists may be prone to "sour grapes" as a result of the failures of screening for lung cancer.)

Before I summarize briefly the studies and point out some interesting aspects of each, allow me to indulge in a few asides. First, I direct you to this interesting article in Medical Decision Making "Cure Me Even if it Kills Me". This wonderful study in judgment and decision making shows how difficult it is for patients to live with the knowledge that there is a cancer, however small growing in them. They want it out. And they want it out even if they are demonstrably worse off with it cut out or x-rayed out or whatever. It turns out that patients have a value for "getting rid of it" that probably arises from the emotional costs of living knowing there's a cancer in you. I highly recommend that anyone interested in cancer screening or treatment read this article.

This article invokes in me an unforgettable patient from my residency whom we screened in compliance with VA mandates at the time. Sure enough, this patient with heart disease had a mildly elevated PSA and sure enough he had a cancer on biopsy. And we discussed treatments in concert with our Urology colleagues. While he had many options, this patient agonized and brooded and could not live with the thought of a cancer in him He proceeded with radical prostatectomy, the most drastic of his options. And I will never forget that look of crestfallen resignation every time I saw him after that surgery because he thereafter came to clinic in diapers, having been rendered incontinent and impotent by that surgery. He was more full of self-flagellating regret than any other patient I have seen in my career. This poor man and his experience certainly jaded me at a young age and made me highly attuned to the pitfalls of PSA screening.

Against this backdrop where cancer is the most feared diagnosis in medicine, we feel an urge towards action to screen and prevent, even when there is a marginal net benefit of cancer screening, and even when other greater opportunities for improving health exist. I need not go into the literature about [ir]rational risk appraisal other than to say that our overly-exuberant fear of cancer (relative to other concerns) almost certainly leads to unrealistic hopes for screening and prevention. Hence the great interest in and attention to these two studies.

In summary, the PLCO study showed no reduction in prostate-cancer-related mortality from DRE (digital rectal examination) and PSA screening. Absence of evidence is not evidence, however, and a few points about this study deserve to be made:

~Because of high (and increasing) screening rates in the control group, this was essentially a study of the "dose" of screening. The dose in the control group was ~45 and that in the screening group was ~85%. So the question that the study asked was not really "does screening work" but rather "does doubling the dose of screening work". Had there been a favorable trend in this study, I would have been tempted to double the effect size of the screening to infer the true effect, reasoning that if increasing screening from 40% to 80% reduces prostate cancer mortality by x%, then increasing screening from 0% to 80% would reduce it by 2x%. Alas this was not the case with this study which was underpowered.

~I am very wary of studies that have cause-specific mortality as an endpoint. There's just too much room for adjudication bias, as the editorialist points out. Moreover, if you reduce prostate cancer mortality but overall mortality is unchanged, what do I, as a potential patient care? Great, you saved me from prostate cancer and I died at about the same time I would have but from an MI or a CVA instead? We have to be careful about whether our goals are good ones - the goal should not be to "fight cancer" but rather to "improve overall health". The latter, I admit, is a much less enticing and invigorating banner. We like to feel like we're fighting. (Admittedly, overall mortality appears to not differ in this study, but I'm at a loss as to what's really being reported in Table 4.) The DSMB for the ESRCP trial argue here that cancer specific mortality is most appropriate for screening trials because of dilution by other causes of mortality, and because screening for a specific cancer can only be expected to reduce mortality for that cancer. From an efficacy standpoint, I agree, but from an effectiveness standpoint, this position causes me to squint and tilt my head askance.

~It is so very interesting that this study was stopped not for futility, nor for harm, nor for efficacy, but because it was deemed necessary for the data to be released because of the [potential] impact on public health. And what has been the impact of those data? Utter confusion. That increasing screening from 40% to 80% does not improve prostate specific mortality does not say to me that we should reduce screening to 0%. In fact I don't know what to do, nor what to make of these data. Especially in the context of the next study.

In the ERSPC trial, investigators found a 20% reduction in prostate cancer deaths with screening with PSA alone in Europe. The same caveats regarding adjudication of this outcome notwithstanding, there are some very curious aspects of this trial that merit attention:

~This trial was, as I stated above, a "real-time meta-analysis" with many slightly different studies combined for analysis. I don't know what this does to internal or external validity because this is such an unfamiliar approach to me, but I'll be pondering it for a while I'm sure.

~I am concerned that I don't fully understand the way that interim analyses were performed in this trial, what the early stopping rules were, and whether a one-sided or two-sided alpha was used. Reference 6 states that it was one-sided but the index article says 2. Someone will have to help me out with the O'Brien-Fleming alpha spending function and let me know if 1% spending at each analysis is par for the course.

~As noted by the editorialist, we are not told what the "contamination rate" of screening in the control group is. If it is high, we might use my method described above to infer the actual impact of screening.

~Look at the survival curves that diverge and then appear to converge again at a low hazard rate. Is it any wonder that there is no impact on overall mortality?


So where does this all leave us? We have a population of physicians and patients that yearn for effective screening and believe in it, so much so that it is hard to conduct an uncontaminated study of screening. We have a US study that is stopped prematurely in order to inform public health, but which is inadequate to inform it. We have a European study which shows a benefit near the a priori expected benefit, but which has a bizarre design and is missing important data that we would like to consider before accepting the results. We have no hint of a benefit on overall mortality. We have lukewarm conclusions from both groups, and want desperately to know what the associated morbidities in each group are. We are spending vast amounts of resources and incurring an enormous emotional toll on men who live in fear after a positive PSA test, many of whom pay dearly ("a pound of flesh") to exorcise that fear. And we have a public over-reaction to the results of these studies which merely increase our quandary.

If ignorance is bliss, then truly 'tis folly to be wise. Perhaps this saying applies equally to individual patients, and the investigation of PSA screening in these large-scale trials. For my own part, this is one aspect of my health that I shall leave to fate and destiny, while I focus on more directly remediable aspects of preventive health, ones where the prevention is pleasurable (running and enjoying a Mediterranean diet) rather than painful (prostatectomy).

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Another [the final?] nail in the coffin of intensive insulin therapy (Leuven Protocol) - and redoubled scrutiny of single center studies

In the March 26th edition of the NEJM, the NICE-SUGAR study investigators publish the results of yet another study of intensive insulin therapy in critically ill patients: http://content.nejm.org/cgi/content/abstract/360/13/1283 .

This article is of great interest to critical care practitioners because intensive insulin therapy (Leuven Protocol) or some diluted or half-hearted version of it has become a de facto standard of care in ICUs across the nation and indeed worldwide; and because it is an incredibly well-designed and well-conducted study. My own interest derives also from my own [prescient] letter to the editor of the NEJM after the second Van den Berghe study (http://content.nejm.org/cgi/content/extract/354/19/2069 , the criticisms I levied against this therapy on this blog after another follow-up study recently showed negative results (http://medicalevidence.blogspot.com/2008/01/jumping-gun-with-intensive-insulin.html ), and in a recent paper railing against the "normalization heuristic" (http://www.medical-hypotheses.com/article/S0306-9877(09)00033-4/abstract ). The results of this study also add to the growing evidence that intensive control of hyperglycemia in other settings may not be beneficial (see the ACCORD and ADVANCE studies.)

The current study was designed to largely mirror the enrollment criteria and outcome definitions of the previous studies, had excellent follow-up, had well described and simple statistical analyses with ample power, and is well reported. Key differences between it and the original Van den Berghe study were the lack of high-calorie parenteral glucose infusions, and its multicenter design. This latter characteristic may be pivotal in understanding why the initially promising Leuven Protocol results have not panned out on subsequent study.

The results of this study can be summarized simply by saying that it appears that this therapy is of NO benefit and actually probably kills patients, in addition to markedly increasing the rate of very very severe hypoglycemia (6.3% increase, P<0.001). In contrast to Van den Berghe's second study in medical patients, there were no favorable trends towards reduction in ICU length of stay, time on the ventilator, or reduced organ failures. In short, this therapy appears to be a complete flop.

So why the difference? Why did this therapy, which in 2001 appeared to have such promise that it enjoyed rapid and widespread [and premature] adoption fail to withstand the basic test of science, namely, repeatability? I think that medical history will judge two factors to be responsible. Firstly, the massive dextrose infusions in the first study markedly jeporadized the external validity of the first (positive) Van den Berghe study - it's not that intensive insulin saves you from your illness, it saves you from the harmful caloric infusions used in the surgical patients in the first study.

Secondly, and this is related to the first, single center studies also compromise external validity. In a single center, local practice patterns may be uniform and idiosyncratic, so that the benefit of any therapy tested in such a center may also be idiosyncratic. Moreover, and I dare say, investigators at a single center may have more decisional latitude and control or influence over enrollment, ascentainment of outcomes, and clinical care of enrolled patients. The so-called "trial effect" whereby patients enrolled in a trial receive superior care and have superior outcomes may be more likely in single center studies. Such effects are of increased concern in trials whre total blinding/masking or treatment assignment is not possible. (Recall that in the Van den Berghe study, kan endocrinologist was consulted for insulin adjustments; in the current trial, a computerized algorithm controlled the adjustments.) Moreover still, for single center studies, investigators and the instutution itself may have more "riding on" the outcome of the study, and collective equipoise may not exist. As an "analogy of extremes", just for illustrative purposes, if you wanted to design a trial where you could subversively influence outcomes in a way that would not be apparent from the outside, would you design a single center study (at your own institution where your cronies were) or a large multicenter, multinational study? Which design would allow you to have more influence?

I LOVE the authors' concluding statement that "a clinical trial targeting a perceived risk factor is a test of a complex strategy that may have profound effects beyond its effect on the risk factor." This resonates beautifully with our conceptualization of the "normalization heuristic" and harkens to Ben Franklin's sage old saw that "He is the best physician who knows the worthlessness of the most medicines." I think that we now have more than ample data to assure us that intensive insulin therapy (i.e., targeting a blood sugar of 80-108) is a worthless medicine, and should be largely if not wholly abandoned.

Addendum 4/7/09: Also note the scrutiny of the only other "positive" study (with mortality as the primary endpoint) in critical care in the last decade: Rivers et al; see: http://online.wsj.com/article/SB121867179036438865.html .

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"Statistical Slop": What billiards can teach us about multiple comparisons and the need to assign primary endpoints

Anyone who has played pool knows that you have to call your shots before you make them. This rule is intended to decrease probability of "getting lucky" from just hitting the cue ball as hard as you can, expecting that the more it bounces around the table, the more likely it is that one of your many balls will fall through chance alone. Sinking a ball without first calling it is referred to coloquially as "slop" or a "slop shot".

The underlying logic is that you know best which shot you're MOST likely to successfully make, so not only does that increase the prior probability of a skilled versus a lucky shot (especially if it is a complex shot, such as one "off the rail"), but also it effectively reduces the number of chances the cue ball has to sink one of your balls without you losing your turn. It reduces those multiple chances to one single chance.

Likewise, a clinical trialist must focus on one "primary outcome" for two reasons: 1.) because preliminary data, if available, background knowledge, and logic will allow him to select the variable with the highest "pre-test probability" of causing the null hypothesis to be rejected, meaning that the post-test probability of the alternative hypothesis is enhanced; and 2.) because it reduces the probaility to find "significant" associations among multiple variables through chance alone. Today I came across a cute little experiment that drives this point home quite well. The abstract can be found here on pubmed: http://www.ncbi.nlm.nih.gov/pubmed/16895820?ordinalpos=4&itool=EntrezSystem2.PEntrez.Pubmed.Pubmed_ResultsPanel.Pubmed_DefaultReportPanel.Pubmed_RVDocSum .


In it, the authors describe "dredging" a Canadian database and looking for correlations between astrological signs and various diagnoses. Significant associations were found between the Leo sign and gastrointestinal hemorrhage, and the Saggitarius sign and humerous fracture. With this "analogy of extremes" as I like to call them, you can clearly see how the failure to define a prospective primary endpoint can lead to statistical slop. (Nobody would have been able to predict a priori that it would be THOSE two diagnoses associated with THOSE two signs!) Failure to PROSPECTIVELY identify ONE primary endpoint led to multiple chances for chance associations. Moreover, because there were no preliminary data upon which to base a primary hypothesis, the prior probability of any given alternative hypothesis is markedly reduced, and thus the posterior probability of the alternative hypothesis remains low IN SPITE OF the statistically significant result.

It is for this very reason that "positive" or significant associations among non-primary endpoint variables in clinical trials are considered "hypothesis generating" rather than hypothesis confirming. Requiring additional studies of these associations as primary endpoints is like telling your slop shot partner in the pool hall "that's great, but I need to see you do that double rail shot again to believe that it's skill rather than luck."

Reproducibility of results is indeed the hallmark of good science.

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PCI versus CABG - Superiority is in the heart of the angina sufferer

In the current issue of the NEJM, Serruys et al describe the results of a multicenter RCT comparing PCI with CABG for severe coronary artery disease: http://content.nejm.org/cgi/content/full/360/10/961. The trial, which was designed by the [profiteering] makers of drug-coated stents, was a non-inferiority trial intended to show the non-inferiority (NOT the equivalence) of PCI (new treatment) to CABG (standard treatment). Alas, the authors appear to misunderstand the design and reporting of non-inferiority trials, and mistakenly declare CABG as superior to PCI as a result of this study. This error will be the subject of a forthcoming letter to the editor of the NEJM.

The findings of the study can be summarized as follows: compared to PCI, CABG led to a 5.6% reduction in the combined endpoint of death from any cause, stroke, myocardial infarction, or repeat vascularization (P=0.002). The caveats regarding non-inferiority trials notwithstanding, there are other reasons to call into question the interpretation that CABG is superior to PCI, and I will enumerate some of these below.

1.) The study used a ONE-SIDED 95% confidence interval - shame, shame, shame. See: http://jama.ama-assn.org/cgi/content/abstract/295/10/1152 .
2.) Table 1 is conspicuous for the absence of cost data. The post-procedural hospital stay was 6 days longer for CABG than PCI, and the procedural time was twice as long - both highly statistically and clinically significant. I recognize that it would be somewhat specious to provide means for cost because it was a multinational study and there would likely be substantial dispersion of cost among countries, but it seems like neglecting the data altogether is a glaring omission of a very important variable if we are to rationally compare these two procedures.
3.) Numbers needed to treat are mentioned in the text for variables such as death and myocardial infarction that were not individually statistically significant. This is misleading. The significance of the composite endpoint does not allow one to infer that the individual components are significant (they were not) and I don't think it's conventional to report NNTs for non-significant outcomes.
4.) Table 2 lists significant deficencies and discrepancies between pharmocological medical management at discharge which are inadequately explained as mentioned by the editorialist.
5.) Table 2 also demonstrates a five-fold increase in amiodarone use and a three-fold increase in warfarin use at discharge among patients in the CABG group. I infer this to represent an increase in the rate of atrial fibrillation in the CABG patients, but because the rates are not reported, I am kept wondering.
6.) Neurocognitive functioning and the incidence of defecits (if measured), known complications of bypass, are not reported.
7.) It is mentioned in the discussion that after consent, more patients randomized to CABG compared to PCI withdrew consent, a tacit admission of the wariness of patients to submit to this more invasive procedure.

In all, what this trial does for me is to remind me to be wary of an overly-simplistic interpretation of complex data and a tendency toward dichotimous thinking - superior versus inferior, good versus bad, etc.

One interpretation of the data is that a 3.4 hour bypass surgery and 9 days in the hospital !MIGHT! save you from an extra 1.7 hour PCI and another 3 days in the hospital on top of your initial committment of 1.7 hours of PCI and 3 days in the hospital if you wind up requiring revascularization, the primary [only] driver of the composite endpoint. And in payment for this dubiously useful exchange, you must submit to a ~2% increase in the risk of stroke, have a cracked chest, risk surgical wound infection (rate of which is also not reported) pay an unknown (but probably large) increased financial cost, risk some probably large increased risk of atrial fibrillation and therefore be discharged on amiodarone and coumadin with their high rates of side effects and drug-drug interactions, while coincidentally risk being discharged on inadequate medical pharmacological management.

Looked at from this perspective, one sees that beauty is truly in the eye of the beholder.

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Money talks and Chantix (varenicline) walks - the role of financial incentives in inducing healthful behavior

I usually try to keep the posts current, but I missed a WONDERFUL article a few weeks ago in the NEJM, one that is pivotal in its own right, but especially in the context of good decision making about therapeutic choices and opportunity costs.

The article, by Volpp et all entitled: A Randomized, Controlled Trial of Financial Incentives for Smoking Cessation can be found here: http://content.nejm.org/cgi/content/abstract/360/7/699
In summary, smokers at a large US company, where a smoking cessation program existed before the research began were randomized to receive additional information about the program, versus the same information plus a financial incentive of up to $750 for successfully stopping smoking. At 9-12 months, smoking cessation was 10% higher in the financial incentive group (14.7% vs. 5.0%, P<0.001).

In the 2006 JAMA article on varenicline (Chantix) by Gonzales et al (http://jama.ama-assn.org/cgi/reprint/296/1/47.pdf ), the cessation rates at weeks 9-52 were 8.4% for placebo and 21.9% for varenicline, an absolute gain of 13.5%. (Similar results were reported in the study by Jorenby et al: http://jama.ama-assn.org/cgi/content/abstract/296/1/56?maxtoshow=&HITS=10&hits=10&RESULTFORMAT=&fulltext=varenicline&searchid=1&FIRSTINDEX=0&resourcetype=HWCIT ) Now, given that this branded pharmaceutical sells for ~$120 for a 30 day supply, and that, based on the article by Tonstad (http://jama.ama-assn.org/cgi/reprint/296/1/64.pdf ), many patients are continued on varenicline for 24 weeks or more, the cost of a course of treatment with the drug is approximately $720, just about the same as the financial incentives used in the index article.

