Evidence In Medicine

Proof, Plausibility, and a Tale of Two Viruses

Listening to NPR

There was a third incitement to this blog that I have not yet mentioned, as I am not currently in possession of an asbestos suit, but I feel the time has come to discuss it. I was driving to work listening to NPR's Morning Edition last month when I heard, "We have news, now, of a scientific breakthrough about a disease that affects over a million people in the U.S."

My ears perked up, wondering what major breakthrough I had missed. I learned from the interview that an article had been published in Science linking the retrovirus XMRV with chronic fatigue syndrome. On the usually reserved and balanced NPR, I was startled to hear the interview proceed in such a way as to assume that the study was accurate and that it proved wrong all those who had questioned CFS as a single disease entity. I had the sense listening that either the interviewer or the producer of the piece had a personal stake in the outcome of the story.

The article in Science reported that 67% of patients with CFS and 3.7% of healthy controls had XMRV DNA. A news story reported that, after the submission to Science, the authors of the study improved their assay for XMRV antibodies and found them in 95% of patients with CFS. Is it plausible that 95% (or 67%) of patients diagnosed with CFS really have a single disease caused by the retrovirus XMRV?

Plausibility

Plausibility in medicine is a tricky concept. Almost any result can be argued to be biologically plausible by someone with a modicum of creativity. And yet, biologic plausibility often does not pan out so well when it meets real life. When I was in training, beta blockers were considered absolutely contraindicated in patients with heart failure and the incipient notion that peptic ulcers were an infectious disease was considered absurd.

There's a different kind of plausibility, though, for which I have greater fondness. It has to do with prior probabilities developed from a fair-minded look at the epidemiology of diseases or from prior trials that test some similar notion to the current idea under scrutiny. For instance, while JUPITER found a 44% reduction in its composite primary endpoint, it seems highly implausible to me that rosuvastatin really lowers risk by this much. Nearly every statin seems to lower risk in primary and secondary prevention by 20-25%; why should rosuvstatin have such a marked effect in a fairly low risk population? It seems more likely that the effect was exaggerated when the trial was stopped early for benefit than that we can really expect these sorts of results from rosuvastatin in patients with low LDLs and mildly elevated CRPs.

Evaluating the Evidence

The article in Science is an odd read for a clinician. The same article in a medical journal would spend a lot of time describing who the patients and controls were, and how the patients were diagnosed with CFS, but none of that is in the article. Like most articles in Science, it spends its time on bench methodology (how the retrovirus was detected) rather than on the methods by which CFS was diagnosed and the blinding used when the samples were analyzed.

That raises an initial question of "are these CFS patients similar to those who walk into a primary care physician's office carrying a diagnosis of CFS?" That is, can the results be generalized to the broad group of people who are said to have CFS? Without a more detailed description in the article, I have no way to be sure.

But beyond that, what has happened with other CFS "breakthroughs"? Back in the 1990s, after an article showing much higher rates of neurally mediated hypotension in patients with CFS (22 of 23 patients) than in healthy controls (4 of 14 controls), I made the same argument on Usenet that I'm in the process of making here. That article led to patients with CFS being treated with fludrocortisone and similar agents. Eventually people concluded that the neurally mediated hypotension story didn't really make sense and clinicians and patients moved on.

From my point of view, given the patients I have seen carrying the label CFS, it seems extremely unlikely that any single etiology will explain 95% of cases. Patients carrying the label CFS in the real world (rather than in research studies) seem to be a mixed bag. Many seem to have atypical depression or another psychological cause of fatigue (thus my need for the asbestos suit). Others, though, likely have a missed diagnosis or have some condition that is, as yet, unknown to medical science (retroviral infection with XMRV would have previously fit in this category).

