When I wrote about the Trial to Assess Chelation Therapy (TACT) trial last week, little did I suspect that I would be revisiting the topic again so soon. For those of you not familiar with TACT, it was a trial designed to test a favorite quack treatment for cardiovascular disease, chelation therapy. It is, as I have described many times in the past, an incredibly implausible therapy based on a hugely simplistic concept that because calcium accumulates in atherosclerotic lesions, then using chelation therapy could remove the calcium and reduce the lesions. Chelation therapy is a favorite treatment option recommended by naturopaths, and the claims made for it border on the absurd. It's frequently referred to as a "Roto Rooter" for the arteries that is a "safe and effective" alternative to angioplasty or coronary artery bypass.
The first time I wrote about the results of TACT, its principal investigator Gervasio Lamas, MD, a professor of clinical medicine at the Columbia University Division of Cardiology and Chairman of Medicine at Mount Sinai Medical Center had just presented part of the trials results at the American Heart Association’s annual meeting back in November. As I noted at the time, the results were at best underwhelming, particularly given the methodological flaws. Basically, there was only a statistically significant difference between groups detected on subgroup analysis of diabetics, and there was no detectable difference in quality of life issues no matter how much Lamas tried to slice and dice the data. The next time around was a mere two weeks ago, when at the American College of Cardiology Meeting Lamas, apparently in pursuit of grinding out as many minimally publishable units (MPUs) as he could (or maybe I should say minimal presentable units), presented the results of the part of the study dealing with the high dose multivitamin and mineral solution that naturopaths so frequently like to administer with their chelation brew. As I explained again, the results were similarly underwhelming. Then, earlier this week, TACT was published online in JAMA. So underwhelming were the results again that I hadn't planned on blogging the study, given how extensively I've already written about it.
Then I saw a post over on Forbes by Harlan Krumholz entitled Chelation Therapy: What To Do With Inconvenient Evidence, and, oh, Lordy, I realized that I had no choice but to jump back into the breach and discuss the study some more because Dr. Krumholz's post was in essence a broadside against science and all those nasty skeptics who, to him, won't accept valid scientific results. It was painful to read and a big disappointment for Forbes given that my good bud Peter Lipson blogs at Forbes. Of course, my good bud Peter immediately (and correctly) took Dr. Krumholz to task for his misguided bloviation about TACT and us supposedly "close-minded" skeptics who won't accept "inconvenient" evidence. How could he resist? After all, Dr. Krumholz begins with a massive straw man:
What do we do with inconvenient evidence? Imagine studying a seemingly absurd practice that is used to an alarming extent by those who believe in it despite the lack of evidence – and finding that the intervention improves outcomes. And imagine that the people conducting that trial are famous scientists with impeccable credentials who have extensive experience with this type of investigation. Imagine that the practice is so out of the mainstream that the investigators cannot even posit how the treatment could reduce patient risk?
We live in a world of evidence-based medicine, where we are urged to base our medical recommendations and decisions on clinical studies. We base our guidelines on the medical literature and evaluate our practices by how well we adhere to the evidence. But what should we do with inconvenient evidence?
What indeed? The implication is that critics of TACT are questioning and rejecting the results because they are having trouble dealing with the results of a trial that seems to support a therapy that they find absurd. The problem, of course, is that is a simplification that is so massive that it's either intentional or reveals that Dr. Krumholz is almost completely unfamiliar with TACT, the sheer unethical design of the study, and the well-described problems with many of the sites at which the study were carried out, which were described in detail by Dr. R. W. Donnell in his most excellent Magical Mystery Tour of NCCAM Chelation Study Sites (part 1, part 2, part 3, part 4, part 5, part 6, part 7). I urge Dr. Krumholz to read all seven parts. As Dr. Donnell points out, only 12 of the 110 TACT study sites were academic medical centers. Many of the study sites were highly dubious clinics touting highly dubious therapies, including heavy metal analysis for chronic fatigue, intravenous infusions of vitamins and minerals (I could never figure out how infusing minerals could be reconciled with chelation therapy to remove minerals, but that’s just me), antiaging therapies, assessment of hormone status by saliva testing, and much more. Dr. Donnell also points out that the blinding of the study groups to local investigators was likely to have been faulty. So right off the bat, this study was dubious for so many reasons, not the least of which was that some of its site investigators were felons, a problem blithely dismissed by the NIH as being in essence irrelevant to whether the study could be done safely.
OK, OK, I get it. Just because several key investigators weren't exactly the sort of people who had demonstrated a high level of dedication to scientific rigor, ethics, or even honest doesn't necessarily mean the results of the trial aren't valid, but they sure as hell make me wonder, particularly given how minimally statistically significant the detected differences were.
Then there was the result of the FDA inspection of the highest accruing TACT site. It's brutal. In fact, it's more brutal than the Form FDA 483 that I just discussed about Stanislaw Burzynski. I kid you not. it's that bad. Read it and note observations that the investigators there:
- The investigators didn't conduct the investigation in accordance with the signed statement and investigational plan. Several examples were given of shoddy procedures, prefilled forms, and failure to train personnel.
- Failure to report promptly to the IRB all unanticipated problems involving risk to human subjects or others. Examples are given, including failure to report the deaths of patients on the study in a timely fashion (in one case the death wasn't reported to the IRB until four months later; in another case it was never reported at all). In other cases, adverse event reports were not submitted to the IRB.
- Failure to prepare or maintain adequate case histories with respect to observations and data pertinent to the investigation.
- Investigational drug disposition records are not adequate with respect to dates, quantity, and use by subjects.
In other words, the trial was a total mess at that site. One wonders what it was like at other sites, for instance the Marino Center.
It's probably worth looking at the paper itself a bit at this point. I didn't see anything there that made me change my original detailed assessment of the study from four months ago. You can go to the link for the full deconstruction. Every word applies to the published study, but let's look at some key points again. First, the primary endpoint (i.e., the aggregated serious cardiovascular events) did indeed show a modest difference, namely 30% of placebo subjects versus 26.5% of the EDTA chelation subjects (hazard ratio 0.82 for chelation). However, one notes that the result is just barely statistically significant, p = 0.035, with the 99% confidence interval for the hazard ratio ranging from 0.69 to 0.99. (The predetermined level for statistical significance for purposes of this study was 0.036; so this is statistically significant by the barest margin.) More importantly, if you look at the individual endpoints that make up that aggregate, there was no statistically significant difference in death, myocardial infarction, stroke, coronary revascularization, and hospitalization for angina. Subgroup analysis (always a questionable analysis that requires replication, even when preplanned, as in TACT) purported to show a much greater benefit for diabetics, with a hazard ratio of 0.61 (p=0.002), while patients without diabetes showed no statistically significant difference in any of the outcome measures, including the aggregated total bad outcomes.
One question that came up last time had to do with other ingredients in the chelation mixture, specifically procaine and heparin, either of which could conceivably have had an effect on cardiovascular outcomes, particularly when given over the course of months intravenously. Another question that came up was how there could have been a better outcome in diabetics. One notes that the placebo solution contained 1.2% glucose in order to match the osmolarities of the control and experimental solutions. That could conceivably have contributed to a slightly worse outcomes in the control group even in the absence of a therapeutic effect due to chelation. Whatever the case, one notes that in nondiabetic patients there was no statistically significant detected benefit due to chelation therapy. Finally, only 65% of subjects finished all infusions, with only 76% finishing at least 30. That’s a high drop-out rate. Moreover, 17% withdrew consent, resulting in missing data. The investigators tried to correct for this in an online supplement, but these issues remain serious. They might not be so serious as to call into doubt the effect reported if there had been a much more convincing treatment effect, but when you get equivocal results such as this such issues loom much larger.