And all of this begs the question: Is it better to pay $750 for 6 months of treatment with a drug that has [potentially serious] side effects to achieve ~13% reduction in smoking, or to pay patients to quit smoking to achieve a 10% reduction in smoking without harmful side effects and in fact with POSITIVE side effects (money to spend on pleasurable alternatives to smoking or other necessities)?

The choice is clear to me, and, having failed Chantix, I now consider whether I should offer my brother payment to quit smoking. (I expect to receive a call as soon as he reads this, especially since I haven't mentioned the cotinine tests yet.)

And all of this begs the more important question of why we seek drugs to solve behavioral problems, when good old fashioned greenbacks will do the trick just fine. Why bother with Meridia and Rimonabant and all the other weight loss drugs when we might be able to pay people to lose weight? (See: http://jama.ama-assn.org/cgi/content/abstract/300/22/2631 .) Perhaps one part of Obama's stimulus bill can allocate funds to additional such an experiments, or better yet, to such a social program.

One answer to this question is that the financial incentive to study financial incentives is not as great as the financial incentive to find another profitable pill to treat social ills. (There is after all a "pipeline deficiency" in a number of Big Pharma companies that has led to several mergers and proposed mergers, such as the announcement today of a possible merger of MRK and SGP, two of my personal favorites.) Yet this study sets the stage for more such research. If we are going to pay one way or another, I for one would rather that we be paying people to volitionally change their behavior, rather than paying via third party to reinforce the notion that there is "a pill for everything". As Ben Franklin said, "S/He is the best physician who knows the worthlessness of the most medicines."

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The Normailzation Heuristic: how an untested hypothesis may misguide medical decisions

Here is an article that may be of interest written by two perspicacious young fellows:
http://www.sciencedirect.com/science?_ob=ArticleURL&_udi=B6WN2-4VP175C-1&_user=10&_rdoc=1&_fmt=&_orig=search&_sort=d&view=c&_acct=C000050221&_version=1&_urlVersion=0&_userid=10&md5=0067dfb6094ecc27303ccd6939257200


In this article, we describe how the general clinical hypothesis that "normalizing" abnormal laboratory values and physiological parameters will improve patient outcomes is unreliably accurate, and use historical examples of practices such as hormone replacement therapy, and the CAST trial to buttress this argument. We further suggest that many ongoing practices that rely on normalizing values should be called into question because the normalization hypothesis is a fragile one. We also operationally define the "normalization heuristic" and define four general ways in which it can fail clinical decision makers. Lastly, we make suggestions for empirical testing of existence of this heuristic and caution clinicians and medical educators to be wary of reliance on the normalization hypothesis and the normalization heuristic. This paper is an expansion of the idea of the normalization heuristic that was mentioned previously on this blog.

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West's estimations of PaO2 on Everest Confirmed - but SaO2 remains an estimation

Recently, Grocott et al published results of an intriguing study in which they drew blood gas samples from climbers near the summit of everest and analyzed them at one of the high camps with a modified blood gas analyzer. (See: http://content.nejm.org/cgi/content/abstract/360/2/140 ) This is no small feat, and the perhaps shocking results confirm earlier estimations of low arterial oxygen tension derived from samples of exhaled gas. The PaO2 of these climbers is often under 30mmHg - a difficult to believe number for clinicians who are accustomed to a danger zone represented by much higher numbers in clinical practice.

As intriguing as the numbers may be, the authors have made a crucial assumption in the estimation of arterial oxygen saturation (SaO2) that leads us to be circumspect about the accuracy of this estimated value. A letter written by me and my colleagues emphasizing several caveats in these estimations was not accepted for publication by the NEJM so I will post it below.

In the article by Grocott et al, an important limitation of using calculated SaO2 values for the estimation of arterial oxygen content is neglected. The equation used for the calculation of SaO2 in the article does not take into account changes in hemoglobin affinity induced by increased 2,3-DPG levels which are known to occur during acclimatization (1;2). Errors resulting from these estimations will be magnified for values of PaO2 on the steep portion of the oxyhemoglobin dissociation curve. The PaO2 values of the subjects studied are on this portion of the curve. Can the authors comment on 2,3-DPG levels in these climbers and how any resulting changes in hemoglobin affinity may have affected calculated values? Were the climbers taking acetazolamide, which has variably been demonstrated to affect the oxygen affinity of hemoglobin (3;4)? Is there any evidence that acclimatization induces increased production of fetal hemoglobin as occurs in some other species (5)? Because of such caveats and possibly other unknown variables, co-oximetry remains the gold standard for determination of arterial oxygen saturation.


Reference List

(1) Wagner PD, Wagner HE, Groves BM, Cymerman A, Houston CS. Hemoglobin P(50) during a simulated ascent of Mt. Everest, Operation Everest II. High Alt Med Biol 2007; 8(1):32-42.
(2) Winslow RM, Samaja M, West JB. Red cell function at extreme altitude on Mount Everest. J Appl Physiol 1984; 56(1):109-116.
(3) Gai X, Taki K, Kato H, Nagaishi H. Regulation of hemoglobin affinity for oxygen by carbonic anhydrase. J Lab Clin Med 2003; 142(6):414-420.
(4) Milles JJ, Chesner IM, Oldfield S, Bradwell AR. Effect of acetazolamide on blood gases and 2,3 DPG during ascent and acclimatization to high altitude. Postgrad Med J 1987; 63(737):183-184.
(5) Reynafarje C, Faura J, Villavicencio D, Curaca A, Reynafarje B, Oyola L et al. Oxygen transport of hemoglobin in high-altitude animals (Camelidae). J Appl Physiol 1975; 38(5):806-810.


Scott K Aberegg, MD, MPH
Leroy Essig, MD
Andrew Twehues, MD

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More Data on Dexmedetomidine - moving in the direction of a new standard

A follow-up study of dexmedetomidine (see previous blog: http://medicalevidence.blogspot.com/2007/12/dexmedetomidine-new-standard-in_16.html )
was published in last week's JAMA (http://jama.ama-assn.org/cgi/content/abstract/301/5/489 ) and hopefully serves as a prelude to future studies of this agent and indeed all studies in critical care. The recent study addresses one of my biggest concerns of the previous one, namely that routine interruptions of sedatives were not employed.

Ironically, it may be this difference between the studies that led to the failure to show a difference in the primary endpoint in the current study. The primary endpoint, namely the percentage of time within the target RASS, was presumably chosen not only on the basis of its pragmatic utility, but also because it was one of the most statistically significant differences found among secondary analyses in the previous study (percent of patients with a RASS [Richmond Agitation and Sedation Scale] score within one point of the physician goal; 67% versus 55%, p=0.008). It is possible, and I reason likely, that daily interruptions in the current study obliterated that difference which was found in the previous study.


But that failure does not undermine the usefulness of the current study which showed that sedation comparable to routinely used benzos can be achieved with dexmed, probably with less delirium, and perhaps with shorter time on the ventilator and fewer infections. What I would like to see now, and what is probably in the works, is a study of dexmed which shows shorter time on the ventilator and/or reductions in nosocomial infections as primary study endpoints.

But to show endpoints such as these, we are going to need to carefully standardize our ascertainment of infections (difficult to say the least) and also to standardize our approach to discontinuation of mechanical ventilation. In regard to the latter, I propose that we challenge some of our current assumptions about liberation from mechanical ventilation - namely, that a patient must be fully awake and following commands prior to extubation. I think that a status quo bias is at work here. We have many a patient with delirium in the ICU who is not already intubated and we do not intubate them for delirium alone. Why, then, should we fail to extubate a patient in whom all indicators show reaolution of critical illness, but who remains delirious? Is it possible that this is the main player in the causal pathway between sedation and extubation and perhaps even nosocomial infections and mortality? (The protocols or lack thereof for assessing extubation readiness were not described in the current study, unless I missed them.) It would certainly be interesting and perhaps mandatory to know the extubation practices in the centers involved in this study, especially if we are going to take great stock in this secondary outcome of this study.

Another thing I am interested in knowing is what PATIENT experiences are like in each group - whether there is greater recall or other differences in psychological outcomes between patients who receive different sedatives during their ICU experience.

I hope this study and others like it serve as a wake-up call to the critical care research community which has heretofore been brainwashed into thinking that a therapy is only worthwhile if it improves mortality, a feat that is difficult to achieve not only because it is often unrealistic and because absurd power calculations and delta inflation run rampant in trial design, but because of limitations in funding and logistical difficulties. This group has shown us repeatedly that useful therapies in critical care need not be predicated upon a mortality reduction. It's past time to start buying some stock in shorter times on the blower and in the ICU.

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Cost: The neglected adverse event / side effect in trials of for-profit pharmaceuticals and devices

Amid press releases and conference calls today pertaining to the release of data on two trials of the investigational drug pirfenidone, one analyst's comments struck me as subtly profound. She was saying that in spite of conflicting data on and uncertainty about the efficacy of the drug (in the Capacity 1 and Capacity 2 trials - percent change in FVC [forced vital CAPACITY] at 72 weeks was the primary endpoint of the study) IPF is a deadly and desperate disease for which no effective treatments exist (save for lung transplantations if you're willing to consider that an effective treatment) and therefore any treatment with any positive effect however small and however uncertain should be given ample consideration, especially given the relative absense of side effects of pirfenidone in the Capacity trials.

And I thought to myself - "absense of side effects?" Here we have a drug that, over the course of about 1.5 years reduces the decline in FVC by about 60ccs (maybe - it did so in Capacity 2 but not in Capacity 1) but does not prolong survival or dyspnea scores or any other outcome that a patient may notice. So, I'm picturing an IPF patient traipsing off to the drugstore to purchase pirfenidone, a branded drug, and I'm imagining that the cash outlay might be perceived by such a patient as an adverse event, a side effect of sorts of using this questionably effective drug to prevent an intangible decline in FVC. The analyst's argument distilled to: "why not, there's no drawback to using it and there are no alternatives", but this utterly neglected the financial hardships that many patients endure when taking expensive branded drugs and ignored alternative ways that patients with IPF may spend their income to benefit their health or general well-being.

This perspective is even more poignant when we consider the cases of "me-too" drugs that add marginally to the benefits or side effect profiles of existing drugs, and which are often approved on the basis of a trial comparing them to placebo rather than existing generic alternatives. One of the last posts on this blog detailed the case of Aliskiren, and I am reminded of the trial of Tiotropium published in the NEJM in October, among many other entire classes of drugs such as the proton pump inhibitors, antidepressants, antihistamines, inhaled corticosteroids, antihypertensives, ACE-inhibitors for congestive heart failure, and the list goes on.

Given todays economy, soaring healthcare costs, and increasing financial burdens and co-pays shouldered by patients especially those of limited economic means or those hit hardest by economic downturns, we can no longer afford (pun intended) to ignore the financial costs of "me too" medications as adverse events of the use of these drugs when cheaper alternatives exist.

In terms of trial design, we should demand that new agents be compared to existing alternatives when those exist, and we need to develop a system for evaluating the results of a trial that does not neglect the full range of adverse effects experienced by patients as a result of using expensive branded drugs. Marginally "better" is not better at all if it costs ridiculously more, and the uncertainty relating to the efficacy of a drug must be accounted for in terms of its value to patients, especially when costly.

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Who is John Galt?

Type your summary here

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"Off-Label Promotion By Proxy": How the NEJM and Clinical Trials are Used as an Advertising Apparatus. The Case of Aliskiren

In the print edition of the June 5th NEJM (mine is delivered almost a week early sometimes), readers will see on the front cover the lead article entitled "Aliskiren Combined with Losartan in Type 2 Diabetes and Nephropathy," and on the back cover a sexy advertisement for Tekturna (aliskiren), an approved antihypertensive agent, which features "mercury-man", presumably a former hypertensive patient metamorphized into elite biker (and perhaps superhero) by the marvels of Tekturna. Readers who lay the journal inside down while open may experience the same irony I did when they see the front cover lead article juxtaposed to the back cover advertisement.

The article describes how aliskiren, in the AVOID trial, reduced the mean urinary albumin-to-creatinine ratio as compared to losartan alone. There are several important issues here. First, if one wants to use a combination of agents, s/he can use losartan with a generic ACE-inhibitor (ACEi). A more equitable comparison would have pitted aliskiren plus losartan against [generic] ACEi plus losartan. The authors would retort of course that losartan alone is a recommended agent for the condition studied, but that is circular logic. If we were not in need of more aggressive therapy for this condition, then why study aliskiren in combination for it at all? If you want to study a new aggressive combination, it seems only fair to compare it to existing aggressive combinations.

Which brings me to another point - should aliskiren be used for ANY condition? No, it should not. It is a novel [branded] agent which is expensive, for which there is little experience, which may have important side effects which are only discovered after it is used in hundreds of thousands of patients, and more importantly, alternative effective agents exist which are far less costly adn for which more experience exist. A common error in decision making occurs when decision makers focus only on the agent or choice at hand and fail to consider the range of alternatives and how the agent under consideration fares when compared to the alternatives. Because aliskiren has only been shown to lower blood pressure, a surrogate endpoint, we would do well to stick with cheaper agents for which there are more data and more experience, and reserve use of aliskiren until a study shows a long-term mortality or meaningful morbidity benefit.

But here's the real rub - after an agent like this gets approved for one [common] indication (hypertension), the company is free to conduct little studies like this one, for off-label uses, to promote its sale [albeit indirectly] in patients who do not need it for its approved indication (BP lowering). And what better advertising to bring the drug into the sight of physicians than a lead article in the NEJM, with a complementary full page advertisement on the back cover? This subversive "off-label promotion by proxy", effected by study of off-label indications for which FDA approval may or may not ultimately be sought, has the immediate benefit of misleading the unwary who may increase prescriptions of this medication based on this study (which they are free to do) withouth considering the full range of alternatives.

My colleague David Majure, MD, MPH has commented to me about an equally insidious but perhaps more nefarious practice that he noticed may be occuring while attending this year's meeting of the American College of Cardiology (ACC). There, "investigtors" and corporate cronies are free to present massive amounts of non-peer reviewed data in the form of abstracts and presentations, much of which data will not and should not withstand peer review or which will be relegated to the obscurity of low-tier journals (where it likely belongs). But eager audience members, lulled by the presumed credibility of data presented at a national meeting of [company paid] experts will likely never see the data in peer-reviewed form, and instead will carry away the messages as delivered. "Drug XYZ was found to do 1-2-3 to [surrogate endpoint/off-label indication] ABC." By sheer force of repetition alone, these abstracts and presentations serve to increase product recognition, and, almost certainly, prescriptions. Whether the impact of the data presented is meaningful or not need not be considered, and probably cannot be considered without seeing the data in printed form - and this is just fine - for sales that is.

(Added 6/11/2008: this pre-publication changing of practice patterns has been described before - see http://jama.ama-assn.org/cgi/content/abstract/284/22/2886 .)

The novel mechanism of action of this agent and the scientific validity of the AVOID trial notwithstanding, the editorialship of the NEJM and the medical community should realize that science and the profit motive are inextricably interwoven when companies study these branded agents. The full page advertisement on the back cover of this week's NEJM was just too much for me.

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Prucalopride: When Delivery is so Suspicious that the Entire Message Seems Corrupt

In this week's NEJM, (http://content.nejm.org/cgi/content/short/358/22/2344) Camilleri (of the Mayo Clinic) and comrades from Movetis (a pharmaceutical company) report the results of a study of Prucalopride, a prokinetic agent, for the treatment of chronic constipation. What is striking about this study is not the agent's relation to Ciaspride (Propulsid, an agent removed from the market a number of years ago because of QTc prolongation and associated cardiac risk) but rather the fact that this study was completed nearly a decade ago, and was only just now published. Such a delay is certainly worthy of concern as astutely pointed out by an editorialist (http://content.nejm.org/cgi/content/short/358/22/2402).

A colleague and I recently pointed out the unethical practice of witholding the results of negative trials from the scientific community (see http://ccmjournal.com/pt/re/ccm/fulltext.00003246-200803000-00060.htm;jsessionid=L2bQSl9ygT9BzlZq81qlnJGfyfG2Jh2f2qQvP4XTp0YqMQ1ZD3T1!195308708!181195628!8091!-1?index=1&database=ppvovft&results=1&count=10&searchid=2&nav=search#P6), but the Prucalopride trial takes the cake. Here, positive results were either intentionally witheld from that community or by happenstance were omitted from publication, delaying further study of this agent (if it is indeed even warranted) and undermining the altruistic basis of subjects' participation in the trial, which, ostensibly, was to advance science (unless they participated for financial incentives, which I might argue [as others already have] should be disclosed in the reporting of a trial - see http://content.nejm.org/cgi/content/extract/358/22/2316.)

I will leave it to other bloggers and commentators to speculate whether the profit or other motives were the impetus behind this delay and whether medical ghostwriting was in any way involved in the publication of this article. Suffice it to say that there are certain irregularities in the way a trial is reported (in addition to those with which it was conducted) that should give us pause. Prucalopride has now shown itself to be worthy of a bright spotlight of intense scrutiny.

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Troponin Predicts Outcome in Heart Failure - But So What?

In today's NEJM, Peacock and others (http://content.nejm.org/cgi/content/short/358/20/2117 ) report that cardiac troponin is STATISTICALLY associated with hospital mortality in patients with acute decompensated heart failure, and that this association is independent of other predictive variables. Let us assume that we take the results for granted, and that this is an internally and externally valid study with little discernible bias.