Interpretation and Proof

Why does it matter? From the clinical perspective, many people with depression (typical or atypical) can be helped by standard therapies. Avoiding the label of depression for those who are depressed is no kindness (though it is also of no help for doctors to insist that symptoms are due to depression when they are not; I do not believe that all patients with CFS really suffer from depression). And getting therapies for purported etiologies that don't pan out (such as fludrocortisone for neurally mediated hypotension) simply exposes patients to side effects, harms, and costs, without resulting benefits.

Beyond that, though, this issue is at the intersection between evidence, experience, and opinion. I have no expertise in retroviruses, know nothing about XMRV or the methods used to detect it, and am lacking detailed evidence about how the study in Science was performed. But evidence about diseases still must be interpreted through the lens of clinical experience.

Ultimately, many of the arguments between clinicians about CFS (let alone the arguments joined by patients) have to do with differing clinical interpretations of whether CFS feels like a believable single disease process. This is an area where a discipline like EBM doesn't provide much of a road map. Yet expert clinicians must make these sorts of judgments all the time when they decide whether to consider a cluster of signs and symptoms as an individual disease. Before HIV was discovered, I listened to expert clinicians reject the arguments for multiple immune system insults or inhaled nitrates as causes of AIDS, and instead point out that AIDS would turn out to be caused by a virus that was transmitted similarly to hep B given the similar epidemiology of the two diseases. There is no path from evidence to understanding that does not rely on expert interpretation, and, ultimately, no mechanical measure of sufficient evidence or proof outside of what counts as proof to those patients and providers who must make decisions.

XMRV

XMRV may yet turn out to be the cause of CFS, but given the track record of such causes, I think we need better evidence. Before NPR describes a "scientific breakthrough" and gets the hopes up of so many, I wish they would spend more time thinking and interviewing and looking for some balance. I have to believe they could have found an expert or two who would have urged caution in interpreting these results.

If future studies confirm the XMRV hypothesis, those out there now who are infuriated by my comments can feel free to say "we told you so." But if XMRV turns out not to be a very good etiology for real world cases of CFS, perhaps there might be more patience for those of us who urge not trying to explain all the many chronically fatigued patients with a single disease entity. In either case, it's worth recognizing the role that expert interpretation plays in medical controversies.

This post is long enough, and the second virus from the title of this piece will need to wait for a future post: I'll discuss the likelihood that we've really found an effective vaccine for HIV.

(After I wrote this, Marilyn Mann pointed me to a blog posting with some similar concerns about CFS having a specific viral etiology.)

Vitamins and Faith

I'd mentioned in an earlier post that a relative was prescribed fairly high dose vitamin D by her primary care physician despite a blood test showing that her vitamin D level was in the normal range. Her PCP may not be much of an outlier. Among the residents I work with, I've been encountering a lot of desire to prescribe vitamin D to pretty much everyone.

Why the willingness to administer vitamins? Would these same doctors feel that a drug with similar levels of evidence for safety and efficacy should be administered to tens of millions of generally healthy people?

Somehow patients and providers alike seem willing to treat vitamins as articles of faith -- as substances that must be good for humans based on their very name and nature. Yet the actual track record of vitamins, and particularly the fat-soluble vitamins, should not lead us to be so sanguine.

Based on their antioxidant properties, vitamin A/beta carotene and vitamin E were believed to be good for health before any reasonable studies had been performed. Doctors recommended beta carotene and vitamin E at moderate or high doses, and health-conscious patients took even higher doses. Then the results of randomized trials started to come in:

 Two large randomized trials of vitamin A/beta carotene found increased rates of lung cancer in smokers, pretty much putting an end to the notion of using beta carotene to prevent cancer. Then, a meta-analysis of trials of vitamin E found an apparent increase in mortality in patients treated with higher doses of vitamin E, and suddenly vitamin E no longer appeared so benign.

With this as a backdrop, we might expect physicians, at least, to show some skepticism before recommending other vitamins, and particularly other fat-soluble vitamins.

Yet, in their defense, vitamin D has been studied in randomized trials (mainly for prevention of fractures/osteoporosis), and these trials have reported other outcomes including cancer rates and mortality.