In fact, so messed up was this trial that it's hard to fathom the decision of JAMA's editors to publish it. Indeed, Kimball Atwood made a compelling case that, given all the ethical problems involved with this trial that any journal that published its results would be violating ethical norms established through the Uniform Requirements for Manuscripts Submitted to Biomedical Journals, established by the International Committee of Medical Journal Editors.
JAMA's editors seem to know this in that they wrote an accompanying editorial justifying their decision to publish this trial using some of the lamest reasoning I've ever seen. First, they claim that they were really, really, really careful in reviewing the article to the point that they even read the Office of Human Research Protections (OHRP) reports, stating:
Moreover, we recognize that publication of research reports in influential journals can do harm. For instance, the debacle involving the study reporting an association between the measles-mumps-rubella vaccine and autism3 and the adverse effects that article had on immunization rates is an important reminder for all medical journal editors about the influence of their work on the attitudes, behaviors, and decisions of physicians and the nonphysician public.
Despite the limitations of the trial by Lamas et al and the continuing controversy surrounding TACT,4 once the scientific issues had been addressed satisfactorily, the decision to publish this report in JAMA involved consideration of several important factors. First, this NIH-sponsored study had been approved by institutional review boards at 2 academic medical centers, was conducted in compliance with federal regulations, and the OHRP investigation had determined that the corrective actions that had been taken were such that patient protection was not at risk.
Second, despite numerous setbacks, criticisms, and concerns, the funding agencies and the investigators (who include one of the preeminent cardiovascular researchers and one of themost respected statisticians) demonstrated courage and persistence in continuing this trial to its completion.
"Courage and persistence"? Give me a break. Dr. Lamas and his co-investigators might have demonstrated many things throughout the long and winding $30 million road of TACT, but courage and persistence were not among them. OK, maybe persistence, but let's not forget that a huge grant was at stake, and no investigator who's the PI of such a huge grant can afford to let it go and let the study crash and burn, although it would have been better for taxpayers and patients if TACT had been allowed to crash and burn. In fact, I get the feeling that the JAMA editors deep, deep down know that, too, as they published an editorial by Steven Nissen, who was utterly blistering in his criticisms of TACT:
Differential dropout in TACT suggests unmasking, but the problem of intentional unblinding is more concerning. The sponsors of the trial, the National Heart, Lung, and Blood Institute (NHLBI) and the National Center for Complementary and Alternative Medicine (NCCAM), were unblinded throughout the trial. The National Institutes of Health policy unwisely allows the sponsor access to unblinded trial data, and both organizations sent observers to the closed sessions of the data monitoring committee. This gave them access to confidential data during each of the 11 interim analyses. The unblinding of the study sponsor represents a serious deviation from acceptable standards of conduct for supervision of clinical trials. If a pharmaceutical company sponsoring a trial were allowed access to actual outcome data during the study, there would be major objections. Like any sponsor, the NHLBI and NCCAM cannot be considered unbiased observers. These agencies made major financial commitments to the trial and may intentionally or inadvertently influence study conduct if inappropriately unblinded during the study.
Dr. Nissen also notes many other limitations in the design of TACT that undermine its reliability, including an observation that the primary endpoint should have only included the most objective and reliable components in its composite endpoint (death, stroke, and myocardial infarction) but also included "softer" endpoints (coronary revascularization and hospitalization for angina) that represented 318 of 483 events reported as primary end point event. He further noted that "if any unblinding occurred, investigator biases could potentially influence the decision to hospitalize or revascularize individual patients."
Dr. Nissen concluded:
Given the numerous concerns with this expensive, federally funded clinical trial, including missing data, potential investigator or patient unmasking, use of subjective end points, and intentional unblinding of the sponsor, the results cannot be accepted as reliable and do not demonstrate a benefit of chelation therapy. The findings of TACT should not be used as a justification for increased use of this controversial therapy.
I couldn't have said it better myself.
Unfortunately, Dr. Krumholz sees it almost exactly the opposite:
The irony is that if a drug manufacturer had gotten this result, they would have celebrated. We have billion dollar drugs like niacin and fenofibrate and ezetimibe that have less evidence than chelation therapy has now. None of those drugs has contemporary outcomes studies showing benefit – and 2 of them (niacin and fenofibrate) have 2 recent negative trials.
If we have little faith in chelation therapy, then it is hard to turn 180 degrees with a positive result and suddenly completely believe in it and recommend its use. Any trial can give an anomalous result and we need to be careful about jumping to a new position with each new piece of evidence. However, we cannot on one hand promote evidence-based medicine and on the other hand ignore what we do not like.
This is, as I've discussed extensively above, not what skeptics and critics are doing. Nor are they being hypocritical, as Dr. Krumholz implies insultingly. The ethical and scientifically rigorous conduct of clinical trials is a key component of evidence-based medicine. Trials that are sloppy in execution, carried out in large part at centers full of quacks (yes, quacks), and unethical are not good evidence-based medicine.
It's highly disappointing that Dr. Krumholz took the results of TACT at face value. As an academic cardiologist, he should know better, but it appears that he didn't even bother to read the paper. He didn't know that there was heparin in the chelation solution, and he didn't seem to have a problem with the addition of "soft" outcomes to the more typical "triple" aggregate outcome used in cardiology studies consisting of myocardial infarction, death, and stroke. In fact, as a commenter pointed out, even the triple composite outcome is not a patient-important outcome. Indeed, given how the individual endpoints that made up the composite endpoint showed no statistically significant differences, the composite endpoint can best be looked at as a way of trying to produce a statistically significant by adding endpoints that are not independent together and hoping that they aggregate to result in a statistically significant difference. I also note, as I have done for defenders of Stanislaw Burzynski, saying that other investigators do it too (or, as I like to call it, the "They do it too!" defense) is not a compelling retort, except perhaps among six year olds. Apparently both Dr. Krumholz and Forbes' Matthew Herper find such a retort compelling because they both use it in comments after Peter Lipson's post.
The bottom line is not, as Dr. Krumholz argues, that proponents of EBM are reflexively rejecting valid clinical trial results. It is rather that TACT is a trial testing a highly implausible therapy using methodology that was incredibly unlikely to produce a useful result. Worse, it was incompetently carried out at many sites and so riddled with problems that Dr. Nissen is quite correct to declare it useless and uninformative. Worse, it endangered patients without offering a reasonable likelihood of helping. If ever there was a dubious trial that is the poster child for using a Bayesian approach to clinical trials, it's TACT.
And if you're in the U.S., as I am, you paid for it to the tune of $30 million. That's $30 million that could have gone to actual, useful biomedical research. It's very sad that apparently neither Dr. Krumholz nor Matthew Herper can see that. It's even sadder still that JAMA published this tripe. In that JAMA is every bit as guilty as The Lancet was in 1998 when it published Andrew Wakefield's antivaccine nonsense. I can (sort of) accept the argument that all clinical trials should be published. However, that doesn't mean a clinical trial so riddled with scientific and methodological flaws should be published in JAMA. If published at all, TACT should have been published in some crappy, bottom-feeding journal, because that's all that it deserves. In a world where medical publishing worked properly, no journal in the top or middle tier would have touched this toxically bad manuscript with the proverbial ten foot pole.