In the first paragraph of the discussion, the authors state that "These results suggest that measurement of troponin adds important prognostic information to the initial evaluation of patients with acute decompensated heart failure and should be considered as part of an early assessment of risk."

Really?


The mortality in patients in the lowest quartile of troponin I was 2.0% and that in the highest quartile was 5.3%. If we make the common mistake of comparing things on a relative scale, this is in an impressive difference - in excess of a twofold increase in mortality. But that is like saying that I saved 50% off the price of a Hershey Kiss which costs 5 cents - so I saved 3 cents! As we approach zero, smaller and smaller absolute differences can appear impressive on a relative scale. But health should not be appraised that way. If you are "buying" something, be it health or some other commodity, you shouldn't care about your relative return on your investment, only the absolute return. You have after all, only some absolute quantity of money. Charlie (from the Chocolate Factory) may find 3 cents to be meaningful, but we are not here talking about getting a 3% reduction in mortality - we are talking about predicting for Charlie whether he will have to pay $0.05 for his kiss or $0.02 for it, and even if our prediction is accurate, we do not know how to help him get the discounted kiss - he's either lucky or he's not.

Imagine that you are a patient hospitalized for acute decompensated heart failure. Does it matter to you if your physician comes to you carrying triumphantly the results of your troponin I test and informs you that because it is low, your mortality is 2% rather than 5%? It probably matters very little. It matters even less if your physician is not going to do anything differently given the results of that test. Two percent, 5 percent, it doesn't matter if it can't be changed.

Then there is the cost associated with this test. My hospital charges on the order of $200 for this test. Consider the opportunity costs - what else could that $200 be spent on, in the care of American patients, and perhaps even more importantly in the context of global health and economics? Also consider the value of the test to a patient who might have to pay out of pocket for it - is it worth $200 to discriminate within an in-hospital mortality range of 2-5%?

This study, while meticulously conducted and reported, underscores the important distinction between statistical significance and clinical significance. With the aid of a ginormous patient registry, the authors clearly demonstrated a statistically significant result that is at least mildly interesting from a biological perspective (is it interesting that a failing heart spills some of its contents into the blodstream and that they can be detected by a highly sensitive assay?) But the clinical significance of the findings appears to be negligible, and I worry that this report will encourate the already rampant mindless use of this expensive test which, outside of the context of clinical pre-test probabilities, already serves to misguide care and run up healthcare costs in a substantial proportion of the patients in whom it is ordered.

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Blood Substitutes Doomed by Natanson's Meta-Analysis in JAMA

When the ARMY gives up on something, you should be on the lookout for red flags. (Pentagon types beholden to powerful contractors and highly susceptible to sunk cost bias still haven't given up on that whirligig of death called the Osprey, have they?) But the ARMY's abandonment of a blood substitute that it found was killing animals in tests was apparently no deterrent to Northfield Laboratories, Inc., makers of "Polyheme", as well as Wall Street investors in this an other companies working on products with a similar goal - to cook up an extracellular hemoglobin-based molecule that can be used in lieu of red blood cell transfusions in trauma patients and others.

Charles Natanson, an intramural researcher at the NIH and co-workers performed a meta-analysis of trials of blood substitutes which was published on-line today at the JAMA website: http://jama.ama-assn.org/cgi/content/full/299.19.jrv80007 . They found that these trials, which were powered for outcomes such as number of transfusions provided or other "surrogate-sounding" endpoints, when combined demonstrate that these products were killing subjects in these studies. The relative risk of death for study subjects receiving one of these products was 1.3 and the risk of myocardial infarction increased more than threefold. The robustness of these findings is enhanced by the biological plausibility of the result - cell-free hemoglobin is known to eat up nitric oxide from the endothelium of the vasculature leading to substantial vasoconstriction and other untoward downstream outcomes.

In addition to my penchant for cautionary tales, my interest in this study has to do with study design. We are beholden to "conventional" study design expectations where a p-value is a p-value, they're all 0.05, and an outcome is an outcome, whether it be bleeding, or pain or death, we don't differentially value them. But if you're studying a novel agent, looking for some crumby surrogate endpoint like number of transfusions, and your alpha threshold for that is 0.05, then the alpha threshold for death should be higher (say 0.25 or so), especially if you're underpowered to detect excess deaths. That kind of arrangement would imply that we value death at least 5 times higher than transfusion (I for one would rather have 500 or more transfusions that be dead, but that's a topic for another discussion).

Fortunately for any patients that may have been recruited to participate in such studies, Natanson et al undertook this perspicacious meta-analysis, and the editiorialists extended their recommendations for more transparency in data dissemination to argue, almost, that future trials of blood substitutes should be banned or boycotted. Even if the medical community does not have the gumption to go that far, prospective participants in such studies and their surrogates can at least perform a simple google search, and from now on the Natanson article is liable to be on the first page.

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A [now open] letter to Congress re: Proposed Medicare Reimbursement Cuts

I'm not sure that this is entirely in keeping with the theme of this blog, but I will justify it by saying that the health of the healthcare system is of vital interest to all stakeholders including researchers with an interest in clinical trials. The following letter was sent via the ACCP to my senators and congressmen in regards to the Medicare reimbursement cuts that are to be instituted in July of this year. We were solicited via the medical professional society to be a voice in opposition to the cuts....

Dear Sir or Madam-

Physicians' income, especially that of primary care providers, upon whom patients rely most heavily for basic care, has been falling in real dollars (not keeping pace with inflation) for years, and the newest cuts will markedly exacerbate the disconcerting trend that already exists.

Most physicians do not begin earning income in earnest until they are over 30 years old, a significant lost opportunity due to prolonged schooling and training. This compounds the problem of substantial debt burden that recent graduates must bear. Economically speaking, medicine, especially in the essential primary care fields, is no longer an attractive option for many talented students and graduates. From a job satisfaction standpoint, medicine has also become far less attractive due to regulatory burdens, paperwork, lack of adequate time to spend with patients, and fragmentation of care.

This fragmentation of care is in fact at least partially driven by Medicare cuts. When reimbursement to an individual physician is cut, s/he simply "farms out" parcels of the overall care of the patient to other physicians and specialists. This "multi-consultism" militates against any cost savings that might be achieved by cuts in reimbursement to individual physicians. Perhaps more alarming is the fact that care delivery is less comprehensive, more fragmented, and less satisfying to patients and physicians alike, the latter which may feel a "diffusion of responsibilty" regarding patients' care when multiconsultism is employed. Reduced reimbursements also likely drive the excess ordering of laboratory tests and radiographic scans, both in situations where the physician stands to profit from the testing and when s/he does not, in the latter case because the care is being "farmed out" not to another physician, but to the laboratory or radiology suite. The result is that Medicare "cuts" may paradoxically increase overall net healthcare expenditures. Physicians are already squeezed as much as they can tolerate being squeezed. Further cuts are certain to backfire in this and myriad other ways.

A perhaps more insidious, invidious, and pernicious result of reimbursement cuts is that it is driving the talent out of medicine, especially primary care medicine. Were it not for the veritable reimbursement shelter that I experience as a practitioner at an academic medical center, I would surely not be practicing medicine in any traditional way - it is simply not worth it. Hence we have the genesis and proliferation of "concierge practices" where the wealthy pay an annual fee for entry into the practice, only cash payments are accepted, and more traditional service from your physician (e.g., time to talk to him/her in an unhurried fashion) can be expected by patients. Hence we have, as pointed out in a recent New York Times article (http://query.nytimes.com/gst/fullpage.html?res=9C05E6D81E38F93AA25750C0A96E9C8B63&scp=2&sq=dermatology&st=nyt ), the siphoning of medical student talent into specialties such as dermatology and plastic surgery because the lifestyle is more attractive and reimbursement is not a problem since the "clientele" (aka patients) are affluent and pay out-of-pocket. Hence we have the brightest physicians, such as my colleague and close friend Michael C., MD, leaving medicine altogether to work on Wall Street in the financial sector. All of these disturbing trends threaten to undermine what was heretofore (and hopefully still is) one of the best healthcare systems on the planet. I, for one, will not recommend a career in primary care to any medical student who seeks my advice, and to undergraduates contemplating a career in medicine I say "enter medicine only if it is the only field you can invision yourself ever being happy in."

The system is broken, and we as a country cannot endure and thrive if our healthcare expenditures continue to eat up 15+% of our GDP. But cutting the payments to physicians, the very workforce upon which delivery of any care depends, is no longer a viable solution to the problem. Other excesses in the system, such as use of branded pharmaceuticals (e.g., Vytorin or Zetia) when generic alternatives are as good or better, use of expensive scans of unproven benefit (screening CT scans for lung cancer) when cheaper alternatives exist (stoping smoking), excessive and wasteful laboratory testing of unproven benefit (daily laboratory testing on hospital inpatients, wanton ordering of chest x-rays, head CTs, EKGs, and echocardiograms), use of therapeutic modalities of very high cost and modest benefit (AICDs, lung transplantation, back surgery, knee arthroscopy, coated stents, etc.), and provision of futile care at the end of life are better targets for cost savings, limitations on which are far less likely to compromise delivery of generally effective and affordable care for the average citizen.

I urge congress to consider the far-reaching but difficult to measure consequences of further reimbursement cuts before an entire generation of the most talented physicians and potential physicians determines that the financial, lifestyle, and opportunity costs of practicing medicine, especially primary care medicine, are just too much to bear.

Regards,

Scott K Aberegg, MD, MPH, FCCP
Assistant Professor of Medicine
The Ohio State University College of Medicine
Columbus,

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MRK and SGP: Ye shall know the truth, and the truth shall send thy stock spiralling

Apparently, the editors of the NEJM read my blog (even though they stop short of calling for a BOYCOTT):

"...it seems prudent to encourage patients whose LDL cholesterol levels remain elevated despite treatment with an optimal dose of a statin to redouble their efforts at dietary control and regular exercise. Niacin, fibrates, and resins should be considered when diet, exercise, and a statin have failed to achieve the target, with ezetimibe reserved for patients who cannot tolerate these agents."

Sound familiar?

The full editorial can be seen here: http://content.nejm.org/cgi/content/full/NEJMe0801842
along with a number of other early-release articles on the subject.

The ENHANCE data are also published online (http://content.nejm.org/cgi/content/full/NEJMoa0800742
and there's really nothing new to report. We have known the results for several months now. What is new is doctors' nascent realization that they have been misled and bamboozled by the drug reps, Big Pharma, and their own long-standing, almost religious faith in surrogate endpoints (see post below). It's like you have to go through the stages of grief (Kubler-Ross) before you give up on your long-cherished notions of reality (denial, anger, bargaining, then, finally, acceptance). Amazingly, the ACC, whose statement just months ago appeared to be intended to allay patients' and doctors' concerns about Zetia, has done a apparent 180 on the drug: "Go back to Statins" is now their sanctimonious advice: http://acc08.acc.org/SSN/Documents/ACC%20D3LR.pdf

I was briefly at the ACC meeting yesterday (although I did not pay the $900 fee to attend the sessions). The Big Pharma marketing presence was nauseating. A Lipitor-emblazoned bag was given to each attendee. A Lipitor laynard was used to hold your $900 ID badge. Busses throughout the city were emblazoned with Vytorin and Lipitor advertisements among others. Banners covered numerous floors of the facades of city buildings. The "exhibition hall," a veritable orgy of marketing madness, was jam-packed with the most aesthetically pleasing and best-dressed salespersons with their catchy displays and gimmicks. (Did you know that abnormal "vascular reactivity" is a heretofore unknown "risk factor"? And that with a little $20,000 device that they can sell you (which you can probably bill for), you can detect said abnormal vascular reactivity.) The distinction between science, reality, and marketing is blurred imperceptibly if it exists at all. Physicians from all over the world greedily scramble for free pens, bags, and umbrellas (as if they cannot afford such trinkets on their own - or was it the $900 entrance fee that squeezed their pocketbooks?) They can be seen throughout the convention center with armloads of Big Pharma propaganda packages: flashlights, laser pointers, free orange juice and the like.

I just wonder: How much money does the ACC receive from these companies (for this Big Pharma Bonanza and for other "activities")? If my guess is in the right ballpark, I don't have to wonder why the ACC hedged in its statement when the ENHANCE data were released in January. I think I might have an idea.

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Torcetrapib, Ezetimibe, and Surrogate Endpoints: A Cautionary Tale

In today's JAMA, (http://jama.ama-assn.org/cgi/content/extract/299/12/1474 ), Drs. Psaty and Lumley echo many of the points on this blog over the last six months about ezetimibe and torcetrapib (see posts below.) While they stop short of calling for a boycott of ezetimibe, and their perspective on torcetrapib is tempered by Pfizer's early conduct of a trial with hard outcomes as endpoints, their commentary underscores the dangers inherent in the long-standing practice of almost unquestioningly accepting the validy of "established" surrogate endpoints. The time to re-examine the validity of surrogate endpoints such as glycemic control, LDL, HDL, and blood pressure is now. Agents to treat these maladies are abundant and widely accessible, so potential delays in discovery and approval of new agents is no longer a suitable argument for a "fast track" approval process for new agents. We have seen time and again that such "fast tracks" are nothing more than expressways to profit for Big Pharma.

Psaty and Lumley's chronology of the studies of ezitimibe and their timing are themselves timely and should refocus needed scrutiny on the role of pharmaceutical companies as the stewards of scientific data and discovery.

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The CORTICUS Trial: Power, Priors, Effect Size, and Regression to the Mean

The long-awaited results of another trial in critical care were published in a recent NEJM: (http://content.nejm.org/cgi/content/abstract/358/2/111). Similar to the VASST trial, the CORTICUS trial was "negative" and low dose hydrocortisone was not demonstrated to be of benefit in septic shock. However, unlike VASST, in this case the results are in conflict with an earlier trial (Annane et al, JAMA, 2002) that generated much fanfare and which, like the Van den Berghe trial of the Leuven Insulin Protocol, led to widespread [and premature?] adoption of a new therapy. The CORTICUS trial, like VASST, raises some interesting questions about the design and interpretation of trials in which short-term mortality is the primary endpoint.

Jean Louis Vincent presented data at this year's SCCM conference with which he estimated that only about 10% of trials in critical care are "positive" in the traditional sense. (I was not present, so this is basically hearsay to me - if anyone has a reference, please e-mail me or post it as a comment.) Nonetheless, this estimate rings true. Few are the trials that show a statistically significant benefit in the primary outcome, fewer still are trials that confirm the results of those trials. This begs the question: are critical care trials chronically, consistently, and woefully underpowered? And if so, why? I will offer some speculative answers to these and other questions below.

The CORTICUS trial, like VASST, was powered to detect a 10% absolute reduction in mortality. Is this reasonable? At all? What is the precedent for a 10% ARR in mortality in a critical care trial? There are few, if any. No large, well-conducted trials in critical care that I am aware of have ever demonstrated (least of all consistently) a 10% or greater reduction in mortality of any therapy, at least not as a PRIMARY PROSPECTIVE OUTCOME. Low tidal volume ventilation? 9% ARR. Drotrecogin-alfa? 7% ARR in all-comers. So I therefore argue that all trials powered to detect an ARR in mortality of greater than 7-9% are ridiculously optimistic, and that the trials that spring from this unfortunate optimism are woefully underpowered. It is no wonder that, as JLV purportedly demonstrated, so few trials in critical care are "positive". The prior probability is is exceedingly low that ANY therapy will deliver a 10% mortality reduction. The designers of these trials are, by force of pragmatic constraints, rolling the proverbial trial dice and hoping for a lucky throw.

Then there is the issue of regression to the mean. Suppose that the alternative hypothesis (Ha) is indeed correct in the generic sense that hydrocortisone does beneficially influence mortality in septic shock. Suppose further that we interpret Annane's 2002 data as consistent with Ha. In that study, a subgroup of patients (non-responders) demonstrated a 10% ARR in mortality. We should be excused for getting excited about this result, because after all, we all want the best for our patients and eagerly await the next breaktrough, and the higher the ARR, the greater the clinical relevance, whatever the level of statistical significance. But shouldn't we regard that estimate with skepticism since no therapy in critical care has ever shown such a large reduction in mortality as a primary outcome? Since no such result has ever been consistently repeated? Even if we believe in Ha, shouldn't we also believe that the 10% Annane estimate will regress to the mean on repeated trials?

It may be true that therapies with robust data behind them become standard practice, equipoise dissapates, and the trials of the best therapies are not repeated - so they don't have a chance to be confirmed. But the knife cuts both ways - if you're repeating a trial, it stands to reason that the data in support of the therapy are not that robust and you should become more circumspect in your estimates of effect size - taking prior probability and regression to the mean into account.

Perhaps we need to rethink how we're powering these trials. And funding agencies need to rethink the budgets they will allow for them. It makes little sense to spend so much time, money, and effort on underpowered trials, and to establish the track record that we have established where the majority of our trials are "failures" in the traditional sence and which all include a sentence in the discussion section about how the current results should influence the design of subsequent trials. Wouldn't it make more sense to conduct one trial that is so robust that nobody would dare repeat it in the future? One that would provide a definitive answer to the quesiton that is posed? Is there something to be learned from the long arc of the steroid pendulum that has been swinging with frustrating periodicity for many a decade now?

This is not to denigrate in any way the quality of the trials that I have referred to. The Canadian group in particular as well as other groups (ARDSnet) are to be commended for producing work of the highest quality which is of great value to patients, medicine, and science. But in keeping with the advancement of knowledge, I propose that we take home another message from these trials - we may be chronically underpowering them.