Although much larger trials have found no effects of vitamin D on cancer rates, one trial that I've heard people cite did indeed find a reduction in cancer rates in patients supplemented with calcium and vitamin D. The RR was 0.23 -- in other words, the supplementation appeared to reduce cancers by 77%. Since virtually nothing in medicine has an effect that large, and such an effect would be hard to have missed in other trials of calcium and vitamin D, this result seems implausible at best.

With regard to mortality, a meta-analysis of randomized trials found that vitamin D supplementation appeared to decrease mortality by 7%. A concern, though, is that the result was just barely statistically significant, and there could be reporting bias with regard to mortality: trials that found larger differences in mortality (or any other safety endpoint -- these were, after all, not trials designed to look at mortality) would be more likely to report on mortality than trials that found nothing interesting when they looked at their safety data. Given the risk that the results could be due to chance, even a small amount of reporting bias would be worrisome.

So, I've now objected to one trial of vitamin D for having too large an effect to be believable, and a meta-analysis for having too small an effect to convincingly rule out chance plus bias. Am I being fair and true to the evidence?

If we were talking about a therapy for a morbid illness where we were compelled to treat, I'd likely accept the evidence from the meta-analysis as being sufficiently hopeful to make vitamin D worth a try. After all if treatment is required, even if vitamin D eventually turned out to be harmful, we would know that we had needed to do something for the ill patient and so we made our best guess.

But that is not the case here. Instead, we are talking about administering a therapy to enormous numbers of healthy people with the hope of preventing disease, and where causing even small increases in harmful outcomes would have no justification. And remember the history of vitamin E and beta carotene. If that is not sufficient to make you concerned, read what happened to cancer rates and mortality in two trials of folate/B12 supplementation in Norway, published just last week in JAMA.

In such a situation we should wait for (and demand) more convincing evidence before we act. It may turn out that vitamin D really does prevent cancer, decrease mortality, and protect people from everything from influenza to the common cold. But I would rather be late jumping on this bandwagon than jump early and find that I hadn't learned a thing from past mistakes.

Pharma, Evidence, and Trust

A number of the other blogs that have noted the existence of this blog seem to have "Pharma" in their titles in one way or another, and the implication is not that the blogger likes much about Big Pharma.

In the late 1990s, when I was spending much of my clinical time providing HIV care, I was a defender of Pharma on Usenet, at least as it related to HIV. We'd discovered the HIV virus in 1985, and by late 1995 we had a spectacularly successful treatment, due, at least in part, to the efforts of the drug manufacturers. HAART changed the lives of people with AIDS, and the lives of their caregivers, and costs of $10K to $15K per year to keep a young person alive and functional seemed perfectly reasonable to me. I thought the carping about the high prices of these medications was unfair -- it was a remarkable accomplishment to find an effective treatment for a viral infection in so short a time, and the billions spent on it deserved some reward.

By a few years later, though, I was finding myself as distrustful and angry at Pharma as anyone out there. I spend a lot of my time reading research papers and interpreting evidence, and realized one day that Pharma was employing people at least as smart and knowledgeable as I to come up with ways to trick us all about what studies showed. One example of this is running parallel studies of an agent and then only publishing the positive studies while burying the negative studies, as was done with trials of SSRIs in adolescents. The concept of a p value becomes essentially meaningless if researchers perform an unknown N of parallel trials and then publish the ones that show a positive result.

I'll write about other ways of manipulating results in future posts, but for today I want to comment on one pernicious effect of this behavior -- I have come to distrust and then dislike the companies that provide the (often useful) drugs I must use on patients. When the new HDL-raising drug torcetrapib went down in flames a few years ago, I was actually pleased: I was furious with Pfizer for having tried to get torcetrapib approved in a way that would have only marketed it in a combo pill with atorvastatin. Objectively, it makes no sense that I should be happy at the failure of a drug that would have helped my patients had it worked.