Shame on JAMA! Shame on NCCAM and the NHBLI for funding this nonsense! And, yes, shame on all the shruggie cardiologists who are apparently unwilling or unable to look beyond the hype.
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I would feel more comfortable - and more likely to listen sympathetically to his arguments - if he was mentioning in the text that this study has been retracted.
Because the way he presents it, one could believe that Wakefield's study is still legit and is another case of "inconvenient Evidence".
Which, for certain people, it is and it is, after all.
tl;dr: I would be more likely to consider if I am rejecting "inconvenient Evidence" if the good doctor was showing the ability to reject "inconclusive Evidence".
The Quackwatch piece on Edta treatment points out that each time a hypothesis for why Edta treatment might work was debunked, the practitioners of Edta treatment came up with another hypothesis. Each was demolished in turn.
It's a classic case of circular logic and of cart before the horse -- let's assume that this treatment does something useful, and try to explain why. The fact that it doesn't do something useful only reveals itself with difficulty, and by then, there is a group with a vested interest in arguing that it works and that there is a reason that it works. Sure sounds like a lot of other quackery, doesn't it?
Perhaps somebody can remind me of the historical progression, but if I recall correctly, this whole Edta thing predates the modern understanding of the fatty streak and of foam cells in the formation of clogged vessels.
Also, I seem to recall that long ago, there was a longevity treatment used in Europe that involved iv infusion of procaine. One Cal Tech professor used it and swore by it. I might be off on the particular molecule, but it was something in that class. It's curious that a similar compound is included in this kind of treatment.
a longevity treatment used in Europe that involved iv infusion of procaine
I'm not too much bothered by the fact that the trial was published but more by the fact that the authors were allowed to claim the treatment was effective. The trial shows several scientifically interesting things: Chelation does nothing for non-diabetics. This eliminates 90% of the population as candidates for the "treatment". It shows an effect for diabetics, potentially due to other components of the mix. As there's no evidence that diabetic lesions and non-diabetic lesions are different, the postulated mechanism of calcium removal for lesion reduction is dead.
So all that is needed is a follow-on study designed to isolate the effect of the heparin vs the edta in diabetics. That will either show a very limited potential for chelation or drive a nail in so deep no one will be able to open that box of refuse again.
Of course, finding someone to risk burying chelation with a follow-on trial might be harder. NCCAM is unlikely to fund that and take out one of their few "success stories".
That’s $30 million that could have gone to actual, useful biomedical research.
Which, in this era of tight budgets, is quite a few R01s. As I've mentioned before, the kind of grants that I compete for (albeit from NASA and NSF) have a three-year cost of a bit more than 1% of this.
Given the level of funding, I can understand why the PI wants to publish something. But the reviewers are under no obligation to accept something like this for publication, and it sounds like they shouldn't have.
Were JAMA's editors going after a high-impact-even-if-low-quality publication, as certain other journals (notably Nature and Science) often do? I find their actions otherwise hard to explain here.
Actually, I would consider the RotoBlator to be the "rotorooter" of arteries given the method of treatment.
However, your link does indicate they are making a comparison to Roto-Rooter; I just don't get the analogy - it seems their method and science is more like "Draino" to me...
As fate and business plans would have it, our woo-meisters have created another chelation scenario which enables many more to benefit from the procedure:
no, I don't mean patients with CV issues but the woo-meisters themselves and patients with other conditions like ASDs, MS, Alzheimer's, cancer, you name it.
It seems they believe that chlorophyll is an effective chelator which can be administered orally, thus creating a market for pills and powdered green products that can be added to drinks. ( see NaturalNews store; Gary Null.com /Power Foods; and a thousand other sites).
They are especially enamoured of chorella ( see Adams' "clean" chlorella), spirulina, alfalfa and more general green products ( powdered spinach, broccoli etc); obviously, do-it-yourself-ers can buy juicers ( also available at these web stores).
So if you fear chemicals or don't have the time for IV, head over to your woo supplier NOW!
My first guess is that they get paid to dig the ditch and they also get paid to fill it.
If I'm recalling your past posts about chelation's dangers correctly, I'd also guess it makes the chelation less risky since extra minerals means there's a buffer staving off hypocalcemia and possibly other hypo-mineral problems.
Don't forget the miraculous chelation powers of rhubarb.
Chelation is old hat; there are better ways to keep the flow going.
"Original Luke guzzled gasoline.
He drank it down till his tube was clean.
Pine trees bent down to make a box
For ashes and a dream.
There's nothing much between."
- The Minus 5
Queen, Queen Caroline
Washed her hair in turpentine
Turpentine to make it shine
"I can (sort of) accept the argument that all clinical trials should be published"
So maybe JAMA should institute a separate journal entitled "The Registry of Unsatisfactory Trials" and then all the crappy or inconclusive ones could at least be available to researchers who honestly want to know what's been tried and failed. If they wanted to be more gentle with the title they could substitute "Inadequate" for Unsatisfactory.
My uncle was in this trial, and I have some questions about it that I haven't found answers for. I'm hoping someone here might have a moment educate me.
First, I wonder what is meant by "Conflict of Interest" here. One of the authors, Theodore Rozema, obviously has some connection to Biogenesis Medical Center, which appears to be a site in the trial and thus I assume, the clinic offers chelation. However, the Conflict of Interest disclosure in the JAMA paper mentions nothing about it. I don't think they are hiding that Rozema has connections to Biogenesis, since it's listed in the supplement. I just wonder how it is that this isn't considered a conflict.
Second, with regard to withdrawals, it appears that there was an adjustment for withdrawn participants in the primary analysis, but is it clear if this adjustment was made for the subgroup analyses?
Thanks for anyone who can shed some light.
@Ignorant Kid: If the clinic is only offering chelation therapy via medical trials such as this one, and they don't charge patients to be in a medical trial, then it's fine. Otherwise, there would be no way to do a medical trial without somebody having a conflict of interest. It's also normal that at least one co-author of such a paper would be affiliated with each trial site. However, if one of the trial sites were already offering chelation therapy to paying patients for treating cardiovascular issues, that would be a conflict of interest.
Now, if Stanislaw Burzynski were to publish trial results of his antineoplaston therapy, he would have to disclose the conflict of interest that his clinic charges money for patients to undergo antineoplaston therapy. That may be yet another reason why Dr. B doesn't publish.
Cautionary tale: as a child I had a habit of chewing on a stick of raw rhubarb from the large rhubarb patch at the end of our garden. I developed renal colic, presumably from the excessive amounts of oxalate I was ingesting, which was extremely painful and put me off ever eating rhubarb again. Rhubarb is almost as dangerous as broccoli (and kiwi fruit, of course).
Coriander leaf (cilantro) is also supposed to chelate heavy metals, though the evidence is slim to non-existent. I do sometimes wonder where these ideas come from.
Finally, some good news. If EDTA really is an effective treatment for atherosclerosis*, several McDonald's products, including Big Mac sauce, contain calcium disodium EDTA (PDF), so they should be effective against cardiovascular disease, in a high enough dose.
* It isn't, don't try this at home.
Niacin a billion dollar drug? It's a B vitamin, it's been around for decades and it's cheap as dirt. It may not be effective, but then, neither is chelation.