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The "Trials" and Tribulations of Powering Clinical Trials: The Case of Vasopressin for Septic Shock (VASST trial)

Nobody likes "negative" trials. They're just not as exciting as positive ones. (Unless they show that something we're doing is harmful or that a product that Wall Street has bet heavily on is headed for the chopping block.) But "negative" studies such as an excellent one by Russell et al in a recent NEJM (http://content.nejm.org/cgi/content/abstract/358/9/877 ) show just how difficult it is to design and conduct a "positive" trial. The [non-significant] trends in this study, namely that vasopressin is superior to norepinephrine in reducing mortality in septic shock, were demonstrated in a study that had an a priori power of 80%, based on an expected mortality rate of 60% in the placebo group. Actual power in the study was significantly less, not because, as the authors appear to suggest, the observed placebo mortality was only ~39%, but rather because the observed effect size fell markedly short of the anticipated 10% absolute mortality reduction. In order to demonstrate a mortality benefit of the magnitude observed in the current trial (~4% ARR) at a significance level of 0.05, approximately 1500 patients in each study arm would be required. This is a formidable number for a critical care trial.

Thus, this trial illustrates the trials and tribulations of designing and conducting studies with 28-day mortality as an endpoint. These studies not only entail substantial costs, but pose challenges for patient recruitment, necessitating the participation of numerous centers in a multinational setting. The coordination of such a trial is daunting. It is understandable, therefore, that investigators may wish to be optimistic about the ARR they can expect from a therapy, as this will reduce sample size and increase the chances that the trial will be successfully completed in a resonable period of time. (For an example of a study which had to be terminated early because of these challenges, see Mancebo et al : http://ajrccm.atsjournals.org/cgi/content/short/200503-353OCv1 ). Powering the trial at 80% instead of 90% likewise represents a compromise between optimism for the efficacy of the therapy and optimism for patient recruitment. In essence, the lower the power, the more "faith" there must be that a roll of the trial dice will confirm the alternative hypothesis.

These realities played out [dissappointingly] in the Russell trial. The p-value for the ARR (28-day mortality - the primary endpoint) associated with vasopressin compared with placebo was 0.26, while that associated with 90-day mortality (a prespecified secondary endpoint) was 0.11. Thus, this trial is considered negative by conventional standards.

But its being "negative" does not mean that it is not of value to practitioners. This large experience with vasopressin demonstrates both that this agent is a viable alternative to norepinephrine in regards to raising the MAP to within the goal range, as also that we can expect that there will not be a significant excess of adverse events when this agent is used. In my opinion, this study represents a veritable "green light" for continued use of this agent, as I agree with the editorialist (http://content.nejm.org/cgi/reprint/358/9/954.pdf ) that many patients with sepsis who are not responding to norepinephrine respond dramatically and favorably to this agent.

Perhaps there is a larger lesson here. Should we use the same p-value threshold for a study of, say, an antidepressant as we do for a study of an agent that may reduce mortality? In the former case, we may be most concerned about exposure of patients to a costly drug with no benefits and potential side effects - in essence, we are most concerned with a Type I Error, i.e., concluding that there is a benefit when in reality there is none. Perhaps in a trial of a potentially life-saving therapy (e.g., vasopressin) we should be most concerned with a Type II Error, i.e., concluding that there is no real benefit when in reality one exists. If that were the case, and you may have already guessed that I believe that it should be, we could address this concern by loosening the standard of statistical significance for a study of potentially life-saving agents.

The standards notwithstanding, critical care practitioners are free to interpret these data as they see fit. And one reasonable conclusion is that, the trends being in the right direction and the side effect profile being acceptable, we should be using more vasopressin in septic shock.

Or, we must make a tough call: do we want to invest the resources in a much larger trail to determine if vasopressin can be shown to reduce mortality at the conventional p-value level of 0.05? Can we recruit the necessary 3000 patients?

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Wake Up and Smell the Coffee then Wake Up Your Patients and Let Them Breathe

A few weeks ago in The Lancet (http://www.thelancet.com/journals/lancet/article/PIIS0140673608601051/abstract ) appeared a wonderful and pragmatic article demonstrating the effectiveness of combining Spontaneous Awakening Trials (SATs) with Spontaneous Breathing Trials (SBTs) in the ICU. This strategy of "Wake Up and Breathe" was highly effective and critical care practitioners everywhere should take heed. Unfortunately, a penchant for the status quo and a heaping of omission bias led the editorialist to foment skepticism for the adoption of "wake up and breathe." My colleagues and I find this skepticism unfounded and frankly dangerous in that it risks reducing the adoption of this highly effective strategy, the benefits of which clearly exceed the risks. Our letter to the editor of The Lancet was not accepted for publication, but is posted below. Hats off to Girard and Ely and co-workers for this vital addition to our literature. Now if we can just convince critical care practitioners to wake up and wake their patients up...

We read with interest the report of the ABC Trial which demonstrated the efficacy of combining daily awakenings with breathing trials in mechanically ventilated patients (1). In the accompanying editorial, Dr. Brochard contends that “sedation is also an important component of care for critically ill patients,” but he cites only one review article to support this claim (2). It is unknown if the disturbing weaning experiences he references are related to sedation restriction. What is known with reasonable certainty is that oversedation is common and associated with increased delirium (1;3), neuroimaging (4), long-term psychiatric consequences (5) and mortality (1) and longer duration of mechanical ventilation and ICU stay (1;4). The ABC trial adds to this body of literature by demonstrating the practical utility of combining daily sedation cessation with spontaneous breathing trails. That 92% of spontaneous awakening trials were well-tolerated strongly suggests that patients were no worse without sedation, and is consistent with prior studies showing that oversedation, not undersedation, is the principal risk to critically ill patients.
For too long, we suffered from a dearth of quality evidence to guide the care of the critically ill. Now that such evidence is available, we would be wise to act upon it. We therefore disagree with Dr. Brochard’s statement that “more information is needed to show that the approach is feasible and safe.” Each year that we await another confirmatory trial is another year that our patients suffer prolonged mechanical ventilation and illness due to our fondness for the status quo.


Reference List

1. Girard TD, Kress JP, Fuchs BD, Thomason JW, Schweickert WD, Pun BT et al. Efficacy and safety of a paired sedation and ventilator weaning protocol for mechanically ventilated patients in intensive care (Awakening and Breathing Controlled trial): a randomised controlled trial. Lancet 2008;371(9607):126-34.
2. Brochard L. Sedation in the intensive-care unit: good and bad? Lancet 2008;371(9607):95-7.
3. Pandharipande P, Shintani A, Peterson J, Pun BT, Wilkinson GR, Dittus RS et al. Lorazepam is an independent risk factor for transitioning to delirium in intensive care unit patients. Anesthesiology 2006;104(1):21-6.
4. Kress JP, Pohlman AS, O'Connor MF, Hall JB. Daily interruption of sedative infusions in critically ill patients undergoing mechanical ventilation. N.Engl.J Med 2000;342(20):1471-7.
5. Kress JP, Gehlbach B, Lacy M, Pliskin N, Pohlman AS, Hall JB. The long-term psychological effects of daily sedative interruption on critically ill patients. Am.J Respir.Crit Care Med 2003;168(12):1457-61.

James M. O'Brien, Md, MSc
Naeem A. Ali, MD
Scott K. Aberegg, MD, MPH

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Have the Peddlers of Antidepressants (Big Pharma) been Successful in Suppressing Negative Trial Results?

Yes, according to this article in yesterday's NEJM:
http://content.nejm.org/cgi/content/short/358/3/252

Talk about publication bias. According to Erick H. Turner, M.D. and coauthors, the selective publication of only "positive" trials, in addition to publishing in a positive light studies that the FDA considered "negative" leads to a 32% increase in the apparent efficacy of antidepressant drugs, on average (range 11-69%). Once again, profit trumps science, safety, and patient and public health.

What can we do about it? First, reduce by one third the effect size of any antidepressant results you see in an industry-sponsored clinical trial. Next, carefully consider whether whatever [probably modest] effect remains is worth the side effects (e.g., increase in suicide), cost, and nuisance of the drug. Third, prescribe generic agents. Fourth, don't allow pharmaceutical reps to speak with you about new products. Fifth, consider alternative treatments.

I am reminded of a curious occurrence relating to a drug that I think is definately worth the cost, side effects, and nuisance associated with it: Chantix (varenicline) - Pfizer's smoking cessation drug. In JAMA in July 2006,
(http://jama.ama-assn.org/content/vol296/issue1/index.dtl)
two nearly identical articles described two nearly identical studies, which shared many of the same authors. What was the intent of this? Why not conduct one larger study? Was the intent to diversify the risk of failure and allow for selective publication of positive results? I'm very interested in any information anyone can provide about this curious arrangement, which appears to be without precedent. Please leave your comments below.

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Is the American College of Cardiology (ACC) Complicit with Big Pharma (Merck and Shering-Plough)?

I am reminded of the surgical attending at Johns Hopkins who (perhaps apocryphally) would scream at the intern in the morning when a patient had done poorly overnight:
"Whose side are you on, the patient or the disease?!"

And I ask the ACC, "Whose side are you on? Patients' or Big Pharma's"?!

Their main web page now links to this statement:
http://www.acc.org/enhance.htm
which states:
"The American College of Cardiology recommends that major clinical decisions not be made on the basis of the ENHANCE study alone."

Is it really a "major clinical decision" to stop Zetia/Vytorin and take a statin or niacin until the very efficacy of Vytorin and Zetia is sorted out?

I'd say that the ACC and its members need to reconsider the rather major decision they made to support the use of this drug based on surrogate end-points. As with torcetrapib, they're going to have to learn the hard way to take their lashings.

The statement goes on to say:
"The ACC recommends that Zetia remain a reasonable option for patients who are currently on a high dose statin but have not reached their goal. The ACC also notes that Zetia is a reasonable option for patients who cannot tolerate statins or can only tolerate a low dose statin."

Well, that sounds reasonable, but do you really thing that the majority of patients on Zetia or Vytorin are on it because they failed a reasonable attempt to use a high-dose statin? We all know that after it hits the market, a drug is generally prescribed willy-nilly rather than carefully and rationally in selected patient groups. The ACC should know this. Hence my suspicion of complicity.

It bothers me how entrenched the use of these drugs becomes and how hard it is to remove patients from them. This is a serious status quo bias that I have commented upon before. Few physicians would start a patient on Avandia now, but the ones who are already on it get left on it. The same is true, it appears, with Vytorin, and the ACC is contributing to the status quo bias!

The mandate for physicians and the FDA is to prescribe only SAFE and EFFECTIVE therapies. The burden of scientific proof is on the drug companies who are driven by profit to promote these drugs. It is up to physicians to stand between patients' health and the companies' profits and prescribe only drugs that have met the burden of proof. And Vytorin and Zetia have not. Boycott them until the proof is in. Use alternative agents in the meantime.

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Vytorin Vanquished: ENHANCE comes out from hiding and the call for a BOYCOTT gathers steam

Merck (MRK) and Shering-Plough (SGP) have finally released the ENHANCE data and they do not look good, neither for MRK and SGP stock prices (both of which were significantly down in pre-market trading!) nor for patients who have been taking ezetimibe as either Vytorin or Zetia - all the trends were in the WRONG DIRECTION (i.e., they favored simvastatin alone) IN SPITE OF robust additional LDL lowering with ezitimibe:
http://biz.yahoo.com/bw/080114/20080114005752.html?.v=1
This further evidence that this drug does not influence important clinical outcomes should renew interest in BOYCOTTING ezitimibe in all forms until/unless improved clinically meaningful outcomes can be shown with this agent in properly designed and conducted trials with sufficient transparency.
(Of course, I recognize that Vytorin is Vanquished only in this battle, that others will follow, and that MRK and SGP will say that these "real trials" are still being conducted, as if they funded ENHANCE for no good reason, and as if, had it been a postive study, they would have downplayed its significance and emphasized cautious interpretation of the results, pending completion of the "real trials".)

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Jumping the Gun with Intensive Insulin Therapy (Leuven Protocol):How ICUs across the nation rushed to adopt a therapy which is probably not beneficial

In this week's NEJM is an anxiously awaited article about intensive insulin therapy in severely septic patients in the ICU: http://content.nejm.org/cgi/content/short/358/2/125
This business of intensive insulin therapy began with publication in the NEJM in 2001 an article by Van den Berghe et al showing a remarkable reduction in mortality in surgical (mostly post-cardiac surgery) patients in a surgical ICU. Thereafter ensued a veritable rush to adopt this therapy, and ICUs around the country began developing and adopting protocols for "tight glucose control" in spite of concerns about the study and its generalization to non-surgical patients who were not being fed concentrated intravenous dextrose solutions....

I vividly remember one of the ICU attendings at Johns Hopkins Hospital, Dr. Jimmy Sylvester, telling us on the morning after the study was published that "this is either the largest break-through in intensive care therapeutics ever, or these data are faked". In essence what he was saying was that the prior expectation of a result as dramatic as demonstrated by Van den Berghe was very low (see also: http://jama.ama-assn.org/cgi/content/full/294/17/2203 ). That lower prior probability should have reduced our confidence in the results, and made us more skeptical of the population studied and the dextrose solutions and the applicability to non-surgical patients. Well then, why didn't it?

My colleague James M. O'Brien, Jr, MD, MSc and I have one possible explanation for the rush to adopt "intensive insulin therapy" which we have dubbed the "normalization heuristic." Physicians, for all of our training, remain quite simple-minded. We like simple, feel-good fixes. Normalizing lab values is one of those things. "Make it normal and all will be fine," goes the mantra. We like to make the potassium normal. We like to make the hematocrit normal. We love it when the magnesium increases after we order 4 grams. It's satisfying. And it feels like we're doing some measurable, that is, easily measurable good in the world. Normalizing blood sugars fits that paradigm and makes us feel like we are doing good. But are we?

We have learned the hard way over the years that many of the things we do to "normalize" some surface value causes an undercurrent of harm for patients. Think suppression of PVCs (the CAST trial: http://content.nejm.org/cgi/content/abstract/321/6/406 ) or transfusion thresholds (the TRICC study and others: http://content.nejm.org/cgi/content/abstract/340/6/409 ). Oftentimes, it seems, our efforts to "normalize" some value cause more harm than good. It is quite possible that this is also the case with intensive insulin, and that the "feel-good" appeal of making the blood sugars normal in the short term in acutely ill patients propelled us to early adoption of this probably useless and possibly harmful therapy.

(For an analogous contemporaneous story about biology's complexity and defiance of simple explanations and logic such as the normalization heuristic, see: http://www.nytimes.com/2008/01/11/science/11ants.html?scp=1&sq=aiding+trees+can+kill+them.)

The interesting thing regarding the "adoption" of Van den Berghe's "Leuven protocol" is that no ICU I have worked in really adopted that protocol. They softened it up, making the target blood sugar not 80-120, but rather 120-150 or some similar range. So what was adopted was "moderate insulin therapy" rather than intensive insulin therapy. Nobody has any idea whether such an approach is beneficial. It's certainly safer. But it has substantial costs in terms of nursing care that might be better spent on other interventions (think sedation interruption).

(I have been highly critical of Van den Berghe's medical insulin article, and my criticisms were published in the NEJM. I was delighted that she did not even address me/them in "the authors reply" - apparently I left her speechless: http://content.nejm.org/cgi/content/extract/354/19/2069.)

So this wonderful article in the current issue by Brunkhorst et al is music to my ears. Rather than hiding the high rate of severe hypoglycemia in supplementary material, Brunkhorst et al come right out and say that not only was the Leuven protocol NOT associated with reduced mortality, but also that it had a very high incidence of severe side effects and that their DSMB had the wherewithal to stop the study early for safety reasons. Bravo!

We await the results of several other ongoing studies of intensive insulin therapy before we nail shut the coffin on the Leuven protocol. Meanwhile, I hope that someone somewhere will design a protocol to test the "moderate insulin therapy" that we rushed to adopt after the first Van den Berghe article as a half-hearted hedge/compromise between our "normalization heuristic", our tempered enthusiasm for the Leuven protocol, our desire to "do something" for critically ill patients, and our fear of causing side effects that result directly from our interventions (omission bias: http://mdm.sagepub.com/cgi/content/abstract/26/6/575 ).

Thank you, Brunkhorst et al, for testing the Leuven protocol in an even-handed and scientifically unbiased manner and for reporting your results candidly.

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Merck and Schering's "Secret Vytorin Panel"

Matthew Herper continues to lead the pack in investigating the shenanigans perpetrated by Shering-Plough (SGP) and Merck (MRK)in the conduct of the ENHANCE trial of Vytorin. I reiterate that it is my strong but measured and carefully considered opinion that this drug or ezetimibe should NOT be used in ANY patients until definitive evidence of efficacy is available, since alternative, more proven alternatives exist. Patients' health should not be risked on this drug. There is too much uncertainty, and too many proven alternatives.

Matthew's article describes more intriguing aspects of this saga, and I couldn't state it any better than he, so I invite you to read his article:

http://www.forbes.com/2008/01/10/merck-schering-vytorin-biz-cx_mh_0111enhance.html?partner=email

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Is there any place for the f/Vt (the Yang-Tobin index) in today's ICU?

Recently, Tobin and Jubran performed an eloquent re-analysis of the value of “weaning predictor tests” (Crit Care Med 2008; 36: 1). In an accompanying editorial, Dr. MacIntyre does an admirable job of disputing some of the authors’ contentions (Crit Care Med 2008; 36: 329). However, I suspect space limited his ability to defend the recommendations of the guidelines for weaning and discontinuation of ventilatory support.