Pharma not only tries to manipulate the interpretation of results of trials, in the design, analysis, and publication phases, they apparently also try to sow doubt about existing competitors. Adriane Fugh-Berman wrote in 2005 about how she was recruited to be the author on a ghost-written manuscript intended to highlight the importance of herbal interactions in patients on warfarin (interactions that Dr. Fugh-Berman felt were overstated). The company recruiting her was presumably working for AstraZeneca, the manufacturer of ximelgatran. Ximelgatran, a direct thrombin inhibitor that aimed to replace warfarin, was eventually withdrawn from the market in Europe (never approved in the US) because of hepatotoxicity.

In the face of this comes the RE-LY trial comparing warfarin with dabigatran, another direct thrombin inhibitor. I didn't start blogging until well after the publication of RE-LY, but hopefully others noted that this 18,000 person trial may reflect one of the biggest advances in medical therapy of the decade. Dabigatran appears to be a superior drug to warfarin -- at lower doses it is safer than wafarin and as effective, and at higher doses it is equally safe to warfarin and more effective. Unlike warfarin it does not require a careful diet or routine monitoring of INRs.

By all rights, dabigatran should take over the oral anticoagulation market, at least for atrial fibrillation (we need additional trials in other clinical settings). The natural skeptic in me would always want to wait a bit on using a new drug. Warfarin has been around for decades and has been used in tens of millions of people and we have a good sense of its benefits and (myriad) risks and burdens, while dabigatran has not been used nearly so widely nor for so long. New drugs have a habit of showing up rare side effects once they are out of clinical trials and on the market.

But my greater fear is that somehow Pharma is pulling something over on me, the editors of the NEJM that published RE-LY, and everyone else, and that it will somehow turn out that dabigatran not only isn't as big an advance as it appears, but that its manufacturers already know this and aren't telling.

Ultimately, if I had to bet, I don't think this will be the case with dabigatran. Five to ten years from now, I'm guessing that the residents I teach will have no clue that we used to routinely treat patients with rat poison and monitor bleeding parameters every couple of weeks or so in order to prevent clots and emboli. But I wish I didn't have to fear that the manufacturers of the drugs I use might not actually be working toward the same goals that I am, and instead might be working to fool me yet again.

USPSTF, Mammography, and Grading Recommendations

It's hard to have a blog about evidence and medicine without commenting on the changes to the USPSTF's breast cancer screening guidelines.

At a first pass, it's worth pointing out that a lot of academic primary care physicians have been wondering what the USPSTF was thinking when they published their 2002 guidelines recommending mammography for women in their 40s. Yes there may be some small benefits (and lots of harms), but this is just the sort of thing that the USPSTF can usually be relied on to not recommend -- look for instance at what they recommend for prostate cancer screening or lipid screening for women. As a result, there were lots of insinuations that the USPSTF had caved to political pressure in making the mammography recommendation. Perhaps others know more about that one way or the other.

Now they've backed away from that recommendation, going from a favorable to a negative recommendation for mammograms. The overall issues aren't actually that complex: if you imagine 1000 women in their 40's getting mammograms yearly for 10 years, the best estimates are that you will cause more than half of them to need repeat mammograms for concerning findings, and will cause nearly 200 to get breast biopsies, while only preventing 2 deaths from breast cancer.

What is remarkable is the firestorm that has been set off. When I present these data to women patients in their 40s (in a way that I think is fair to both sides of the argument), I've found that approximately half want mammography and half want to wait until they turn 50. Individual patient values and preferences heavily influence the decision. The USPSTF takes this into account by recommending against routine mammograms in the 40s, but states that a decision to screen should take consider an individual woman's values. All in all, not that unreasonable a position as far as I'm concerned.

I think, though, that the USPSTF's way of grading recommendations is awkward in general and may even have contributed to the confusion over their 2002 and 2009 recommendations. The evidence base didn't substantially change over that time frame, but the recommendations did, and that opens them to attack.