Quick correction: Dr Chandra/Tru Med was not the highest enrolling TACT site. Trial sites are listed in order of subjects enrolled and Dr Rozema is first on the list with Dr Chandra second. The list of investigators is in the Supplemental Online Content for Lamas et al:
This is surprising. In the response to FDA's inspectional findings at Dr Chandra's site, which is written by Drs Chandra and Lamas - mostly the latter based on prose style - we learn that as of June 2010, 2595 TACT infusions had been given at the site. See p. 12, para. 3
Dividing 2595 by 40 (the total # of infusions in TACT) gives 65 subjects enrolled at the site. But it's almost certain that not all subjects got 40 infusions because of the deaths noted in the inspection & because only 60% of subjects in the entire trial got all 40 infusions. If we divide by 30 we get 84 subjects (rounding down). 30 infusions may be too ambitious as well given overall numbers and Dr Chandra may have enrolled more subjects before the end of enrollment in Sept 2010.
Even so if Dr Chandra enrolled 84 subjects, Dr Rozema enrolled more. If we estimate that Dr Rozema enrolled 1 more subject than Dr Chandra, i.e. 85 subjects, 169 subjects were enrolled at 2 trial sites. This is nearly 10% of the total enrollment of 1708. Lopsided enrollments like this tend to confound data interpretation.
The inspectional findings that Orac linked to are nothing compared to Dr Lamas' response letter to FDA. It's quite astounding in fact.
I, too, would pluck stalks of rhubarb from the patch on my grandparents' farm and eat it raw. Never ate enough to cause any problems, though.
Little bit of trivia: in the Aubrey-Maturin series (Master and Commander) by Patrick O'Brian, a captain is prescribed some rhubarb for an illness. Thinking that "if a little is good, more must be better", the captain ingests far too much rhubarb and finds himself in the head for quite a long while (over a day, IIRC).
Thank you for your reply. I saw that Biogenesis Medical Center does offer chelation therapy under services and they push it via testimonials and such on their website. Hard to imagine they don't charge for it. Anyway, thank you for your time. I appreciate the explanation.
I'm a long time fan of your work. And I want to note, before I respond to your post, that my own reaction to the TACT results was not so different from yours. You can find it here:
I'm not nearly so sure that all your arguments here are as convincing as you think. I am certain that in your haste to attack anything known as woo you are misreading Dr. Krumholz.
I know that you say you hate arguments from authority, but I'm a journalist, and what someone has accomplished does matter to me. Krumholz is probably best known for his work in reducing door to balloon time. He was also one of the loudest critics of Vioxx and said Merck's ezetimibe might be nothing more than a placebo. He's one of the most respected voices in cardiology. I'm pretty sure Steve Nissen still agrees with that. He has been a proponent of science-based medicine. He has something like 700 pubmed citations.
What I hear Krumholz saying is that although the benefits of chelation therapy are still questionable, it is impossible for him to look at a randomized controlled trial showing a positive result and not explore the possibility that there's something to it. (Maybe it's the heparin?)
On your composite endpoint argument, C. Michael Gibson, another of the country's top cardiologists, agreed on Twitter that it was a non-issue.
Krumholz's concern was that people are so eager to dismiss the results that they are refusing to grapple with the data. There is no question that, if this were a traditional new drug therapy, these results would be unlikely to pass muster with the FDA. Chelation is not evidence-based medicine.
But can you really argue that you're more certain there is absolutely nothing to chelation after seeing these results? More than that, can you really embrace the position that other respected doctors aren't allowed to grapple with the data and come to their own views?
I hear a lot of talk about TACT that starts with the assumption that it must be wrong, and, more than that, that things like this should not be studied. If we're going to live by the perspective that there should be no "alternative" medicine but only real medicine, there is a need to collect evidence.
Respectfully, I do think that if you're casting Krumholz as part of the enemy you're probably making a mistake.
I'm no fan of chelation therapy, so take no position on whether the actual scientific data generated by this study should be rejected out of hand or not. However, you do need to be prepared to explain why your criticisms of trial design, particularly the endpoints, should not be equally applicable to other cardiovascular trials of more favored modalities. It is extraordinarily common for the primary endpoint in studies of drugs, or even invasive procedures for which treating physicians are totally unblinded, to be a composite such as "death from any cause, heart attack, stroke, revascularization, or hospitalization for cardiovascular causes." Then the study reports that these events were cut by 40% in the verum group, and the news media claim that the product "Saves Lives." Only by reading the fine print can you learn that the vast majority of events prevented were stentings and hospitalizations, that strokes and heart attacks were nonsignificantly reduced and total deaths not reduced at all. Oh yes, and non-cardiovascular hospitalizations, e.g., for drug side effects, do not count in the primary outcome, as if patients dislike hospitalizations only if they are for heart problems. Indeed, this appears to be a trifle unethical. Would you agree?
Just to make sure I am reading this correctly:
The treatment arm (chelation) contained heparin, a known blood thinner.
The control arm (placebo) did not contain heparin.
So, the "control" arm of the study (the placebo) was not in fact a control at all because it was missing an ingredient with an known or suspected impact on the study outcomes.
If I tried to set up an experiment with a "control" like that my boss would bite my head off.
Science: you're doing it wrong.
I think the money thing is overrated. The biggest problem, even if the clinic only ever performed chelation for free, is that they were already performing this treatment while stating publicly (via their website) that it has lots of benefits other than the FDA-recognized use. Obviously there is a huge motivation to find evidence which supports what they had already been doing and saying without evidence.
Yes. In fact, even if I grant you the issue of composite endpoints, there are plenty of other issues with TACT to make its results completely unreliable, which have been detailed by Kimball Atwood.
As for Dr. Krumholz, I am not attacking him as an enemy of SBM. I am pointing out that in this case he screwed up and that he really should know better, particularly given that he's such a respected academic. Basically, it was very clear from his post that he was not at all familiar with the numerous issues with the trial that doomed it from the start to the point that any result it produced would have to be really striking to overcome them. Its results were anything but striking, for the reasons I explained ad nauseam.
Also, if Dr. Krumholz is going to write a blog that strongly implies that supporters of EBM are hypocrites exercising a double standard with respect to evidence, dogmatic, or otherwise close-minded for not accepting TACT at face value, he should be prepared to take the criticism he's going to going to receive, particularly given that it's clear from his comments that he didn't read the paper very carefully and is unfamiliar with the history of TACT. In fact, I found his implication that SBM supporters are hypocrites for not being more open to the results of TACT insulting.
As for composite outcomes, I'm sorry, but they're dubious at best and misleading at worst; they are also very poorly reported and widely abused. I can provide references if necessary to support my position. Not surprisingly, most of the papers are from cardiovascular trials, where this deceptive practice seems to be most common as far as I can tell.
As I said, though, you can completely leave out the issue of the composite endpoint, and TACT would still be crap.
I'm flattered that you are a fan. As a fan, you must be aware that I rarely pull punches. I like to think that the fact that I restrained myself from using some of my favorite terms for quackery supporters (e.g., "burning stupid") should show that I don't consider Dr. Krumholz to be a woo. I just consider him to be disappointingly mistaken and uninformed on this one trial.