Tobin and Jubran provide a whirlwind tour of the limitations of meta-analyses. These are important considerations when interpreting the reported results. However, lost in this critique of the presumed approach used by the McMaster group and the joint tack force are the limitations of the studies on which the meta-analysis was based. Tobin and Jubran provide excellent points about systematic error limiting the internal validity of the study but, interestingly, do not apply such criticism to studies of f/Vt.

For the sake of simplicity, I will limit my discussion to the original report by Yang and Tobin (New Eng J Med 1991; 324: 1445). As a reminder, this was a single center study which included 36 subjects in a “training set” and 64 subjects in a “prospective-validation set.” Patients were selected if “clinically stable and whose primary physicians considered them ready to undergo a weaning trial.” The authors then looked a variety of measures to determine predictors of those “able to sustain spontaneous breathing for ≥24 hours after extubation” versus those “in whom mechanical ventilation was reinstituted at the end of a weaning trial or who required reintubation within 24 hours.” While not explicitly stated, it looks as if all the patients who failed a weaning trial had mechanical ventilation reinstituted, rather than failing extubation.

In determining the internal validity of a diagnostic test, one important consideration is that all subjects have the “gold standard” test performed. In the case of “weaning predictor tests,” what is the condition we are trying to diagnose? I would argue that it is the presence of respiratory failure requiring continued ventilatory support. Alternatively, it is the absence of respiratory failure requiring continued ventilatory support. I would also argue that the gold standard test for this condition is the ability to sustain spontaneous breathing. Therefore, to determine the test performance of “weaning predictor tests,” all subjects should undergo a trial of spontaneous breathing regardless of the results of the predictor tests. Now, some may argue that the self-breathing trial (or spontaneous breathing trial) is, indeed, this gold standard. I would agree if SBTs were perfectly accurate in predicting removal of the endotracheal tube and spontaneous breathing without a ventilator in the room. This is, however, not the case. So, truly, what Yang and Tobin are assessing is the ability of these tests to predict the performance on a subsequent SBT.

Dr. MacIntyre argues that “since the outcome of an SBT is the outcome of interest, why waste time and effort trying to predict it?” I would agree with this within limits. Existing literature supports the use of very basic parameters (e.g., hemodynamic stability, low levels of FiO2 and PEEP, etc.) as screens for identifying patients for whom an SBT is appropriate. Uncertain is the value of daily SBTs in all patients, regardless of passing this screen or not. One might hypothesize that simplifying this step even further might provide incremental benefit. Yang and Tobin, however, must consider a failure on an SBT to have deleterious effects. They consider “weaning trials undertaken either prematurely or after an unnecessary delay…equally deleterious to a patient’s health.” There is no reference supporting this assertion. Recent data suggest that inclusion of “weaning predictor tests” do not save patients from harm due to avoiding SBTs destined to fail (Tanios et al. Crit Care Med, 2006; 34: 2530). On the contrary, inclusion of the f/Vt as the first in Tobin’s and Jubran’s “three diagnostic tests in sequence” resulted in prolonged weaning time.

Tobin and Jubran also note the importance of prior probabilities in determining the performance of a diagnostic test. In the original study, Yang and Tobin selected patients who “were considered ready to undergo a weaning trial” by their primary physicians. Other studies have reported that such clinician assessments are very unreliable with predictive values marginally better than a coin-flip (Stroetz et al, Am J Resp Crit Care Med, 1995; 152: 1034). Perhaps, the clinicians whose patients were in this study are better than this. However, we are not provided with strict clinical rules which define this candidacy for weaning but can probably presume that “readiness” is at least a 50% prior probability of success. Using Yang and Tobin’s sensitivity of 0.97 and specificity of 0.64 for f/Vt, we can generate a range of posterior probabilities of success on a weaning trial:


As one can see, the results of the f/Vt assessment have a dramatic effect on the posterior probabilities of successful SBTs. However, is there a threshold below which one would advocate not performing an SBT if one’s prior probability is 50% or higher? I doubt it. Even with a pre-test probability of successful SBT of 50% and a failed f/Vt, 1 in 25 patients would actually do well on an SBT. I am not willing to forego an SBT with such data since, in my mind, SBTs are not as dangerous as continued, unneeded mechanical ventilation. I would consider low f/Vt values as completely non-informative since they do not instruct me at all regarding the success of extubation – the outcome for which I am most interested.

Other studies have used f/Vt to predict extubation failure (rather than SBT failure) and these are nicely outlined in a recent summary by Tobin and Jubran (Intensive Care Medicine 2006; 32: 2002). Even if we ignore different cut-points of f/Vt and provide the most optimistic specificities (96% for f/Vt <100, Uusaro et al, Crit Care Med 2000; 28: 2313) and sensitivities (79% for f/VT <88, Zeggwagh et al., Intens Care Med 1999; 25:1077), the f/Vt may not help much. As with the prior table, using prior probabilities and the results of the f/Vt testing, we can generate posterior probabilities of successful extubation:


As with the predictions of SBT failure, a high f/Vt lowers the posterior probability of successful extubation greatly. However, one must consider the cut off for posterior probabilities in which one would not even attempt an SBT. Even with a 1% posterior probability, 1 in 100 patients will be successfully extubated. This is the rate when the prior probability of successful extubation is only 20% AND the patient has a high f/Vt! What rate of failed extubation is acceptable or, even, preferable? Five percent? Ten percent? If one never reintubates a patient, it is more likely that he is waiting “too long” to extubate rather than possessing perfect discrimination. Furthermore, what is the likelihood that patients with poor performance on an f/Vt will do well on an SBT? I suspect this failure will prohibit extubation and the high f/Vt values will only spare the effort of performing the SBT. Is the incremental effort of performing SBTs on those who are destined to fail such that it requires more time than the added complexity of using the f/Vt to determine if a patient should receive an SBT at all? Presuming that we require an SBT prior to extubation, low f/Vt values remain non-informative. One could argue that with a posterior probability of >95%, we should simply extubate the patient, but I doubt many would take this approach, except in those intubated for reasons not related to respiratory problems (e.g. mechanical ventilation for surgery or drug overdose).

Drs. Tobin, Jubran and Marini (who writes an additional, accompanying editorial, Crit Care Med 2008; 36: 328) are master clinicians and physiologists. When they are at the bedside, I do not doubt that their “clinical experience and firm grasp of pathophysiology” (as Dr. Marini mentions), can match or even exceed the performance of protocolized care. Indeed, expert clinicians at Johns Hopkins have demonstrated that protocolized care did not improve the performance of the clinical team (Krishnan et al., Am J Resp Crit Care Med 2004; 169: 673). I have heard Dr. Tobin argue that this indicates that protocols do not provide benefit for assessment of liberation (American Thoracic Society, 2007). I doubt that the authors would strictly agree with his interpretation of their data since several of the authors note in a separate publication that “the regularity of steps enforced by a protocol as executed by nurses or therapists trumps the rarefied individual decisions made sporadically by busy physicians” (Fessler and Brower, Crit Care Med 2005; 33: S224). What happens to the first patient who is admitted after Dr. Tobin leaves service? What if the physician assuming the care of his patients is more interested in sepsis than ventilatory physiology? What about the patient admitted to a small hospital in suburban Chicago rather than one of the Loyola hospitals? Protocols do not intend to set the ceiling on clinical decision-making and performance, but they can raise the floor.

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Results of the Poll - Large Trials are preferred

The purpose of the poll that has been running alongside the posts on this blog for some months now was to determine if physicians/researchers (a convenience sample of folks visiting this site) intuitively are Bayesian when they think about clinical trials.

To summarize the results, 43/68 respondents (63%) reported that they preferred the larger 30-center RCT. This differs significantly from the hypothesized value of 50% (p=0.032).

From a purely mathematical and Bayesian perspective, physicians should be ambivalent about the choice between a large(r) 30-center RCT involving 2100 patients showing a 5% mortality reduction at p=0.0005, and 3 small(er) 10-center RCTs involving 700 patients each showing the same 5% mortality reduction at p=0.04. In essence, unless respondents were reading between the lines somewhere, the choice is between two options with identical posterior probabilities. That is, if the three smaller trials are combined, they are equal to the larger trial and the meta-analytic p-value is 0.0005. Looked at from a different perspective, the large 30-center trial could have been analyzed as 3 10-center trials based on the region of the country in which the centers were located or any other arbitrary classification of centers.

Why this result? I obviously can't say based on this simple poll, but here are some guesses: 1.) People are more comfortable with larger multicenter studies, perhaps because they are accustomed to seeing cardiology mega-trials in journals such as NEJM; or 2.) The p-value of 0.04 associated with the small(er) studies seems "marginal" and the combination of the three studies is non-intuitive, and/or it is not possible to see that the combination p-value will be the same. However, I have some (currently unpublished) data which show that [paradoxically] for the same study, physicians are more willing to adopt a therapy with a higher rather than a lower p-value.
Further research is obviously needed to determine how physicians respond to evidence from clinical trials and whether or not their responses are normative. In this poll, it appears that they were not.

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Patients and Physicians should BOYCOTT Zetia and Vytorin: Forcing MRK and SGP to come clean with the data

You wouldn't believe it - or would you? The NYT reports today that SGP has data from a number of - go figure - unpublished studies that may contain important data about increased [and previously undisclosed] risks of liver toxicity with Zetia and Vytorin: http://www.nytimes.com/2007/12/21/business/21drug.html Unproven benefits, undisclosed risks? If I were a patient, I would want to be taken off this drug and be put on atorvastatin or simvastatin or a similar agent. If teh medical community would get on board and take patients off of this unproven and perhaps risky drug, that might at least force the companies to come clean with their data.

In fact, I'm astonished at the medical community's reluctance to challenge the status quo which is represented by widespread use of drugs such as this and Avandia, for which there is no proof of efficacy save for surrogate endpoints, and for which there is evidence of harm. These drugs are not good bets unless alternatives do not exist, and of course they do. I am astonished in my pulmonary clinic to see many patients referred for dyspnea, with a history of heart disease and/or cardiomyopathy who remain on Avandia. Apparently, protean dyspnea is not a sufficient wake-up call to change the diabetes management of a patient who is receiving an agent of unproven efficacy and which is known to cause fluid retention and CHF. This just goes to show how effective pharmaceutical marketing campaigns are, how out-of-control things have become, and how non-normative physicians' approach to the data are.

The profit motive impels them forward. The evidence does not support the agents proffered. Evidence of harm is available. Alternatives exist. Why aren't physicians taking patients off drugs such as vioxx, avandia, zetia, and vytorin, and using alternative agents until the confusion is resolved?

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Dexmedetomidine: a New Standard in Critical Care Sedation?

In last week's JAMA, Wes Ely's group at Vanderbilt report the results of a trial comparing dexmedetomidine to lorazepam for the sedation of critically ill patients:
http://jama.ama-assn.org/cgi/content/short/298/22/2644
This group, along with others, has taken the lead as innovators in research related to sedation and delirium in the ICU (in addition to other topics), and this is a very important article in this area. In short, the authors found that, when compared to lorazepam, dexmed led to better targeted sedation and less time in coma, with a trend toward improved mortality.

One of the most impressive things about this study is stated as a post-script:

“This investigator-initiated study was aided by receipt of study drug and an unrestricted research grant for laboratory and investigational studies from Hospira Inc….Hospira Inc had no role in the design or conduct of the study; in the collection, analysis, and interpretation of the data; in the preparation, review, or approval of this manuscript; or in the publication strategy of the results of this study. These data are not being used to generate FDA label changes for this medication, but rather to advance the science of sedation, analgesia, and brain dysfunction in critically ill patients….”

Investigator-initiated....investigator-controlled design and publication, investigators as stewards of the data.....music to my ears.


But is dexmed going to be the new standard in critical care sedation? For that question, it would appear that it is too early for answers. I have the following observations:
• This study used higher doses of dexmed for longer durations than what the product labeling advises. Should practitioners use the doses studied or the approved doses? My very small experience with this drug so far at the labelled doses is that it is difficult to use in that it does not achieve adequate sedation in the most agitated patients - those receiveing the highest doses of benzos and narcotics, in whom lightenting of sedationl is assigned the highest priority.
• The most impressive primary endpoint achieved by the drug was days alive without delirium or coma, but most of it was driven by coma-free days. Perhaps this is not surprising given two aspects of the study's design
1. Patients did not have daily interruptions of sedative infusions, a difficult-to-employ, but evidence-based practice to reduce oversedation and coma
2. lorazepam was titrated upwards without boluses between dose increases. Given the long half-life of this drug, we would expect overshoot by the time steady state pharmacokinetics were achieved.
So is it surprising that patients in the dexmed group had fewer coma-free days?
• We are not told about the tracheostomy practices in this study. Getting a trach earlier may lead to both sedation reduction and improved mortality (See http://ccmjournal.org/pt/re/ccm/abstract.00003246-200408000-00009.htm;jsessionid=HlfG93Qfvb113sCpnD10053YzKqMB3zFfDTdbGvgCQPdlMZ3S8kV!1219373867!181195629!8091!-1?index=1&database=ppvovft&results=1&count=10&searchid=1&nav=search).
• We are not told the proportion of patients in each group who had withdrawal of support. Anecdotally, I have found that families have greater willingness to withdraw support for patients who are comatose, regardless of other underlying physiological variables or organ failures. Can the trend towards improved mortality with dexmed be attributed to differrences in willingness of families to WD support?
• In spite of substantial data that delirium is associated with mortality (http://jama.ama-assn.org/cgi/content/abstract/291/14/1753?maxtoshow=&HITS=10&hits=10&RESULTFORMAT=&fulltext=delirium&searchid=1&FIRSTINDEX=0&resourcetype=HWCIT ), and these data showing that there is a TREND towards fewer delirium-free days with dexmed, the hypothesis that dexmed improves mortality via improvement in delirium is one that can only be tested by a study with mortality as a primary endpoint.
The data from the current study are compelling, and Ely and investigators are to be commended for the important research they are doing (this article is only the tip of that iceberg of research). However, it remains to be seen if one sedative compared to others can lead to improvements in mortality or more rapid recovery from critical illness, or whether limitation of sedation in general with whatever agent is used is primarily responsible for improved outcomes.

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ENHANCE trial faces congressional scrutiny

Merck and Shering-Plough had better get their houses in order. Congress is on the case:

http://www.nytimes.com/2007/12/12/business/12zetia.html?_r=1&oref=slogin

Apparently, representatives of the US populus, which pays for a substantial portion of the Zetia sold, are not pleased by the delays in release of the data from the ENHANCE trial. The chicanery is going to be harder to sustain.

I certainly hope for everyone's sake (especially patients') that there is no foul play afoot with this trial or ezetimibe - Merck can hardly withstand another round of Vioxx-type suits, can it? Or can it. Merck's stock price (MRK: http://finance.yahoo.com/q/bc?s=MRK&t=5y&l=on&z=m&q=l&c=) is at the same level as it was in Jan, 2004. Some high price to pay for obfuscating the truth, concealing evidence of harm, bilking insurers and the American public and government for billions of $$$ for a prescription painkiller when equivalent non-branded products were available, and causing thousands of heart attacks in the process....

The consequences should be harsher the second time around.....

Type rest of the post here

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Pronovost, Checklists, and Putting Evidence into Practice

In this week's New Yorker:
http://www.newyorker.com/reporting/2007/12/10/071210fa_fact_gawande
Atul Gawande, a popular physician writer who may be familiar to readers from his columns in the NEJM and the NYT, chronicles the hurculean efforts by Peter Pronovost, MD, PhD at Johns Hopkins Hospital to make sure that the mundane but effective does not always take back seat to the heroic but largely symbolic efforts of critical care doctors.

One of my chronic laments is that evidence is not utilized and that physician efforts do not appear to be rationally apportioned to what counts most. There appears to be too much emphasis on developing evidence and too little emphasis on making sure it is expeditiously adopted and employed; to much emphasis on diagnosis, too little emphasis on evidence-based treatment; too much focus on the "rule of rescue" too little focus on the "power of prevention". Pronovost has demonstrated that simple checklists can have bountiful yields in terms of teamwork, prevention, and delivery of effective care - then why aren't we all familiar with his work? Why doesn't every ICU use his checklists?

My own experience at the Ohio State University Medical Center is emblematic of the challenges of getting an unglamorous thing like a checklist accepted as a routine part of clinical practice in the ICU. In spite of evidence supporting it, its obvious rational basis, widespread recognition that we often miss things if we aren't rigorous and systematic, adopting an adapted version of Pronovost's checklist at OSUMC has proven challenging (albeit possible). As local champion of a checklist that I largely plagarized from Pronovost's original, I have been told by colleagues that it is "cumbersome", but RNs that it is "superfluous", by fellows that it is a "pain", by people of all disciplines that they "don't seen the point" and have been frustrated that when I do not personally assure that it is being done daily (by woaking through the ICU and checking), that it is abandoned as yet another "chore", another piece of bureaucratic red tape that hampers the delivery of more important "patient-centered" care - such as procudures and ordering of tests.

All of these criticisms are delivered despite my admonition that the checklist, like a fishing expedition, is not expected to yield a "catch" on every cast, but that if it is cast enough, things will be caught that would otherwise be missed; desipte my reminder that it is an opportunity to improve our communication with our multi-disciplinary ICU team (and to learn the names of its constituents); despite producing evidence of its benefit and evidence of underutilization of evidence-based therapies which the checklist reminds practitioners to consider. If I were not personally committed to making sure that the checklist is photocopied/available and consistently filled out (by our fellows, who deserve great credit for filling it out), it would quicly fall by the wayside, another relic of a well-meaning effort to encourage concsientiousness through bureaucracy and busy-work (think HIPPA here -the intent is noble, but the practical result an abject failure).