I think the USPSTF would be better off using a different grading system, such as GRADE, which they explicitly chose not to do recently.

(Here I need to make one of the only conflict of interest disclosures I should ever need to mention on this blog: one part of my work is as a medical editor, and in our publication we use GRADE.)

That out of the way, the USPSTF grading scheme is unusual in the way that it combines strength of recommendation and quality of evidence into a single value (a letter grade). To me, this overloading causes problems. For many of the recommendations that USPSTF gives a grade of I to (insufficient evidence), GRADE and a number of other schemes would note the low or moderate quality of the evidence and still allow a guideline committee or other recommending body to make a suggestion about what a clinician should do.

When there is enough evidence to make a suggestion (a "weak recommendation" in GRADE parlance), GRADE explicitly deals with the need for considering patient values and preferences. If, instead of being used to this single letter grade from USPSTF, we were used to seeing evidence and recommendation divided, I'm not sure the recommendation change would have caused quite so much trouble.

The USPSTF recommendation, cast into GRADE style, would likely have read:

For most women ages 40 to 50, we suggest not performing yearly mammography (Grade 2B). Women who are willing to accept a high risk of false positive mammograms and a high risk of unnecessary biopsies in return for a small mortality benefit may reasonably prefer annual mammography starting at age 40.

Would a recommendation written this way have caused the same firestorm? I'd be interested in what others think about this. Would it have caused a firestorm if the 2002 recommendation had said the opposite?:

For most women ages 40 to 50, we suggest performing yearly mammography (Grade 2B). Women who are unwilling to accept a high risk of false positive mammograms and a high risk of unnecessary biopsies in return for a small mortality benefit may reasonably prefer annual mammography starting at age 50.

You can see how easy it is to split the unchanged evidence base from the change in what you are suggesting for the majority of women (based on a guess about their values and preferences) when using GRADE. I think such an approach is more transparent than that used by the USPSTF, and keeps the focus where it belongs in a situation like this -- on the benefits, risks, and burdens that influence the decisions for individual patients and for society.

I'll write more about the methods of GRADE, including its strengths and weaknesses, down the road. I do want to say that while I don't like the grading scheme used by USPSTF, I think they mostly do a wonderful job of staying true to the evidence as they present their guidelines. We should all hesitate to recommend screening tests in the absence of solid evidence showing benefit, and the USPSTF can almost always be counted on in this regard.

ARBITER 6 and Combining Therapies with Statins

The results from ARBITER 6 were released this week.

The interpretation is less clear.

I've been in a minority who has doubted that most drugs that lower LDL are actually beneficial in primary prevention. Statins clearly show benefit, but really no other agents have shown a reduction in all cause mortality or, in primary prevention, in cardiovascular mortality. As such, I'd been raising concerns about ezetimibe even before ENHANCE was published, and have been unconvinced that anyone should be treated with combination therapy to achieve LDL goals, since there is little to suggest added benefit when other lipid-lowering drugs are combined with a statin.

Recently, the Oxford Niaspan Study found that CIMT was improved when niacin was combined with a statin, but CIMT is a surrogate marker and it's not so clear that changes in CIMT will predict clinical benefits. However, of all the non-statin therapies, niacin has been the one that looks most promising for reducing cardiovascular mortality, at least in secondary prevention.

Now, soon after that study, we have ARBITER 6, showing that niacin plus a statin seemingly reduced cardiovascular events compared with ezetimibe plus a statin. There were 2 events in the niacin arm (1%) and 9 in the ezetimibe arm (5%) and this was statistically significant. So, what can we conclude from this?

One possibility is that niacin actually does add some clinical benefit to a statin in secondary prevention, while ezetimibe does not.

Another possibility is that ezetimibe is actively harmful, while niacin is neutral. There were slightly more events in ENHANCE in the ezetimibe arm, but the numbers were tiny.