This is weren prior plausibility and Bayesian analysis comes in. I can't do the maths, as I don't know the figures or previous research well enough, but if before, we could say it was 98% certain chelation does not work, then when we include this slight benefit from one poorly controlled study, it is unlikely to shift that figure much.
As a related example, if 10 studies find absolutely no benefit to a treatment, and an eleventh comes out and finds a small one, we don't throw out the previous 10 and just focus on the one that worked (well, we don't if we are aware of them. If they didn't get published this won't help).
I do not endorse chelation therapy, and do not view the TACT results as providing actionable evidence for regulatory decision making or for guiding clinical practice. However, notwithstanding the flaws in trial design and conduct, I would like to make the following observations regarding TACT.
1. For a variety of reasons, I am not a big fan of the type of composite endpoint used in TACT. However, the so called 'soft' subjective components of CV hospitalization and revascularization are more prone to ascertainment and misclassification error, and therefore likely to bias the results towards the null. While this might be anti-conservative for safety assessment where one is interested in ruling out unacceptable risk, it can be overly conservative for efficacy assessment. The choice of these 'more prevalent but less important' endpoints is driven primarily by trial feasibility considerations.
2. The amount of missing data, while vexing, is not unexpected given the onerous treatment protocol involving multiple infusions over a prolonged period of time. The missing data can challenge the interpretation of trial results, but the claim that it invalidates the results is not supported by careful examination of the data provided in the supplement. There does not appear to be major imbalances in either the key prognostic covariates or in the reasons for 'missingness' amongst the 2 randomized groups in those who dropped out. Thus, the potential for 'informative censoring' appears to be minimal. By the way, the problem of missing data (and sloppy trial conduct) is quite common even in clinical trials run by academic research organizations of the highest repute!
3. There are several examples in medicine (antioxidant vitamins, hormone replacement therapy, magnesium for MI, anti-reperfusion injury therapy, etc.) that have shone the spotlight on the slippery slope argument of plausibility. As Thomas Huxley said it best, "the tragedy of science, the slaying of a beautiful (plausible) hypothesis by ugly facts!"
4. The principle of equipoise, an ethical prerequisite for patient randomization and enrollment, would require a pretrial null hypothesis probability of 50%. If the pretrial null probability is 98% as suggested by G. Shelley, then how can one ethically justify conducting the trial to begin with? Surely, the sponsor, NHLBI, must have given it some thought!
5. The p value of 0.03 translates into a minimum Bayes' factor of 0.09, which reduces the null probability from 50% pretrial to about 9% post-trial. While this does not represent strong evidence against the null, it does reduce the level of skepticism surrounding chelation therapy.
6. There is clearly a double standard when it comes to accepting the results of trials evaluating so-called dubious quack cures such as chelation versus trials assessing promising de rigueur cures such as gene transfer or stem cell therapy.
Finally, while the debate surrounding TACT is clearly warranted and welcome, I hope it generates more light than heat.
4. Why in the world would you make that assumption? Trials are routinely done, by many of the same people, of treatments with pretrial null probabilities of greater than 99.9999% (homeopathy or reiki, for example).
5. #4 kills this argument too; the null probability pre-trial was much much much greater than 50%.
6. Evidence for said double standard? Orac regularly calls out mainstream research when it is faulty.
That was the question being asked by sceptical bloggers several years ago.
Well, I did say I just made up the 98% figure as an example, but I don't think it too unlikely. As others mentioned, people still study homeopathy and get grants to do that and I'd argue that the pre-trial null plausibility is much greater.
Even if 98% is too high, the pre-trial value can't be 50%. That might be the case if it had never been investigated at all (though even then, you'd have to fail to take into account biological plausibility), but previous trials will have shifted this, otherwise you get the contradictory result that after this trial you are at a 9% probability, but if someone starts a new trial, that jumps back up to 50%.
OK, let's assume the pretrial null probability is 75% (and not 98%), the TACT evidence (howsoever flawed), will moderate the post-trial null probability to 22%, which means that more likely than not, chelation is associated with a non-null treatment effect.
If one is a skeptic (pretrial null probability >50-75%), why would one expose one's patients to the hazard of chelation?
Conversely, if you are an enthusiast (pretrial null probability <25-50%), why would one deny their patients the benefits of chelation?
In principle, one can ethically justify randomizing one's patients if one is not overly sure of its treatment effect, i.e., suspending one's belief as reflected in a pretrial null probability of 50%.
Bottom line, in my opinion, the arguments that the TACT results are dubious or not valid are overstated!
On what basis do you believe that "arguments that the TACT results are dubious or not valid are overstated!"? If the flaws in the studies are as significant as some claim, your discussion of statistics is rather pointless - calculating error bars and p values based on skewed observations produces meaningless numbers.
Thank you for your comments. Before I go on, I have to mention that the concept of equipoise doesn't require a pretrial prior probability of 50%. It requires that there be genuine and substantial uncertainty over whether the treatment is effective, particularly when the trial is placebo-controlled, where the control is in essence doing nothing. Or, perhaps a better way of putting it is that there has to be real uncertainty over whether the risk/benefit ratio is favorable, preferably with preclinical and clinical evidence suggesting that it is. TACT met none of these criteria, nor did it meet the standards of the Helsinki Declaration:
I note that there was no compelling clinical or preclinical evidence that chelation therapy has significant efficacy against atherosclerotic cardiovascular disease, and we know that chelation therapy can cause harm; so the risk was not minimal. Moreover, as demonstrated in the links I provided, many, if not most, of the site investigators carrying out the trial do not have appropriate scientific training and qualifications.
As for the composite endpoint, I never could figure out why they are so prevalent in cardiology research. In oncology, we tend to frown on them in our clinical trials—and with good reason. I'm also not particularly convinced by your argument, at least in this case, that a composite endpoint is more conservative, given that not a single one of the components that made up the composite endpoint reached statistical significance. There are so many other issues that have been widely discussed in the blogosphere about TACT that I could only briefly touch on here about how the trial was completely unethical and violated the principles of informed consent. Moreover, not everyone agrees that the dropout rate is not a problem:
Even if we take the trial at face value and ignore all the major problems with its design and how it was carried out that almost certainly make its results completely unreliable (as Dr. Nissen points out), all we're left with are two findings. First, chelation therapy does absolutely nothing for quality of life. Second, it provides zero benefit for patients who are not diabetic. The only reason for a barely statistically significant difference in the overall population boils down to the modest benefit reported in diabetics. Personally, I strongly suspect that that benefit in diabetics is not real (for all of the reasons I discussed above and here), but let's for the moment say it is, just for the sake of argument. In that case, what the recommendation from this trial should be is that no non-diabetic with cardiovascular disease should be treated with chelation therapy because it definitely does not work for them. It should also be stated that no claims for improvement in quality of life and symptoms should be made, because chelation does nothing for that, either. Interestingly, even Lamas doesn't suggest that chelation should be used even in diabetics.
Regarding the issue of prior probability, it's not overstated as you claim. In fact, I like to point to the masterful analysis of TACT by Kimball Atwood, Elizabeth Woeckner, Robert S. Baratz, and Wally Sampson published five years ago in Medscape. Besides detailing at huge length why the trial is unscientific and unethical, Atwood et al made this prediction:
Sounds eerily like the outcome to me, except that the outcome arguably showed even fewer "positives" than Atwood et al had predicted. All that for $30 million. What a waste.
Thank you for responding to my comments.