So what is the solution? How are we to increase acceptance of Pronovost's checklist and recognition of its utility and its necessity? It could be through fiat, through education, through a variety of means. But it appears that it has survived at Hopkins because of Pronovost's ongoing efforts to promote it and extol its benefits and its virtues and to get "buy-in" from other stake-holders: RNs, patients, adminitrators, the public, and other physicians. This is not an easy task - but then again, rarely is anything that is worth it. Hopefully other champions of this and other unglamorous innovations will continue to advocate for mundane but effective interventions to improve communication among members of multidisciplinary healthcare teams, the utilzation of evidence-based therapies, and outcomes for patients.

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Eltrombopag: Alas data that speak for themselves

In this week's NEJM, two articles describe the results of two phase 2 studies of Eltrombopag, a non-peptide, oral agonist of the thrombopoetin receptor, one in patients with HCV and thrombocytopenia:
http://content.nejm.org/cgi/content/abstract/357/22/2227
and another in patients with ITP:
http://content.nejm.org/cgi/content/abstract/357/22/2237.

I have grown so weary of investigators who must speak for their data - massaging them, doing post-hoc analyses, proffering excuses for them, changing their endpoints and designs to conform to the data, offering partial analyses, ignoring alternative interpretations, stacking the deck in favor of their agent - that I breathe a sigh of relief and contentment when I see data like these which are robust enough to speak for themselves - both in level of statistical significance and effect size which is clearly clinically meaningful.

Of course, we should be clear what these studies can tell us and what they can't. This is a phase 2 trial and it certainly demonstrated efficacy and a dose response which should satisfy even the harshest critics (e.g., me). However, the time of treatment was relatively short so we don't know if the response can be sustained over time; and the study was wildly underpowered to detect side effects at all but the highest frequencies. What untoward effects of stimulating megakaryocytes through this pathway might there be? What about thrombotic complications?
(This is an interesting question also - supposing there are increased thrombotic complications with this agent - how will we know whether this is a direct adverse effect of the agent or whether it results from reversal of protection against thrombosis conferred by ITP itself, if that even exists?)

So, we await the results of larger phase 3 trials of Eltrombopag, hoping that they are well designed and attuned to careful measure of adverse effects, content for now that a novel and apparently robust agent has been discovered to add to the currently inadequate treatments for cirrhotic thrombocytopenia and that associated with ITP.

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Are Merck and Schering-Plough "enhancing" the ENHANCE data?

I'm from Missouri, "The Show-Me State," and like many others, I'd like Merck and Schering-Plough to show me the ENHANCE trial results. I'd like them raw and unenhanced, please. This expose in the NYT last week is priceless:

http://www.nytimes.com/2007/11/21/business/21drug.html?ex=1353387600&en=2d41b634a5c553df&ei=5124&partner=permalink&exprod=permalink

I just learned that Matthew Herper at Forbes reported it first in an equally priceless article:
http://www.forbes.com/home/healthcare/2007/11/19/zetia-vytorin-schering-merck-biz-health-cx_mh_1119schering.html

In a nutshell: Sinvastatin (misspelling intentional) recently lost patent protection. Sinvastatin (Zocor) has been combined with ezetimibe (Zetia) to yield combination drug Vytorin. This combination holds the promise of rescuing Sinvastatin, a multi-billion dollar drug, from generic death if doctors continue to prescribe it in combination with ezetimibe as a branded product. There's only one problem: unlike sinvastatin, ezetimibe has never been shown to do anyting but lower LDL cholesterol, a surrogate endpoint. That's right, just like Torcetrapib, we don't know what ezetimibe does to clinically meaningful outcomes, the ones that patients and doctors care about. (The drug compaines care about surrogate outcomes because some of them are sufficient for FDA approval - that subject is a blog post or two in itself.)

So Merck and Schering-Plough designed the ENHANCE trial, which compares 80 mg of simvastatin to 80 mg of simvastatin + 10 mg of ezetimibe on the primary outcomes of carotid intima-media thickness and femoral artery (IMT). Note that we still don't have a clinically meaningful endpoint as a primary outcome, but we're getting there. A trial assessing the combination's effects on meaningful outcomes isn't due to be completed until 2010. Of course a big worry here is that ezetimibe is like torcetrapib and that in spite of creating a more favorable cholesterol profile, there is no clinically meaningful outcome improvement; i.e., the cholesterol panel is a merely cosmetic result of ezetimibe.

(Regarding the ongoing trials evaluating clinical outcomes: Schering-Plough is up to some tricks there too to rescue Sinvastatin from generic death. The improve-it study [they need a study to "prove-it" before they embark on a mission to "improve-it," don't you think?] design can be seen here:
http://clinicaltrials.gov/ct/show/NCT00202878
In this study, ezetimibe is not being compared to maximum dose sinvastatin, nor is a combination of ezetimibe and sinvastatin being compared to maximum sinvastatin alone. If one of those comparisons were done, important information could be gleaned - doctors would know, for example, if ezetimibe is superior to an alternative (one that is now available in generic, mind you) at maximum dose, or if its addition to maximum dose sinvastatin has any additional yield. But such trials are too risky for the company - they may show that there is no point to prescribing ezetimibe because it is either less potent than max dose sinvastatin, or that it has no incremental value over max dose sinvastatin. So, instead, sinvastatin 40mg+ ezetimibe 10mg is being compared to sinvastatin 40mg alone. The main outcomes are hard clinical endpoints - death, stroke, MI, etc. Supposing that this trial is "positive" - that the combination (Vytorin) is superior to sinvastatin 40mg. Should patients now be on Vytorin (sinvastatin 40mg+ ezetimibe =patent-protected=expensive) instead of sinvastatin 80 mg (=generic=cheap)? Well, there will be no way to know based on this trial, which is exactly the way Schering-Plough wants it. You see, this trial was designed primarily for the purpose of securing patent protection for simvastatin in the combination pill. Its potential contribution to science and patient care is negligible. So much so in fact, that I think this trial is unethical. It is unethical because patients volunteer for research mainly out of altruism (although in this case you could argue it's for free drugs). The result of such altruism is expected to be a contribution to science and patient care in the future. But in this case, the science sucks and the main contribution patients are making goes to the coffers of Schering-Plough. Physicians should stop allowing their patients to participate in such trials, so that their altruism is not violated.)

The NYT article makes some suspicious and concerning observations:

• The data, expected to be available 6 months ago (the trial was completed almost 2 years ago!), will not be released until some time next year, and then only a partial dataset analysis, not complete data analysis.
• The primary endpoint was changed after the trial was concluded! (Originally it was going to be carotid IMT at three places, now only at one place - a change that is rich fodder for conspiracy theorists, regardless if an outside consulting agency suggested the change.)
• Data on femoral artery IMT are not going to be released at all now

Matthew Herper's Forbes article also notes that the trial was not listed on http://www.clinicaltrials.gov/ until Forbes asked why it was not there!

For the a priori trial design and pre-specified analyses, see pubmed ID # 15846260 at http://www.pubmed.org/ . In that report of the study's design, I do not see mention of monitoring of safety endpoints such as mortality and cardiovascular outcomes. But I presume these are being monitored for safety reasons. And Merck and Schering-Plough, who have claimed that they have not released the IMT data because it's taking longer than anticipated to analyze it, could certainly allay some of our concerns by releasing the data on mortality and safety endpoints, couldn't they? It doesn't take very long to add up deaths.

The problem with pre-specifying all these analyses (carotid IMT at 3 locations and femoral IMT) is that now you have multiple endpoints, and your chances of meeting one of them by chance alone is increased. That's why the primary endpoint holds such a hallowed position in the heirarchy of endpoints - it forces you to call your shot. I liken this to billiards where it doesn't matter how many balls you put down unless you call them. And none of them counts unless you first put down your first pre-specified ball - if you fail that, you lose your turn. In this case, if you check a bunch of IMTs, one of them might be significantly different based on chance alone - so if you change the primary endpoint after the study is done, we will rightly be suspicious that you changed it to the one that you saw was positive. That's bad science, and we and the editors of the journals should not let people get away with it.

I have a proposal: When you register a trial at http://www.clinicaltrials.gov/ , you should have to list a date of data/analysis release and a summary of the data/analyses that will be released. Should you not release the data/analysis by that pre-specified date, your ability to list or publish future trials, and your ability to seek or pursue regulatory approval for that or any other drug you have is suspended until you release the data. Moreover, you are forbidden from releasing the data/analyses prior to the pre-specified date - to prevent shenanigans with pre-specified list dates in the remote future, followed by premature release.

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Lung Transplantation: Exempt from the scrutiny of a randomized controlled trial?

In last week's NEJM, Liou et al in an excellent article analyzed pediatric lung transplant data and found that there is scant evidence for an improvement in survival associated with this procedure:
http://content.nejm.org/cgi/content/short/357/21/2143.

The authors seem prepared to accept the unavoidable metholodical limitations of their analyses and call for a randomized controlled trial (RCT) for pediatric lung transplantation. The editorialist, however, does not share their enthusiasm for a RCT, and appears to take it on faith that the new organ allocation scheme (whereby the sickest children get organs first) will make everything OK:
http://content.nejm.org/cgi/content/short/357/21/2186


True believers die hard. And because of their hardiness, an RCT will be difficult to perform, as many pediatric pulmonologists will be loathe to allow their patients to be randomized to no transplant. They have no individual equipoise, even though there appears to be collective equipoise among folks willing to give serious consideration to the available data.

What we have here may be an example of what I will call "action bias" - which is basically the opposite of omission bias. In omission bias, people fail to act even though outcomes from action are superior to those from omission - often as a result of reluctance to risk or cause direct harm even though direct benefits outweigh them in the net. Action bias, as the enantiomer of omission bias, would refer to causing worse outcomes through action because of the great reluctance to stand by helplessly while a patient is dying, even when the only "therapies" we can offer make patients worse off - save for the hope they offer, reason notwithstanding.

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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.

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Plavix Defeated: Prasugrel is superior in a properly designed and executed study

Published early on Sunday, November 5th in the NEJM (http://content.nejm.org/cgi/content/abstract/NEJMoa0706482v1) is a randomized controlled superiority trial comparing clopidogrel to a novel agent - Prasugrel.

Prasugrel was superior to Plavix. And it was superior to a degree similar to the degree to which Plavix is superior to aspirin alone. (See http://content.nejm.org/cgi/content/abstract/352/12/1179
and
http://content.nejm.org/cgi/content/abstract/345/7/494).

So therefore, by precedent, if one accepts the notion that aspirin alone is inferior to aspirin and Plavix because reductions in death and MI on the order of 2-3% are thought to be non-negligible (as I think they should be considered), one must therefore accept the notion that given the choice between Plavix and Prasugrel, one should choose the latter.



There is this issue of bleeding. But, eschewing your tendency towards omission bias, as I know you are wont to, you will agree that even if bleeding is as bad as death or MI (and it is NOT!), the net benefit of Prasugrel remains positive. Bleeding gums with dental flossing is annoying until you compare your life to your neighbor in cardiac rehab after his MI.

There is also the issue of Plavix's patent expiration in a few years. If the medications were equivalently priced, the choice is a no-brainer. If Prasugrel is costly and Plavix is generic, the calculus increases considerably in complexity - both from the perspective of the patient paying out of pocket, and the policy expert wielding his cost-effectiveness analysis. If my co-pay were the same, I would certainly choose Prasugrel. But if money is/were tight, I might consider that diet and excersise (which are free, financially, at least) may be a more cost-effective personal intervention than the co-pay for an expensive drug.

And what if Plavix at a higher dose is just as effective as Prasugrel? That question will have to be answered by future RCTs, which may be unlikely to happen if Plavix is about to lose patent protection...

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Post-exposure prophylaxis for Hepatitis A: Temptation seizes even the most well-intentioned authors

Victor et al report in the October 25th NEJM (http://content.nejm.org/cgi/content/abstract/357/17/1685) the non-inferiority of Hepatitis A vaccine to Immune Globulin for post-exposure prophylaxis of hepatitis A. The results are convincing for the non-inferiority hypothesis: symptomatic hepatitis A occurred in 4.4% of subjects who received vaccine versos 3.3% of subjects who received immune globulin (RR 1.35%; 95% CI .70-2.67).

This is a very well-executed non-inferiority study. If one looks at the methods section, s/he sees that the authors described very well their non-inferiority hypothesis and how it was arrived at. Given the low baseline rate of symptomatic hepatitis A (~3%), a RR of 3.0 is reasonable for non-inferiority, as non-inferiority implies<2%> non-significant trend toward less symptomatic Hepatitis A in the immune globlin group, the authors suggest that this agent may be preferred.

Again, one cannot have his cake and eat it too. One either conducts a non-inferiority trial and accepts non-inferior results as meaning that one agent is non-inferior to the alternative agent, or one conducts a superiority trial to demonstrate that one agent is truly superior. If the point estimates in this trial are close to correct, and immune globulin is 1.1% superior to HAV vaccine, ~7300 patients would be required in EACH group to determine superiority at a power of 90% and an alpha of 0.05. So the current trial is no substitute for a superiority trial with~7300 patients in each group. Unless such a trial is performed, HAV vaccine and immune globulin are non-inferior to each other for post-exposure prophylaxis to HAV, period.

To sum up: one either believes that two agents are non-inferior (or more conservatively, equivalent) and he therefore conducts a non-inferiority trial and accepts the results based on the a priori margins (delta) that he himself specified - or he conducts a superiority trial to demonstrate unequivocally that his preferred agent is superior to the comparator agent.

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Lanthanic Disease increasing because of MRI, reports NEJM

In this week's NEJM (http://content.nejm.org/cgi/content/short/357/18/1821) authors from the Netherlands report a large series of asymptomatic patients who had brain MRI scans. There was a [surprisingly?] large incidence of abnormalities, particularly [presumed] brain infarcts, the incidence of which [predictably] increased with age. This is a timely report given the proliferation and technical evolution of advanced imaging techniques, which we can expect to lead to the discovery of an increasing number of "abnormalities" in asymptomatic patients. As in the case of screening for lung cancer (http://jama.ama-assn.org/cgi/content/abstract/297/9/953?maxtoshow=&HITS=10&hits=10&RESULTFORMAT=&fulltext=computed+tomography&searchid=1&FIRSTINDEX=0&resourcetype=HWCIT), the benefits of early detection of an abnormality must be weighed against the cost of the technology and the diagnostic and therapeutic misadventures that result from pursuit of incidentalomas that are discovered. The psychological impact of the "knowledge" gained on patients must also be considered. Sometimes, ignorance truly is bliss, and therefore 'tis folly to be wise.

Lanthanic disease (with which I am familiar thanks to the sage mentorship of Peter B. Terry, MD, MA at Johns Hopkins Hospital) refers to incidentally discovered abnormalities in asymptomatic individuals. Not surprisingly, it generally is thought to have a better prognosis than disease that is discovered after symptoms develop, presumably because it is discovered at a less advanced stage or is behaving in a less sinister fashion.

The discovery of Lanthanic disease poses challenges for clinicians. Is the natural history of incidentally discovered disease different from what is classically reported? Should pre-emptive interventions be undertaken? What of the elderly female with mental status changes who presents to the ED and in whom a cortical infarct or SDH is discovered on an MRI? Can her current symptoms be attributed to the imaging abnormalities? Clinicians will do well to be aware of the high prevalence of asymptomatic abnormalities on such scans.

The authors' conclusions are perspicacious: "Information on the natural history of these lesions is needed to inform clinical management."

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CROs (Contract Reseaerch Organizations) denounced in the NEJM

This last week's NEJM contains a long-overdue expose on CROs (contract research organizations): http://content.nejm.org/cgi/content/short/357/14/1365 .

These organizations have one purpose: to carry out studies for the pharmaceutical industry in the most expeditious and efficient manner. The problem is that often, it is expeditious and efficient to compromise patient safety.

The article states the issue better than I could hope to. I will only comment that regardless of who is carrying out the actual clinical trial, that industry control of or involvement in the design of the trial is another MAJOR problem that must be addressed if we wish to search for the truth and protect study participant and subsequent patient safety in the study of novel pharmaceutical agents.

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Badly designed studies - is the FDA to blame?

On the front page of today's NYT (http://www.nytimes.com/2007/09/28/health/policy/28fda.html?ex=1348718400&en=30b7a25ac3835517&ei=5124&partner=permalink&exprod=permalink)
is an article describing a report to be released today by teh inspector general of the Department of Health and Human Service that concludes that FDA oversight of clinical trials (mostly for drugs seeking approval by the agency from the industry) is sorely lacking.

In it, Rosa DeLauro (D-CT) opines that the agency puts industry interests ahead of public health. Oh, really?

Read the posts below and you might be of the same impression. Some of the study designs the FDA approves for testing of agents are just unconscionable. These studies have little or no value for the public health, science, or patients. They serve only as coffer-fillers for the industry. Sadly, they often serve as coffin-fillers when things sometimes go terribly awry. Think Trovan. Rezulin. Propulsid. Vioxx.

The medical community, as consumers of these "data" and the resulting products, has an obligation to its patients which extends beyond those which we see in our offices. We should stop tolerating shenanigans in clinical trials, "me-too" drugs, and corporate profiteering at the expense of patient safety.

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Defaults suggested to improve healthcare outcomes

In today's NEJM (http://content.nejm.org/cgi/content/short/357/13/1340), Halpern, Ubel, and Asch describe the use of defaults to improve utilization of evidence-based practices. This strategy, which requires that we give up our status quo and omission biases (http://www.chestjournal.org/cgi/content/abstract/128/3/1497?maxtoshow=&HITS=10&hits=10&RESULTFORMAT=&author1=aberegg&searchid=1&FIRSTINDEX=0&sortspec=relevance&resourcetype=HWCIT ), could prove highly useful - if we have the gumption to follow their good advice and adopt it.