A third possibility is that this was due to chance. The actual results are quite "fragile" in the sense that only a few events moving from one arm to the other would make the difference disappear. While, in theory, a statistical test captures this, there's been a sense in the EBM world that very small event numbers create a fragility of results not adequately captured by a p value. It seems extremely unlikely that niacin really reduces events by 80%, since this should have been obvious in prior trials of niacin. As such, either niacin combined with a statin is much superior to niacin alone, or these results are in part due to the play of chance. (It's not likely that ezetimibe raises events by this degree when used with a statin, since we would likely have noticed this in other trials.)

ARBITER 6 was stopped early for benefit, based on CIMT results. This seems like an odd decision to say the least, since change in CIMT is not a clinical outcome requiring an ethical decision to stop a trial. The early stopping was unfortunate since with more events we might be more certain about whether the reduction in events was real.

I'll be interested to see how others interpret ARBITER 6. So far I've communicated with one lipid expert (who has not shared my views about non-statin therapy) and he doesn't believe that ezetimibe is clearly to be avoided, while another expert (who does share my views about non-statin therapy) doesn't feel that ARBITER 6 means that niacin should be used. Apparently neither one found ARBITER 6 substantially reshaped their positions on this.

My best guess is that niacin reduces events a bit, though not as much as ARBITER 6 suggests. If so, for the highest risk patients, such as those who have CV events while on a statin, adding niacin might make sense. Given the side effects with niacin (36% of patients in ARBITER 6 had  flushing, and many more in the niacin arm than the ezetimibe arm discontinued therapy), I'd hesitate to use niacin in lower risk patients even for secondary prevention, out of concern that they might discontinue both niacin and the statin.

I'd be quite hesitant to treat anyone with ezetimibe at this point. While I was a skeptic that ezetimibe did anything beneficial even before ARBITER 6, I'm now substantially more concerned that it could be causing real harm.

Opinion, Evidence, and Consensus Statements

In the future, I'll write more about this subject, since the distinction between expert opinion and clinical experience seems to cause unending confusion to people who write and talk about EBM.

For now, though, I want to write about the second recent event that caused me to decide to blog on evidence and medicine. I caught a snippet on NPR's Science Friday where they were talking about concussions in athletes and heard the following: "And take a very careful step-wise return not just to the playing of the sport, but also to even, you know, text messaging and doing things intellectually that can be harmful to their brains while they're still recovering from a concussion." www.npr.org/templates/story/story.php?storyId=120174333

I was startled to hear that an expert thought that someone should not be texting after a concussion (it turns out this is referred to as "cognitive rest"), and I had a hard time believing there was any evidence for it. And though I have no expertise in concussion management, the idea sounded somewhat contrived or even goofy to me.

It turns out that this mainly comes from consensus guidelines for the management of concussion (PMID 19433429) where, if they have any evidence to back this up, I couldn't find it. I certainly didn't find any published studies showing that cognitive rest improves outcomes after a concussion. If anyone reading this knows of such evidence, I'd be interested to see it.

To make recommendations, experts always need to interpret what evidence there is (expert opinion), and in the absence of high or moderate quality evidence about cognitive rest, the consensus panel presumably had to make their best guess for management. This particular recommendation seems a bit odd in that it has potentially high burdens on the injured athlete (don't read; don't text) in the absence of good evidence, and rest is not always such a good idea after a physical injury -- bed rest for low back pain and immobilization for an injured shoulder are both clearly a bad idea. But ultimately doctors need to either recommend cognitive rest or not recommend it and if some people think it's a good idea an expert recommendation is required.

However, a certain degree of humility would seem to be required when transmitting a recommendation grounded in such low quality evidence. Perhaps this is not such an instance, and I am just missing the better evidence, but it would certainly be common to hear expert panels and individual doctors make forceful pronouncements based on little or no foundation. If there really is nothing much to support this, perhaps the experts describing the recommendation (both in the guideline and on the radio) might have said, "Well, we think cognitive rest is a good idea, but we don't really know. In fact, for all we know, it might do more harm than good."