“Before I go on, I have to mention that the concept of equipoise doesn’t require a pretrial prior probability of 50%. It requires that there be genuine and substantial uncertainty over whether the treatment is effective, particularly when the trial is placebo-controlled, where the control is in essence doing nothing.”
How would you quantify genuine and substantial uncertainty?
"I note that there was no compelling clinical or preclinical evidence that chelation therapy has significant efficacy against atherosclerotic cardiovascular disease, and we know that chelation therapy can cause harm; so the risk was not minimal."
Is there robust evidence it is not effective or it is harmful? The answer has a bearing on quantifying uncertainty.
"I’m also not particularly convinced by your argument, at least in this case, that a composite endpoint is more conservative, given that not a single one of the components that made up the composite endpoint reached statistical significance."
I don’t think the composite endpoint is conservative! What I am saying is that inclusion of soft and somewhat subjective endpoints such as CV hospitalization or revascularization increase the potential for ascertainment error and misclassification that typically biases the results towards the null. So, if the objective of the trial is to prove superiority, then the bias will operate against it (conservative). On the other hand, if the objective of the trial is to prove noninferiority (rule out unacceptable risk), then the bias will operate in its favor (anti-conservative).
"There are so many other issues that have been widely discussed in the blogosphere about TACT that I could only briefly touch on here about how the trial was completely unethical and violated the principles of informed consent. Moreover, not everyone agrees that the dropout rate is not a problem:
The commentators quoted in the AP story in November 2012 are correct in expressing their surprise at the pattern of differential missing data (more in placebo group). However, without access to the details of the data (provided in the JAMA supplement), they had no way of assessing whether this could lead to informative censoring. Careful scrutiny of the data doesn’t lead to the conclusion that informative censoring did indeed occur in favor of chelation. Moreover, the results of the sensitivity analyses don’t support this assertion. I acknowledge that missing data are problematic in general as they challenge the interpretation of the overall results, but the onus is on those who claim that it invalidates the results to prove so!
"Personally, I strongly suspect that that benefit in diabetics is not real (for all of the reasons I discussed above and here), but let’s for the moment say it is, just for the sake of argument. In that case, what the recommendation from this trial should be is that no non-diabetic with cardiovascular disease should be treated with chelation therapy because it definitely does not work for them."
Your interpretation about treatment effect in diabetics is not unreasonable. Even though the subgroup analysis was prespecified, and the interaction is quantitative (difference in magnitude of effect), adjustment for multiple comparisons would have weakened the interaction term. Your presumption that TACT provides actionable evidence for clinical practice is not endorsed by anyone including the TACT investigators. The best case interpretation of the data is that the evidence is inconclusive. Ideally, under such circumstances, the only worthwhile recommendation should be ‘additional studies are warranted to adjudicate the uncertainties’. That is how science and knowledge should progress.
"The trial, moreover, is unlikely to yield “an informative negative result” even though chelation is almost certainly ineffective for CAD. It is more likely to yield ambiguous results. There are multiple endpoints, including subjective quality-of-life measures, and several subgroup analyses.[4,5] The variety of trial settings increases the likelihood of heterogeneity of procedures and reporting. Promotions of chelation by TACT co-investigators have already introduced unacceptable bias into the trial. There is ample, additional opportunity for mischief, and ample reason to think that several co-investigators are inclined to make it. The statistical analyses will not be Bayesian.[322–324]"
Here is my Bayesian analysis of TACT which you might find instructive:
Evidence (likelihood) = 0.82 (0.69, 0.99)
Prior (skeptical) = 1.0 (0.75, 1.33) (this means that the mean is centered on null, and there is only 10% probability of the effect being >25% risk reduction or >33% risk increase; many would argue that this is a reasonably skeptical prior distribution)
Posterior = 0.87 (0.75, 1.02), i.e., the probability of a >13% risk reduction is 50%, and the probability of a >10% risk reduction is 66%.
So if we start from a position of skepticism, integrating the results of the TACT trial reduces the degree of skepticism. This is exactly how Bayesian analysis helps upgrade knowledge and information.
One would require a prior of 2-fold increase in CV risk with chelation (not supported by evidence to my knowledge) to completely nullify the results of TACT trial, an arguably IMPLAUSIBLE conjecture!
There are many cases where previously established beliefs are later proven to be wrong or require substantial revision.
To suggest that this study should not have been published would be to support publication bias and is the antithesis of proper science.
The contention inferring that this study somehow shows that chelation is ineffective clearly shows the kind of double standard and willingness to misinterpret results that exists in the profession.
@Cvrai - proper studies stand up to scrutiny. If you read the study, the critique, and the follow-up, you'd understand that there were serious problems with the study design, implementation and overall methodology - saying the study is bad isn't saying it shouldn't have been published, it is saying that it should stand on its own merits, which unfortunately, it does not.
@Lawrence - What I see is a double standard. The shortcomings of the current study are standard and overlooked in others. What I see is a misleading interpretation. I don't see how from any objective standard someone could interpret the results as somehow showing chelation is now more worthy of being dismissed, but astonishingly that is how an accompanying editorial spins it.
For any who believe in the proper pursuit of science such displayed bias should reek. People who see such incongruities are right to grow more skeptical of those who would apply such double standards.
I am aware of other studies on other health issues that have been relied upon for policy that have gaping problems. For example the Seven Countries Study and the Oslo Diet-Heart Study. Compare this study to those studies and tell me this study even with all its flaws is really fundamentally worse. Tell me why this blog isn't up in arms in the same way when those studies that I have mentioned are actually used to support current policies despite their glaring weaknesses.
The kind of criticism seen here is selectively applied. It is because the topic explored is chelation a therapy that has become associated with alternative medicine. As others have pointed out if this was some novel drug the chances it would illicit much passion would be low.
That means there is an outside issue at work here: hostility towards alternative medicine. Going by the reactions hostility even in the face of evidence. Such passion has no place in processes that claim to be scientific.
Cvrai, you've provided no evidence for this statement. If you want to be taken seriously, try engaging with the actual study instead of blanket statements like this.
What evidence? I've seen assertions, but no evidence. Also, you may want to peruse this blog a bit more, as you will find that Orac (and the regulars) do address "conventional" medicine and "novel" drugs. For instance, take Stanislaw Burzynski's "novel" (well, 30+-year-old) drug, antineoplastons, as an example that has been addressed recently (and with many, many posts).
Try to avoid making sweeping declarations of bias like that, especially when you have yet to do your homework.
Tell me why this blog isn’t up in arms in the same way when those studies that I have mentioned are actually used to support current policies despite their glaring weaknesses.
Perhaps because those studies were published more than 40 years ago, and that their prinicple findings regarding diet and health risk have been refined and upheld by multiple additional studies during the ensuing 4 decades?
The Seven Countries Study was the first to examine associations among diet, risk, and disease in contrasting populations beginning in1958 and ending in 1971. While today we can point to genuine criticisms of it's methodology (notably the manner in which they selected the populations studied and the limited populations units used for comparison, in 1958 it was state of the art and the idea of looking for ecologic correlations ground breaking.
The Oslo-Diet heart study was published in 1966, and again was among the first of these types of ecologic correlation studies.
The TACT study on the other hand was begun in 2003. What's their excuse?
It is interesting to compare TACT with the Oslo Diet-Heart Study (the Seven Countries Study was an epidemiological study, not an interventional one).