It is known that patients recieve only approximately 50% of the evidence-based therapies that are indicated in their care (see McGlynn et al: http://content.nejm.org/cgi/content/abstract/348/26/2635) and that there is a lag of approximately 17 years between substantial evidence of benefit of a therapy and its adoption into routine care.

Given this dismal state of affairs, it seems that the biggest risk is not that a patient is going to receive a defalut therapy that is harmful, wasteful, or not indicated, but rather that patients are going to continue to receive inadequate and incomplete care. The time to institute defaults into practice is now.

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Dueling with anideulafungin

Our letter to the editor of the NEJM regarding the anidulafungin article (described in a blog post in July - see below) was published today and can be seen at: http://content.nejm.org/cgi/content/short/357/13/1347 .

To say the least, I am disappointed in the authors' response, particularly in regards to the non-inferiority and superiority issues.

The "two-step" process they describe for sequential determination of non-inferiority followed by superiority is simply the way that a non-inferiority trial is conducted. Superiority is declared in a non-inferiority trial if the CI of the point estimate does not include zero. (See http://jama.ama-assn.org/cgi/content/abstract/295/10/1152?maxtoshow=&HITS=10&hits=10&RESULTFORMAT=&fulltext=piaggio&searchid=1&FIRSTINDEX=0&resourcetype=HWCIT .

The "debate" among statisticians that they refer to is not really a debate at all, but relates to the distinction between a non-inferiority trial and an equivalence trial - in the latter, the CI of the point estimate must not include negative delta; in this case that would mean the 95% CI would have to fall so far to the left of zero that it did not include minus 20, or the pre-specified margin of non-inferiority. Obviously, the choice of a non-inferiority trial rather than an equivalence trial makes it easier to declare superiority. And this choice can create, as it did in this case, an apparent contradiction that the authors try to gloss over by restating the definition of superiority they chose when designing the trial.

Here is the contradiction, the violation of logic. The drug is declared superior because the 95% CI does not cross zero, but of course, that 95% CI is derived from a point estimate, in this case 15.4%. So, 15.4% is sufficient for the drug to be superior. But if your very design implied that a difference less than 20% is clinically negligible (a requirement for the rational determination of a delta, a prespecified margin of non-inferiority), aren't you obliged by reason and fairness to qualify the declaration of superiority by saying something like "but, we think that a 15.4% difference is clinically negligible?"

There is no rule that states that you must qualify it in this way, but I think it's only fair. Perhaps we, the medical community, should create a rule - namely that you cannot claim superiority in a non-inferiority trial, only in an equivalence trial. This would prevent the industry from getting one of the "free lunches" they currently get when they conduct these trials, and the apparent contradictions that sometimes arise from them.

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Lilly, Xigris, the XPRESS trial and non-inferiority shenanigans

The problem with non-inferiority trials (in addition to the apparent fact that the pharmaceutical industry uses them to manufacture false realities) is that people don't generally understand them (which is what allows false realities to be manufactured and consumed.) One only need look at the Windish article described below to see that the majority of folks struggle with biomedical statistics.

The XPRESS trial, published in AJRCCM Sept. 1st, (http://ajrccm.atsjournals.org/cgi/content/abstract/176/5/483) was mandated by the FDA as a condition of the approval of drotrecogin-alfa for severe sepsis. According to the authors of this study, the basic jist is to see if heparin interferes with the efficacy of Xigris (drotrecogin-alfa) in severe sepsis. The trial is finally published in a peer-reviewed journal, although Lilly has been touting the findings as supportive of Xigris for quite a while already.


The stated hypothesis was that Xigris+placebo is equivalent to Xigris+heparin (LMWH or UFH). [Confirmation of this hypothesis has obvious utility for Lilly and users of this drug because it would allay concerns of coadministration of Xigris and heparinoids, the use of the latter which is staunchly entrenched in ICU practice).

The hypothesis was NOT that Xigris+heparin is superior to Xigris alone. If Lilly had thought this, they would have conducted a superiority trial. They did not. Therefore, they must have thought that the prior probability of superiority was low. If the prior probability of a finding (e.g., superiority) is low, we need a strong study result to raise the posterior probability into a reasonable range - that is, a powerful study which produces a very small p-value (e.g., <0.001)>

This study used 90% confidence intervals. Not appropriate. This is like using a p-value of 0.10 for significance. I have calculated the more appropriate 95% CIs for the risk difference observed and they are: -0.077 to +0.004.

The analysis used was intention to treat. The more conservative method for an equivalence trial is to present the results as "as treated". This could be done at least in addition to the ITT analysis to see if the results are consistent.

Here we are doing an equivalence trial with mortality as an outcome. This requires us to choose a "delta" or mortality difference between active treatment and control which is considered to be clinically negligible. Is an increased risk of death of 6.2% negligible? I think not. It is simply not reasonable to conduct a non-inferiority or equivalence trial with mortality as the outcome. Mortality differences would have to be, I would say, less than 1% to convince me that they might be negligible.

Because an equivalence design was chosen, the 95% CIs (90% if you're willing to accept that -and I'm not) for the treatment difference would have to fall entirely outside of delta (6.2%) in order for treatment to be declared superior to placebo. Clearly it does not. So any suggestion that Xigris+heparin is superior to Xigris alone based on this study is bunkum. Hogwash. Tripe. Based upon the chosen design, superiority is not even approached. The touted p-value of 0.08 conceals this fact. If they had chosen an superiority design, yes, they would have been close. But they did not.

Equivalence was not demonstrated in this trial either, as the 95% (and the 90%) CIs crossed the pre-specified delta. So sorry.

The design of this study and its very conception as an equivalence trial with a mortality endpoint is totally flawed. Equivalence was not demonstrated even with a design that would seem to favor its demonstration. (Interestingly, if a non-inferiority design had been chosen, superiority of Xigris+heparin would in fact have been demonstrated! [with 90, but NOT with 95% CIs] ).

The biggest problem I'm going to have is when the Kaplan-Meier curve presented in Figure 3A with its prominently featured "near miss" p-value of 0.09 is used as ammunition for the argument that Xigris+heparin trended toward superior in this study. If it had been a superiority trial, I would be more receptive of that trend. But you can't have your cake and eat it too. You either do a superiority trial, or you do an equivalence trial. In this case, the equivalence trial appeared to backfire.

Having said all that, I think we can be reassured that Xigris+heparin is not worse than Xigris+placebo and the concern that heparin abrogates the efficacy of Xigris should be mostly dispelled. And because almost all critically ill patients are at high frisk of DVT/PE, they should all be treated with heparinoids, and the administration of Xigris should not change that practice.

I just think we should stop letting folks get away with these non-inferiority/equivalence shenanigans. In this case, there is little ultimate difference. But in many cases a non-inferiority or equivalence trial such as this will allow the manufacture of a false reality. So I'll call this a case of "attempted manufacture of a false reality".

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Medical Residents Don't Understand Statistics

But they want to: http://jama.ama-assn.org/cgi/content/abstract/298/9/1010

This is but one of many unsettling findings of an excellent article by Windish et al in the September 5th issue of JAMA.

Medical residents correctly answer only approximately 40% of questions pertaining to basic statistics related to clinical trials. Fellows and general medicine faculty with research training fared better statistically, but still have some work to do: they answered correctly approximately 70% of the questions.

An advanced degree in addition to a medical degree conferred only modest benefit: 50% answered correctly rather than 40%.


The solution to this apparent problem is therefore elusive. Even if we encouraged all residents to pursue advanced degrees or research training, we would still have vast room for improvement in the understanding of basic biomedical statistics. And this is not a realistic expectation (that they all pursue advanced degrees or research training).

While it would appear that directed training in medical statistics might have a beneficial effect on performance of this test, with work hours restrictions and the daunting amount of material they must already master for the practice of medicine, it seems unlikely that a few extra courses in statistics during residency is going to make a large and sustainable difference.

Moreover, we must remember that performance on this test is a surrogate outcome - what we're really interested in is how they practice medicine with whatever skills they have. My anecdotal experience is that few physicians are actually keeping abreast of the medical literature - few are actually reading the few journals that they subscribe to - so improving their medical evidence interpretation skills is going to have little impact on how they practice. (For example, few of my colleagues were aware of the Windish article itself, in spite of their practice in an academic center, its publication in a very high impact journal, and their considerable luxury of time compared to our colleagues in private practice.)

In some ways, the encouragement that the average physician critically evaluate the medical literature seems like a far-fetched and idyllic notion. This may be akin to expecting them to stay abreast of the latest technology for running serum specimens, PCR machines, or to the sensitivity and specificity of various assays for BNP - they just don't have the time or the training to bother with nuances such as these, which are better left to the experts in the clinical and research laboratories. Likewise, it may be asking too much in the current era of medicine to expect that the average physician will possess and maintain biostatistical and trial analysis skills, consistently apply them to emerging literature, and change practice promptly and accordingly. Empirical evidence suggests that this is not happening, and I don't think it has much to do with lack of statistical skills - it has to do with lack of time.

Perhaps what Windish et al have reinforced is support for the notion that individual physicians should not be expected to keep abreast of the medical literature, but should instead rely upon practice guidelines formulated by those experts properly equipped and compensated to appraise and make recommendations about the emerging evidence.

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Idraparinux, the van Gogh investigators, and clinical trials pointillism: connecting the dots shows that Idraparinux increases the risk of death

It eludes me why the NEJM continues to publish specious, industry-sponsored, negative, non-inferiority trials. Perhaps they do it for my entertainment. And this past week, entertained I was indeed.

Idraparinux is yet another drug looking for an indication. Keep looking, Sanofi. Your pipeline problems will not be solved by this one.

First, let me dismiss the second article out of hand: it is not fair to test idraparinux against placebo (for the love of Joseph!) for the secondary prevention of VTE after a recent epidode! (http://content.nejm.org/cgi/content/short/357/11/1105).

It is old news that one can reduce the recurrence of VTE after a recent episode by either using low intensity warfarin (http://content.nejm.org/cgi/content/abstract/348/15/1425) or by extending the duration of warfarin anticoagulation (http://content.nejm.org/cgi/content/abstract/345/3/165). Therefore, the second van Gogh study does not merit further consideration, especially given the higher rate of bleeding in this study.


Now for the first study and its omissions and distortions. It is important to bear in mind that the only outcome that cannot be associated with ascertainment bias (assuming a high follow-up rate) is mortality, AND that the ascertainment of DVT and PE are fraught with numerous difficulties and potential biases.

The Omission: Failure to report in the abstract that Idraparinux use was associated with an increased risk of death in these studies, which was significant in the PE study, and which trended strongly in the DVT study. The authors attempt to explain this away by suggesting that the increased death rate was due to cancer, but of course we are not told how causes of death were ascertained (a notoriously difficult and messy task), and cancer is associated with DVT/PE which is among the final common pathways of death from cancer. This alone, this minor factoid that Idraparinux was associated with an increased risk of death should doom this drug and should be the main headline related to these studies.

Appropriate headline: "Idraparinux increases the risk of death in patients with PE and possibly DVT."

If we combine the deaths in the DVT and PE studies, we see that the 6-month death rates are 3.4% in the placebo group and 4.5% in the idraparinux group, with an overall (chi-square) p-value of 0.035 - significant!

This is especially worrisome from a generalizability perspective - if this drug were approved and the distinction between DVT and PE is blurred in clinical practice as it often is, we would have no way of being confident that we're using it in a DVT patient rather than a PE patient. Who wants such a messy drug?

The Obfuscations and Distortions: Where to begin? First of all, no justification of an Odds Ratio of 2.0 as a delta for non-inferiority is given. Is twice the odds of recurrent DVT/PE insignificant? It is not. This Odds Ratio is too high. Shame.

To give credit where it is due, the investigation at least used a one sided 0.025 alpha for the non-inferiority comparison.

Second, regarding the DVT study, many if not the majority of patients with DVT also have PE, even if it is subclinical. Given that ascertainment of events (other than death) in this study relied on symptoms and was poorly described, that patients with DVT were not routinely tested for PE in the absence of symptoms, and that the risk of death was increased with idraparinux in the PE study, one is led to an obvious hypothesis: that the trend towary an increased risk of death in the DVT study patients who received idraparinux was due to unrecognized PE in some of these patients. The first part of the conclusion in the abstract "in patients with DVT, once weekly SQ idraparinux for 3 or 6 months had an efficacy similar to that of heparin and vitamin K antagonists" obfuscates and conceals this worrisome possibility. Many patients with DVT probably also had undiagnosed PE and might have been more likely to die given the drug's failure to prevent recurrences in the PE study. The increased risk of death in the DVT study might have been simply muted and diluted by the lower frequency of PE in the patients in the DVT study.

Then there is the annoying the inability to reverse the effects of this drug with a very long half-life.

Scientific objectivity and patient safety mandate that this drug not receive further consideration for clinical use. Persistence with the study of this drug will most likely represent "sunk cost bias" on the part of the manufacturer. It's time to cut bait and save patients in the process.

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More on Prophylactic Cranial Irradiation

One of our astute residents at OSU (Hallie Prescott, MD) wrote this letter to the editor of the NEJM about the Slotman article discussed 2 weeks ago - unfortunately, we did not meet the deadline for submission, so I'm posting it here:

Slotman et al report that prophylactic cranial irradiation (PCI) increases median overall survival (a secondary endpoint) by 1.3 months in patients with small cell lung cancer. There were no significant differences in various quality of life (QOL) measures between the PCI and control groups. However, non-significant trends toward differences in QOL measures are noted in Table 2. We are not told the direction of these trends, and low compliance (46.3%) with QOL assessments at 9 months limits the statistical power of this analysis. Moreover, significant increases in side effects such as fatigue, nausea, vomiting, and leg weakness may limit the attractiveness of PCI for many patients. Therefore, the conclusion that “prophylactic cranial irradiation should be part of standard care for all patients with small-cell lung cancer” makes unwarranted assumptions about how patients with cancer value quantity and quality of life. The Evidence-Based Medicine working group has proposed that all evidence be considered in light of patients’ preferences, and we believe that this advice applies to PCI for extensive small cell lung cancer.


References

1. Slotman B, Faivre-Finn C, Kramer G, Rankin E, Snee M, Hatton M et al. Prophylactic Cranial Irradiation in Extensive Small-Cell Lung Cancer. N Engl J Med 2007; 357(7):664-672.
2. Weeks JC, Cook EF, O'Day SJ, Peterson LM, Wenger N, Reding D et al. Relationship Between Cancer Patients' Predictions of Prognosis and Their Treatment Preferences. JAMA 1998; 279(21):1709-1714.
3. McNeil BJ, Weichselbaum R, Pauker SG. Speech and survival: tradeoffs between quality and quantity of life in laryngeal cancer. N Engl J Med 1981; 305(17):982-987.
4. Voogt E, van der Heide A, Rietjens JAC, van Leeuwen AF, Visser AP, van der Rijt CCD et al. Attitudes of Patients With Incurable Cancer Toward Medical Treatment in the Last Phase of Life. J Clin Oncol 2005; 23(9):2012-2019.
5. Guyatt GH, Haynes RB, Jaeschke RZ, Cook DJ, Green L, Naylor CD et al. Users' Guides to the Medical Literature: XXV. Evidence-Based Medicine: Principles for Applying the Users' Guides to Patient Care. JAMA 2000; 284(10):1290-1296.

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Prophylactic Cranial Irradiation: a matter of blinding, ascertainment, side effects, and preferences

Slotman et al (August 16 issue of NEJM: http://content.nejm.org/cgi/content/short/357/7/664) report a multicenter RCT of prophylactic cranial irradiation for extensive small cell carcinoma of the lung and conclude that it not only reduces symptomatic brain metastases, but also prolongs progression-free and overall survival. This is a well designed and conducted non-industry-sponsored RCT, but several aspects of the trial warrant scrutiny and temper my enthusiasm for this therapy. Among them:

The trial is not blinded (masked is a more sensitive term) from a patient perspective and no effort was made to create a sham irradiation procedure. While unintentional unmasking due to side effects may have limited the effectiveness of a sham procedure, it may not have rendered it entirely ineffective. This issue is of importance because meeting the primary endpoint was contingent on patient symptoms, and a placebo effect may have impacted participants’ reporting of symptoms. Some investigators have gone to great lengths to tease out placebo effects using sham procedures, and the results have been surprising (e.g., knee arthroscopy; see: https://content.nejm.org/cgi/content/abstract/347/2/81?ck=nck).


We are not told if investigators, the patient’s other physicians, radiologists, and statisticians were masked to the treatment assignment. Lack of masking may have led to other differences in patient management, or to differences in the threshold for ordering CT/MRI scans. We are not told about the number of CT/MRI scans in each group. In a nutshell: possible ascertainment bias (see http://www.consort-statement.org/?o=1123).

There are several apparently strong trends in QOL assessments, but we are not told what direction they are in. Significant differences in these scores were unlikely to be found as the deck was stacked when the trial was designed: p<0.01 was required for significance of QOL assessments. While this is justified because of multiple comparisons, it seems unfair to make the significance level for side effects more conservative than that for the primary outcome of interest (think Vioxx here). The significance level required for secondary endpoints (progression-free and overall survival) was not lowered to account for multiple comparisons. Moreover, more than half of QOL assessments were missing by 9 months, so this study is underpowered to detect differences in QOL. It is therefore all the more important to know the direction of the trends that are reported.