So, while I'll write more about expert opinion and clinical experience down the road, this episode of seeing yet another consensus guideline treated as gospel was an added push to create this blog.

First post and origins

Although an early participant in the world of Usenet newsgroups, I'm a latecomer to the world of blogging. I don't read or participate in blogs often, and as a newbie will undoubtedly make mistakes of etiquette and function much as I did in the very early days of Usenet before I got a feel for the music of the newsgroups. I hope anyone reading this will take this into account and cut me some slack!

I'd been considering for a while now blogging about evidence and medicine, something I spend a fair amount of my time thinking about in any case, but a couple of events pushed me to take the plunge.

The first was when a relative, a woman in her mid-40's, called to tell me that she'd seen her new primary care doctor. The doctor had run tests on her including checking a lipid profile. The lipid profile showed a total cholesterol of 160, an HDL of 44, and an LDL of 105. Based on these results, the doctor informed her that she should be very concerned about her "low" HDL number and told her to start taking fish oil.

This was an interesting interpretation of the results and an unusual suggestion for management, and it gives some sense of my concerns about how evidence is used, ignored, or misused in medicine. This relative had a low normal blood pressure, no smoking history, did not have diabetes, and had no family history of coronary heart disease. As such, there is even  some controversy as to whether she should have had a lipid profile checked at all.

Assuming a lipid profile was worth doing, she should certainly have been told that this was an excellent profile putting her at low risk for a cardiovascular event, and that there was little modern medicine could do to substantially affect her risk. Her 10-year risk of an event (using the 2008 calculator that overestimates vascular risk by including things that probably shouldn't be included -- a blog for another day) works out to about 2.2%. If we pretend that somehow fish oil could increase her HDL to 80 and that she would get all the same benefit as if her HDL were naturally 80, we could drop her calculated risk to about 1.4%. So, if she took medication daily for 10 years, she would reduce her risk of an event (under these outlandishly favorable assumptions) by 0.8%. Not something this relative was interested in doing.

But, do we even know that fish oil raises HDL? The main effect of fish oil on lipids is to lower triglycerides. Most studies suggest that fish oil only raises HDL levels by about 3%, so we might expect an increase from an HDL of 44 to an HDL of 45. It's hard to see how the doctor felt this would fix the woman's "low" HDL.

But, beyond that, we have no solid evidence that raising HDL with  medication improves outcomes. Changing HDL with medication is a surrogate outcome for that medication  -- that is, it is of no direct interest to the patient unless it also predicts better cardiovascular outcomes, and HDL appears to be a poor surrogate.  Some medications that raise HDL appear to cause harm and worse vascular outcomes.

As for whether fish oil supplements are beneficial through some non-HDL mechanism, I think we can safely say that the jury remains out as to whether a woman in her 40s at low cardiac risk could expect any important benefit from fish oil supplementation.

Interestingly, my relative's doctor also checked her vitamin D level and told her that a level of 34 (in the normal range) was concerningly low and that she should start taking 1000 IU of vitamin D per day (she was already taking 400 IU). Vitamin D supplementation is controversial, with lots of people claiming big benefits, but we can safely say for now (again, perhaps a longer blog for another day) that there is no solid evidence that having a woman with a normal vitamin D level start taking additional vitamin D is likely to be of any benefit to her.

My relative asked what I thought these events said about her doctor, but I'm not really sure. I see decisions like this made all the time, where evidence is misunderstood, misapplied, or ignored. I have the sense that this particular doctor may believe she is getting out ahead of the evidence -- suggesting therapies that she believes will be proven down the road to be of benefit. She could, of course, turn out to be right, but we should be very hesitant to give preventive medications without a decent evidentiary basis. Other drugs that raise HDL have increased mortality. Supplementation with other vitamins that were thought beneficial has turned out to cause cancer or increase mortality.

I said there were a couple of events that prompted me to start this blog, but this post seems long enough. I'll talk about other events in future postings.