TACT had marginally statistically significant results for serious cardiovascular events:
n = 1708, 30% of placebo subjects versus 26.5% of the EDTA chelation subjects with p = 0.035
The Oslo Diet-Heart Study also had marginally statistically significant results for serious cardiovascular events:
n = 412, 39% of control subjects versus 30% of diet patients with p = 0.05
TACT showed (at best) at 3.5% reduction in serious cardiovascular events, whereas the Oslo Diet-Heart Study reduced reduction in serious cardiovascular events by 9%. The current consensus view is that diet modification has only a minor effect on serum cholesterol levels, but that even these small changes can result in improved cardiovascular outcomes, so they are worth pursuing before resorting to medication. That seems consistent with not only these studies but a whole raft of other more recent evidence - see Steinberg's 'Thematic review series: The Pathogenesis of Atherosclerosis. An interpretive history of the cholesterol controversy'.
Above should read "the Oslo Diet-Heart Study reduced reduction inserious cardiovascular events by 9%".
Look at earlier comments regarding composite endpoints and their standard usage in similar studies. Also see below.
Are you suggesting the results of the TACT study are merely assertions and not evidence?
The Seven Countries Study and Oslo Diet-Heart Study old as they are still mentioned in defense of the current policies and guidelines. TACT isn't. I've even seen the Oslo study referred to as among the best studies of its kind. I wonder what you would think though if you knew that the participants in that study were provided sardines in cod liver oil and instructed to eat seafood in place of meat and eggs. Compare that to the small presence of heparin in the TACT trial and the TACT trial doesn't seem so bad. Consider also the recent findings on sugar and refined carbohydrates and one might want to ask if all the studies of the past properly accounted and adjusted for their effect. Current nutritional policies are built on sand. This is far more scandalous than anything chelation related, but all I hear are crickets chirping instead of full-throated voices from those who would insist on science-based evidence.
I haven't read the Steinberg link in detail but there is some question as to whether statins are effective due to their effect on cholesterol or some other pathway. It may well be they are beneficial because of their effect on inflammation. A recent study shows that omega 3s seem to lose their efficacy in the presence of statins. Maybe statins interfere with omega 3 but maybe omega 3 and statins work in the same way? Reducing cholesterol wouldn't appear to be that mechanism however. There are some studies that show that those with the lowest levels of cholesterol (supposedly good) had the highest incidence of mortality.
I though I detected a hint of cholesterol skepticism - I suggest you read Harriet Hall's criticism of their ideas before you go too much further down that particular rabbit hole. Read the Steinberg series too, or at least skim through the summaries. The cholesterol skeptics are wrong - they cherry-pick their way through the literature, ignoring large amounts of evidence that contradicts their claims.
They are still mentioned because they were the first attempts to look at dietary interventions to reduce cardiovascular disease. They are part of a very large body of evidence that supports the consensus on diet and cardiovascular disease. TACT has no such body of evidence, nor scientific plausibility to support it.
I disagree. Could you be more specific about which current nutritional policies you are referring to, and what evidence contradicts it?
We know that reducing cholesterol by any means, whether through diet, cholestyramine, statins etc..has a beneficial effect on cardiovascular disease. So it seems likely that statins also exert at least part of their beneficial effect on cardiovascular disease by reducing cholesterol, but they also reduce all-cause mortality, which may be due to their anti-inflammatory effects.
That claim is a particular bugbear of mine; having worked in clinical biochemistry I know very well that very sick people have low serum cholesterol, but they also have low serum albumin and low total proteins, because they have poor nutrition and often, in the case of cancer patients, cachexia. Low cholesterol is a result, not a cause of serious illness. Older people with chronic diseases also tend to have low cholesterol because the people with high cholesterol already died of cardiovascular diseases, not because their low cholesterol made them sick.
There's a paper on the interaction of statins and omega 3 here. I wasn't aware of this, so thanks for drawing my attention to it, though I'm not sure what to make of it yet.
I looked at the Harriet Hall link. I cannot say I'm impressed. THINCS presented more citations and the comments section is filled with comments lambasting Hall's argument.
If dietary cholesterol only has a small effect as Hall admits, current dietary guidelines to avoid saturated fats at best have minimal relevance. If statins work to reduce CVD and mortality by pathways other than reducing cholesterol then the cholesterol question it seems still remains unresolved contrary to Steinberg's claim.
Worse if you combine the recommendation to avoid saturated fats with the use of statins one possible deleterious effect would be to avoid meat (a main source for coenzyme Q10) while taking a medication associated with weakening muscles.
This is still debatable. Even by Steinberg's estimation this question was settled only by the advent of statins. But if statins work via other pathways.... Correlation yes; causation still room for doubt. Unconvinced? Read the comments of a developer of a drug that shows potentially stronger cholesterol lowering effects than statins. Statins will still remain the mainstay because they are proven to reduce events. Perhaps if that drug is approved and with more studies a more definitive answer to the question can be given.
I keep seeing the phrase "the totality of evidence" used by Hall and medical organizations to justify their views but in my own personal attempts to look at the "totality of evidence" I find significant omissions and skewed interpretations and have a reaction similar to the one found in this paper.
You don't settle a scientific debate by putting citations that support or do not support your hypothesis into two piles, with the biggest pile winning, though if that were the case the lipid hypothesis would come out well ahead. You need to look at the literature as a whole, including the quality of the studies, how well confounding factors are controlled for prior plausibility, epidemiological evidence and our understanding of atherogenesis, among other factors. On the basis of this evidence the great majority of doctors and scientists in this field accept the lipid hypothesis as proven. It is only a minority of so-called skeptics that don't accept this, and I think it's fair to describe many of them as cranks, including some of those "lambasting" Dr. Hall.. Dig a bit deeper and you will find their claims don't stand up to close scrutiny.
I suggest you spend a bit of time looking at those THINCS citations and compare what they actually say to what THINCS claims they say. Also, look at all the citations in Steinberg that THINCS pointedly ignores. When I did this a few years ago I was shocked at how THINCS deliberately misrepresented studies, cherry-picked only studies that supported their beliefs, and even cherry-picked bits out of studies, ignoring the very large amount of evidence that completely contradicts their position. Don't take my word for it, look for yourself. Compare the citations Harriet Hall provides and see if they say what she claims they do.
It's not a matter of Hall admitting this, we have known this for decades. Only a minority of cholesterol in the blood is dietary, most is made in the liver, that's why statins were developed, to reduce cholesterol synthesis. The conventional approach in patients at high risk of cardiovascular disease is usually to try lifestyle modification to reduce cholesterol first, and resort to medication if this fails. Isn't a 14% reduction in cardiovascular risk well worth pursuing?
If? Steinberg's "claim" is supported by a huge mountain of evidence gathered over several decades. We know how statins work, and we have a pretty good idea of how reducing circulating LDL cholesterol reduces atherosclerosis. Statins may have other effects through other mechanisms, but we can be close to certain that their effect on CVD is through lowering LDL.
There's more CoQ10 in soy bean oil, olive oil, grapeseed and some fish than there is in beef, so that isn't necessarily a problem. Some doctors prescribe CoQ10 to patients on statins who suffer side effects, which may be a good idea, though the evidence still isn't very clear.
It really isn't debatable. Most scientists were convinced before the advent of statins, and there really isn't any reasonable doubt any more.