The authors appear to “gloss over” the significant side effects associated with this therapy. It made some subjects ill.

If we are willing to accept that overall survival is improved by this therapy (I’m personally circumspect about this for the above reasons) the bottom line for patients will be whether they would prefer on average 5 additional weeks of life with nausea, vomiting weight loss, fatigue, anorexia, and leg weakness to 5 fewer weeks of life without these symptoms. I think I know what choice many will make, and our projection bias may lead us to make inaccurate predictions of their choices (see Lowenstein, Medical Decision Making, Jan/Feb 2005: http://mdm.sagepub.com/cgi/content/citation/25/1/96).

The authors state in the concluding paragraph:

“Prophylactic cranial irradiation should be part of standard care for all patients with small-cell lung cancer who have a response to initial chemotherapy, and it should be part of the standard treatment in future studies involving these patients.”

I think the decision to use this therapy is one that only patients are justified making. At least now we have reasonably good data to help them inform their choice.

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Thalidomide, Phocomelia, and Lessons from History

In tracing the history of evidence-based medicine tonight (for a lecture I have to give on Friday), a found the story of thalidomide on wikipedia (http://en.wikipedia.org/wiki/Thalidomide ).

(While I recognize that the information provided on this site is uncorroborated, I also recognize that it has been referenced by Federal Distric Courts in various decisions - see http://www.nytimes.com/2007/01/29/technology/29wikipedia.html?ex=1186545600&en=4e6683fb4fac3044&ei=5070 - so I consider it possibility generating rather than evidence corroborating.)

This story is a tragic one of a company with a product to sell (a "treatment looking for an indication" - hmmm...) and its unscrupulous marketing of this product in the absence of evidence of both safety and efficacy.

The story of Thalidomide should serve as a stark and poignant reminder of the potential harmful effects of a marketing campaign, impelled by profiteering, gone awry.

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AVANDIA and Omission Bias

Amid all the hype about Avandia recently, a few relatively clear-cut observations are apparent (most of which are described better than I could hope to do in the July 5 issue of NEJM. Drazen et al, Dean, and Psaty each wrote wonderful editorials available at www.nejm.org).

1.) Avandia appears to have NO benefits besides the surrogate endpoint of improved glycemic control (and engorging the coffers of GSK, the manufacturer).

2.) Avandia may well increase the risk of CHF, MI, raise LDL cholesterol, cause weight gain and increase the risk of fractures (the latter in women).

3.) Numerous alternative agents exist, some of which improve primary outcomes (think UKPDS and metformin), and most of which appear to be safer.

So, what physician in his right mind would start a patient on Avandia (especially in light of #3)? And if you would not START a patient on Avandia, then you should STOP Avandia in patients who are already taking it.


To not do so would be to commit OMISSION BIAS - which refers to the tendency (in medicine and in life) to view the risks and/or consequences of doing nothing as superior to the risks and/or consequences of acting, even when the converse is true (i.e., the risks and/or consequences of acting are superior to those related to inaction). (For a reference, indulge me: Aberegg et al http://www.chestjournal.org/cgi/content/abstract/128/3/1497.)

This situation is reminiscent of recommendations relating to the overall (read "net") health benefits of ethanol consumption - physicians are told to not discourage moderate alcohol consumption in patients who already consume, but not to encourage it in those who currently abstain. Well, alcohol is either good for you, or it is not. And since it appears to be good for you, the recommendation on its consumption should not hinge one iota on an arbitrarily established status quo (whether for reasons completely unrelated to health a person currently drinks).
(For a reference, see Malinski et al: http://archinte.ama-assn.org/cgi/content/abstract/164/6/623; the last paragraph in the discussion could serve as an expose on omission bias.)

So, let me go out on a limb here: Nobody should be taking Avandia, and use of this medication should not resume until some study demonstrates a substantive benefit in a meaningful outcome which outweighs any risks associated with the drug. Until we do this, we are the victims of OMISSION BIAS (+/- status quo bias) and the profiteering conspiracy of GSK which is beautifully alluded to, along with a poignant description of the probably intentional shortcomings in the design and conduct of the RECORD trial here: Psaty and Furberg http://content.nejm.org/cgi/content/extract/356/24/2522.

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Secondary Endpoints, Opportunity Costs, Alternatives, Vioxx, Avandia, and Actos

There are few endpoints that can hold a candle to mortality as the end-all, be-all of clinical trials design, but two appear to be fit for the challenge, (at least according to past FDA decisions) - or are they? Blood Pressure lowering and glycemic control.



It is old news that Vioxx kills people, and does so utterly unnecessarily: alternative treatments are available that are generic, low cost, and have no toxicities that are demonstrably greater than Vioxx (despite Big Pharma inuendo to the contrary - you know, GI toxicity and the like).



(I am reminded of cognitive dissonance theory here - originally described by Alport, 1938; It has been demonstrated that folks who are more harshly hazed by a fraternity have greater allegence to it.....could this be one of the reasons why paying big bucks for a prescription NSAID with no demonstrable benefits over OTC generics leads to patient claims of superiority of the branded product?)



Well, the old news is still being published: http://content.nejm.org/cgi/content/full/357/4/360 .

The interesting thing to me about the Vioxx story is that with alternatives available (you know, Aleve, Mortin, and the like), and in relation to a "lifestyle drug," safety was not given greater weight. If your primary endpoint is mortality, you might allow an MI or two in your dataset (although you should report them). But when your endpoint is "confirmed clinical upper gastrointestinal events " (http://content.nejm.org/cgi/content/full/343/21/1520), perhaps closer attention ought to be paid to the side effects you have to pay in order to receive the benefits of the primary endopint. If no other NSAIDS were available to treat patients with crippling arthritis, that would be one thing (think IBS: Alosetron withdrawn and then reintroduced to the market because of lack of a suitable alternative; http://content.nejm.org/cgi/content/full/349/22/2136). But there were alternatives and this was a lifestyle drug....



And now we have the Avandia debacle, which, surprisingly, did not lead to a recommendation for withdrawl of this drug from teh US markey by the recent FDA advisiory panel (http://sciencenow.sciencemag.org/cgi/content/full/2007/730/1). Once again, it seems this decision, if made by a rational agent, would have given due consideration to whether there are alternative agents that might be used in place of Avandia if it were no longer available. Well, sure enough, in addition to metformin (think UKPDS), and insulin, and other oral hyopglycemics, lo and behold: Pioglitazone.

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The Swan Ganz graces the pages of JAMA yet again

The debate on the Swan Ganz catheter continues, this time spurred by a well done report documenting declining use of the catheter over the last decade, the results of an analysis of an administrative database (available at http://jama.ama-assn.org/cgi/content/short/298/4/423 ).

The arguments used in this debate continue to befuddle me with their obvious lack of logical consistency with many other things that are going on apparently unnoticed around us, and about which no fuss is being made. I will enumerate some of these here.


1.) An air of derision often accompanies denouncements of the Swan Ganz catheter because it is "invasive". This buzz word, however, carries little consequence in reality. That something is "invasive" does not necessarily mean that it is riskier than other things that are done that are "non-invasive". Administration of Cytoxan or other chemotherapeutic agents is not "invasive" by the common definition of the term, yet is clearly very risky. Other analogies abound. I am not convinced by hyperbolic statements of "invasiveness" that are not supported by actual negative consequences of the device that exceed other risks which we routinely take (and take for granted) in medicine.

2.) And what are the actual negative consequences? In the FACTT trial of ARDSnet, the only adverse consequence was transient arrythmias. I remain unconvinced.

3.) What OTHER "invasive" (their definition, not mine) things do we routinely do that have no proven mortality benefit? How about arterial lines, or many (most?) central lines? Why is not the critical care (especially the academic critical care) community rallying against those, if it is invasive devices of unproven [mortality] benefit that we are concerned with?

4.) Why must this device, unlike almost all other devices and diagnostic modalities, demonstrate a mortality benefit in order to qualify for our acceptance? Must the ECHOcardiogram (within the ICU or without) reduce mortality for its use to be justified? Not invasive, no risks, doesn't count you say. OK, how about CT angiogram? There are increasing data about the carcinogenecity of radiation from CT scans (Lee et al, 2004, Health Policy and Practice, "Diagnostic CT Scans..", available at: http://radiology.rsnajnls.org/cgi/reprint/231/2/393.pdf), and there is not insubstantial renal morbidity and risk of anaphylactoid reactions to the dye. Yet we evaluate the CT angiogram on the basis of its ability to identify pulmonary emboli (sensitivity and specificity and the like), not to reduce mortality (and meanwhile we largely ignore the risks or accept them as the costs of diagnosis). How many patients would be required to conduct such a study of mortality reduction with CT angiogram? Is there a study in existence of a diagnostic modality the use of which improves mortality? Is there precedent for such a thing? Should it surprise us that intervening more proximally (diagnosis rather than treatment) in a clinical pathway makes it harder (or impossible) to demonstrate a benefit further downstream?

5.) Let's extend the analogy. Suppose we were to design a study of routine use of CT angiogram in the ICU for this or that indication, let's say sudden unexplained hypoxemia. Suppose also that this study shows no benefit (mortality or otherwise) of routine use in this patient population. Does this mean that I should stop using CT angiogram on a selective basis, as those who call for a moratorium imply I should do with the Swan?

6.) If the arterial line analogy was not sufficient, because there was not a recent study demonstrating a lack of mortality benefit with this device, we have an alternative candidate: the Canadian Critical Care Trials Group study of ("invasive") BAL for the diagnosis of VAP published in the NEJM in December ( http://content.nejm.org/cgi/content/abstract/355/25/2619 ). No rallying cry, no proposed moratorium followed this extermely well conducted trial. No denouncement of BAL in the editorial (http://content.nejm.org/cgi/content/extract/355/25/2691). Quite the contrary - the exclusion of patients with staph and pseudomonas was construed as all but undermining the validity of the results for application to clinical practice. At my own institution, pre-existing staunch enthusiasm for BAL diagnosis of VAP has not wavered since publication of this trial.

I am no Swan Ganz apologist, and I rarely use the device. But the state of the debate and the arguments used to denounce the Swan do not stand the test of logic or consistency that I expect of the critical care community. And this leads me to believe that these arguments are the spawn of idealogy and sanctimoniousness, rather than logic and balanced consideration.

An afterthought - Perhaps the most obvious moratorium for the academic community to call for is a moratorium on clinical trials of the Swan. They continue to be performed long after it became clear, meta-analytically, that it will be impossible to show a convincing positive result. The prior probability is now prohibitively low for any reasonably-sized trial to move the posterior away from the prior or sway the results of a meta-analysis.

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The WAVE trial: The Canadians set the standard once again

Today's NEJM contains the report of an exemplary trial (the WAVE trial) comparing aspirin to aspirin and warfarin combined in the prevention of cardiovascular events in patients with peripheral vascular disease (http://content.nejm.org/cgi/reprint/357/3/217.pdf). Though this was a "negative" trial in that there was no statistically significant difference in the outcomes between the two treatment groups, I am struck by several features of its design that are worth mentioning.

Although the trial was the beneficiary of pharmaceutical funding, the authors state:

"None of the corporate sponsors had any role in the design or conduct of the trial, analysis of the data, or preparation of the manuscript".

Ideally, this would be true of all clinical trials, but right now it's a precocious idea.



One way to remove any potential or perceived conflicts of interest might be to mandate that no phase 3 study be designed, conducted, or analyzed by its sponsor. Rather, phase 3 trials could be funded by a sponsor, but are mandated to be designed, conducted, analyzed, and reported by an independent agency consisting of clinical trials experts, biostatisticians, etc. Such an agency might also receive infrastructural support from governmental agencies. It would have to be large enough to handle the volume of clinical trials, and large enough that a sponsor would not be able to know to what ad hoc design committee the trial would be assigned, thereby preventing unscrupulous sponsors from "stacking the deck" in favor of the agent in which they have an interest.

The authors of the current article also clearly define and describe inclusion and exclusion criteria for the trial, and these are not overly restrictive, increasing the generalizability of the results. Moreover, the ratinoale for the parsimonious inclusion and exclusion criteria are intuitively obvious, unlike some trials where the reader is left to guess why the authors excluded a particular subgroup. Was it because it was thought that the agent would not work in that group? Because increased risk was expected in that group? Because study was too difficult (ethically or logistically) in that group (e.g., pregnancy). Inadequate justification of inclusion and exclusion criteria make it difficult for practitioners to determine how to incorporate the findings into clinical practice. For example, were pregnant patients excluded from trials of therapeutic hypothermia after cardiac arrest (http://content.nejm.org/cgi/reprint/346/8/549.pdf) for ethical reasons, because of an increased risk to the mother or fetus, because small numbers of pregnant patients were expected, because the IRB frowns upon their inclusion or for some other reason? Without knowing this, it is difficult to know what to do with a pregnant woman who is comatose following cardiac arrest. Obviously, their lack of inclusion in the trial does not mean that this therapy is not efficacious for them (absense of evidence is not evidence of absense). If I knew that they were excluded because of a biologically plausible concern for harm to the fetus (and I can think of at least one) rather than because of IRB concerns, I would be better prepared to make a decision about this therapy when faced with pregnant patient after cardiac arrest. Improving the reporting and justification of inclusion and exclusion criteria should be part of efforts to improve the quality of reporting of clinical trials.

Interestingly, the authors also present an analysis of the composite endpoints (coprimary endpoints 1 and 2) that excludes fatal bleeding or hemorrhagic stroke. When these side effects are excluded from the composite endpoints, there is a trend favoring combination therapy (p values 0.11 and 0.09 respectively). Composite endpoints are useful because they allow a trial of a given number of patients to have greater statistical power, and it is rational to include side effects in them, as side effects reduce the net value of the therapy. However, an economist or a person versed in expected utility theory (EUT) would say that it is not fair to combine these endpoints without first weighting them based on their relative (positive or negative value). Not weighting them implies that an episode of severe bleeding in this trial is as bad (negative value or utility) as a death - a contention that I for one would not support. I would much rather bleed than die, or have a heart attack for that matter. Bleeding can usually be readily and effectively treated.

In the future, it may be worthwhile to think more about composite endpoints if we are really interested in the net value/utility of a therapy. While it is often difficult to assign a relative value to different outcomes, methods (such as standard gambles) exist and such assignment may be useful in determining the true net value (to society or to a patient) of a new therapy.

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Anidulafungin - a boon for patients, physicians, or Big Pharma?

The June 14th edition of the NEJM (http://content.nejm.org/cgi/content/short/356/24/2472) contains an article describing a trial of anidulafungin, a new echinocandin antifungal agent similar to the more familiar caspofungin, in invasive candidiasis. The comparator agent was fluconazole. This is a proprietary agent, and the study was was fully funded by the pharmaceutical sponsor.

The trial was a non-inferiority trial, and the chosen "delta" (the treatment difference which was determined to be clinically insignificant) was 20%. This means that the authors would consider a difference in clinical response between the 2 agents of 19% to be clinically insignificant. No justification for this delta was provided, as is recommended (http://jama.ama-assn.org/cgi/content/abstract/295/10/1152?maxtoshow=&HITS=10&hits=10&RESULTFORMAT=&fulltext=non-inferiority&searchid=1&FIRSTINDEX=0&resourcetype=HWCIT). It is not clear if clinicians agree with this implicit statement of clinical insignificance, and no poll has been taken to determine if they do.


Which begs a question: should there be a requirement that clinicians be polled to determine what THEY, rather than the study sponsors think is a clinically insignificant difference? After all, clinicians are the folks who will be using the drug (if it is approved by the FDA.)

The design of non-inferiority trials is, in my experience, poorly understood among clinicians, and this may be due to inadequate reporting as reported in the above article and in this one (http://jama.ama-assn.org/cgi/content/abstract/295/10/1147?maxtoshow=&HITS=10&hits=10&RESULTFORMAT=&fulltext=equivalence&searchid=1&FIRSTINDEX=0&resourcetype=HWCIT).

Interestingly the difference in the agents favored anidulafungin by 15.4%, a difference that the authors did not emphasize as clinically insignificant.

I am left wondering if individual patients or society are better off now that we have another drug of the echinocandin class available. I would be more convinced that they were if anidulafungin had been compared to 800 mg of fluconazole (rather than 400 mg) or to caspofungin, but alas, it was not. I don't know what the cost of developing and testing this drug was, but I expect that it was on the order of tens to hundreds of millions of dollars - not to mention the costs of subsequent testing, advertising and marketing.

And the opportunity costs - the other possibilities. What else could have been done with that money that may have benefited individual patients or society more than another echinocandin agent?

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The Medical Evidence Blog - Introduction and Goals

The goals of this blog are manifold. I will list a few of them below. Hopefully it will serve as a forum to discuss:

• Emerging evidence in medicine
• The design, conduct, analysis, and reporting of clinical trials evidence
• Shenanigans perpetrated by investigators and pharmaceutical companies in the design, conduct, analysis, and reporting of clinical trials the impetus behind which appears to be something other than a search for the truth
• The expected impact of emerging evidence on clinical practice and patient care
• The value of new evidence to individual patients and society
• Underutilization of emerging and available evidence and therapies
• Biases in the interpretation of clinical trials evidence

Given these goals, I feel compelled to admit my own potential conflicts of interest. First, my research focus is on biases in the interpretation of clinical trials evidence, and my career stands to benefit from success in this line of research. Second, I have received and continue to receive speaker fees from Eli Lilly in relation to their promotion of the drug drotrecogin-alfa.

I think the best thing to do is to just "dive in" - so for the next post I will open discussion about a recent NEJM article....

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