Deeply unconvinced. I'm not really clear what you are arguing here. Are you suggesting that saturated fats do not increase cardiovascular risk? That replacing them with PUFAs doesn't reduce cardiovascular risk? I think the evidence for this is compelling. I see a lot of people complaining about carbohydrates, but I think the evidence shows that consuming more calories than we expend, resulting in obesity, is the real problem with carbohydrates.
I don't understand what your argument is here either. Statins will remain the mainstay until the new drug is proven to be safer and/or more effective. It is very likely that a further reduction in LDL will further reduce cardiovascular risk.
I can only suggest you plow through all five parts of Steinberg's review, which discusses "the totality of evidence" in detail. This is a complex area, there's a lot of evidence of varying quality, and you really do need to look at the forest as a whole with a critical and skeptical eye, not just a few interesting-looking trees, or you may get a very distorted view, like that promoted by THINCS.
I've seen stretched arguments from some THINCS members in advancing their positions—but I've also seen the same from those promoting the current dogma. In fact you see it quite vividly in this TACT chelation study where the results are ignored or massaged to conform to predominant thinking rather than presented in light of their significance.
Would you be referring to the same mountain of evidence that was the basis for the low-fat American Heart Association Prudent Diet that was dumped in favor of the Mediterranean Diet after it was humiliatingly found to be inferior? The same mountain of evidence that castigated low-carbohydrate diets before direct RCT diet comparisons were actually done?
You stated previously you were unaware of the recent research suggesting statins interfering with omega 3. Moreover from what I can tell how omega 3 works is still not well understood nor is omega 6. If we don't know how those work I suggest we still have a significantly unclear picture.
Which saturated fats are you talking about? Palmitic and myristic acids? I'll agree that they likely increase risk. Stearic and lauric acids? No and possibly even reduce risk. Saturated fats as a group may fall in-between whole grain and refined carbohydrates in terms of association with increased CVD risk. So it might actually be apropos to call saturated fats neutral and from that point-of-view the better way to phrase your question is "Do PUFAs lower the risk of CVDs in comparison to saturated fats?"
Now the evidence for the beneficial effects of omega 3 seem to be quite clear but omega 6 is another story.
Are you aware of the theory that omega 6 is actually harmful and promotes inflammation? It appears that there isn't really that strong a body of research showing the benefits of omega 6 alone. In fact a recent update to the Sydney Diet Heart Study, one of the handful equipped to test its effects on its own showed negative results, significantly worse than for saturated fats.
One of the other interesting suggestions of the statin and omega 3 paper I mentioned earlier if I read it right is how statins interact with omega 6 in place of omega 3. That is a potentially significant mechanism if the omega 6 is dangerous theory is true.
You are right this is a complex area but the current dogma has been prevalent for over 30 years and has seen a concomitant rise in obesity with no lowering of CVD incidence. The superiority of the Mediterranean diet and low-carb diets contrary to expectations strongly call into question the assumptions of the prevailing wisdom.
You described the 14% reduction in cardiovascular risk we see in a systematic review of the effects of modification of dietary fat in 65,508 participants as being of "minimal relevance", yet you appear to think the 3.5% reduction in cardiovascular risk we see in 1,700 participants in the TACT study is significant? Who is massaging the figures here?
No, the mountain of evidence that supports the lipid hypothesis, in contrast to the tiny amount of poor quality evidence that supports chelation, which is what I thought we were discussing. You appear to be trying to steer the discussion towards other more controversial areas of nutrition that I agree are less well-supported by good evidence.
As I have stated many times here, my opinion on diet goes little further than Michael Pollan's maxim, "eat, not too much, mostly plants". I think the main problems we see in the developed world are from people eating too much, period.
I was not talking about statistical significance, but significance in the body of research on chelation. The TACT study is significant in that it is one of the largest of its kind and the results are contrary to the received wisdom about chelation. Instead of noting this, however, what is presented in editorials is a watering down and misrepresentation of the study's findings.
That the body of research on chelation is thin is more reason to be open-minded about its possible effects since even when there is a "mountain of evidence" it hasn't always been enough to insure clarity on an issue. Given such examples one would think medical editors would be more humble and circumspect in their comments. The issue here I'm concerned with isn't chelation but the pattern of behavior and attitudes among medical practitioners that undermine the scientific process in their desire to promote prior unsubstantiated cherished beliefs.
Neither was I.
That really isn't true. Firstly chelation has zero prior plausibility i.e. our understanding of atherogenesis does not suggest that chelation will reverse it; I suppose you could describe that as "received wisdom". Secondly, the available evidence strongly suggests that chelation is not effective in treating CVD. Thirdly the TACT study has a raft of very serious problems, such as shoddy procedures, prefilled forms, failure to train personnel, convicted felons with serious conflicts of interest at some sites... (you did read Orac's OP above, didn't you?), as well as problems like a lack of blinding, and the lack of heparin in the placebo. Its results are underwhelming at best, and do not remotely support the claims made for chelation by its practitioners.
Please give specific examples of this.
I didn't say the body of research on chelation is "thin", I wrote of the "tiny amount of poor quality evidence that supports chelation" (I don't consider anecdotal reports to be evidence). There is a moderate amount of evidence that supports the hypothesis that chelation is not effective in CVD - see the review I link to above which concludes:
Compare the similar review on reduced or modified dietary fat for preventing cardiovascular disease I have referred to before, and that you dismiss as being of “minimal relevance”.
This is a treatment in widespread use that offers false hope to patients, leads them to spend money unnecessarily, and that has serious risks that clearly outweigh any benefits, even if the TACT study's results are accurate (3.5% reduction in CV risk?). I think that's why medical editors are hostile.
That's exactly the pattern of behavior I am seeing in you here. You seem willing to embrace the poor quality evidence for chelation, yet unwilling to accept much higher quality evidence for dietary fat modification. Why is that?
I often see complaints in CAM circles about conventional medical practitioners and scientists being dogmatic and closed-minded. Having worked with many of these over the years, I have found the opposite to be true. Most of the doctors and scientists I have worked with are curious and open-minded, willing to look at new ideas and to consider evidence that challenges their beliefs.
In contrast, CAM true believers I have talked to are very often dogmatic and narrow-minded, unwilling to even look at evidence that challenges their beliefs, and ready to embrace conspiracy theories to dismiss anything that doesn't fit their "prior unsubstantiated cherished beliefs".
I'd say our understanding of atherogenesis is incomplete. Calcium intake has recently been associated with higher CVD mortality. Chelation it is theorized removes the calcium in atherosclerotic plaques. It looks like a rational theory that deserves to be tested. It's not saying for example that the alignment of the stars is affecting the blood's properties. Saying beforehand it is implausible because it does not conform with the prior model (that has a less than stellar record) is unscientific and narrow-minded.
A headline from Fox. I'd suggest that reading that article one might be led to believe the TACT study came out against chelation. It certainly seems that's how the reporter read the accompanying editorial.
The review you refer to seems to be based on six studies two of which were supportive of chelation. I aver that is hardly a basis for a slamdunk conclusion especially in light of the results of the TACT study.
You refer to the Hooper et al. study. It is an update on an older review. Compare the two and you'll notice a trend towards less significance. Keeping in mind the past 30 years has been a heyday of dietary fat dogma and it is surprising the evidence isn't weighted even more in favor of the reduction of saturated fats. There are other relatively recent reviews that arrive at a different conclusion from the Hooper study here and here.