Am I missing something?

The cover of this week’s Lancet, in bold: “No doctor should be practicing, even after that single glass of cold Chardonnay”.

This refers to a brief editorial on the topic, “Just one before the scalpel“. In that editorial, the Lancet states:

“The individual response to alcohol varies greatly, depending on sex, body size, eating food, taking other drugs (eg, antihistamines), and the complexity of the impending task. Because of the unpredictability of the response, no alcohol in the blood when on call must become the norm. Indeed, other professions face that stricture. For example, UK pilots are not meant to fly for at least 8 h after drinking even small amounts. US pilots face stricter rules: no drinking within 8 h of take-off.”

Now let’s see. No drinking within 8h of take-off is stricter than not flying for at least 8h after drinking. Am I missing something? Or have the proof-readers at the Lancet been sneaking off to their local pub?

Women and non-smokers need not apply

The new USPSTF recommendations concerning screening for AAA appear in this week’s Annals of Internal Medicine, and are being quoted in the press.

Bottom-line: screen men who have ever smoked, once between the ages of 65 and 75.

  • Under 65: too low morbidity/mortality to make screening worthwhile
  • Over 75: too high co-morbidities to make a big difference.
  • Smoking status: 90% of AAA mortality found in the 70% of men who have ever smoked.
  • Women: incidence of AAA in 65-75 year old group too low to make screening sufficiently beneficial.

This is all fine, but the way the conclusions are presented, it is as if, in the non-recommended groups, the harms of screening outweigh the benefits. I don’t think the data support this. The data just suggest that in these groups, screening simply isn’t cost-effective or sufficiently beneficial. The task force concludes:

“Because of the low prevalence of large AAAs in women, the number of AAA-related deaths that can be prevented by screening this population is small. There is good evidence that screening and early treatment result in important harms, including an increased number of surgeries with associated morbidity and mortality, and psychological harms. The USPSTF concluded that the harms of screening women for AAA outweigh the benefits.”

As I see it, the real point is not that the harms of screening women outweigh the benefits. The same harms that apply to women apply to male smokers. It’s rather that the number of deaths that can be prevented by screening this population is too small to recommend it. But that doesn’t quite sound good enough. When telling someone they will not be screened, it sounds much better if you say “the risks outweigh the the benefits”. Even if that’s not clearly supported by the data.

Is spin doctoring now a medical specialty?

Vioxx and the 140,000 MI’s

As I previously noted here, a study by Graham et al, examining the cardiovascular risks of Vioxx, was being considered for publication in the Lancet when it was prematurely published on the FDA’s website, much to the Lancet’s dismay. Today, that same study, with some modifications, has been published online at the Lancet. It is being widely quoted in the press, particularly the assertion that Vioxx is shown to be responsible for 88,000 to 140,000 excess cases of serious coronary heart disease in the United States between 1999 and 2004. Let us take a closer look at this assertion.

The study itself is from Kaiser Permanente. It is a nested case-control study of 1,394,764 persons who were exposed to various NSAIDs between 1999 and 2001. The subset of patients who had myocardial infarction or sudden death from coronary disease were identified and constituted the cases. They were each matched to 4 controls from the overall group (matched for age, sex and health-plan region). In the Lancet study published today, the various types of NSAIDS were then evaluated for the odds-ratio of coronary events compared with remote use of NSAIDS (basically similar to non-users) and compared with celecoxib. This study found that Vioxx users had an increased risk of coronary events of 1.34 compared to remote users, and 1.5 compared to current users of celecoxib. This risk increase was particularly significant for high dose Vioxx (3.00 compared to remote users and 3.58 compared with celecoxib users).

Apart from the the usual caveats that apply to non-randomized cohort studies, I don’t have much of a problem with this part of the study. It becomes more interesting when the excess morbidity from Vioxx is considered.

In the original report published on November 2 at the FDA’s website, the authors state in their discussion:

High-dose rofecoxib conferred a 3.7-fold increase in risk and standard-dose a 1.5-fold increase compared with celecoxib, the most frequently prescribed COX-2 selective agent… From 1999 to 2003, there were an estimated 92,791,000 prescriptions for rofecoxib, of which 17.6% were high-dose. Combining this with data on mean prescription length, we estimate that the increased rofecoxib risk observed in this study would yield an excess of 27,785 cases of AMI and SCD in the US over the years 1999-2003, with 53.4% due to standard-dose use.

Now compare this statement, which estimated an excess of 27,785 cases of AMI and SCD, with the following statement in the conclusion of today’s Lancet paper:

From 1999 to September, 2004, an estimated 106.7 million rofecoxib prescriptions were dispensed in the USA, of which 17.6% were high-dose. In two Merck-sponsored randomised clinical trials relative risks for acute myocardial infarction of 5 for high-dose rofecoxib and 2 for the standard dose were recorded. The background rate for acute myocardial infarction among control groups from studies of cardiovascular risk in NSAID users varied from 7.9 per 1000 person-years in CLASS to 12.4 per 1000 person-years in TennCare. Using the relative risks from the abovementioned randomised clinical trials and the background rates seen in NSAID risk studies, an estimated 88,000–140,000 excess cases of serious coronary heart disease probably occurred in the USA over the market-life of rofecoxib.

Note that here, the authors use relative risks for MI of 5 and 2 for their calculations, which they did not derive from their own data but rather from two trials that have nothing to do with their study. They then use these numbers to come up with estimates of excess cases of serious coronary disease between 88,000 and 140,000, rather than the 27,785 from their original analysis (the slight increase in prescriptions used in the calculations only accounts for a small fraction of the difference).

It is very possible that the latter numbers more accurately reflect the truth than the former ones. And I am quite convinced of the excessive cardiovascular risk of Vioxx. Nevertheless, it seems disingenuous, at best, to publish a large trial whose primary purpose is to estimate the cardiovascular risk from Vioxx, and then, in the conclusion, calculate the number of patients harmed using risk estimates from totally different studies, without even mentioning that this is what is being done. And, of course, the number 140,000 is what gets picked up.

Politics, politics.

Aspirin vs. Plavix after upper GI bleeding

What a frustrating paper.

In last week’s NEJM is a study from the Prince of Wales Hospital in Hong Kong looking at clopidogrel versus aspirin and esomeprazole to prevent recurrent ulcer bleeding. More precisely, the authors studied patients who had been on 325 mg aspirin or less, who presented with upper GI bleeding and who were either H. Pylori negative or successfully treated. These patients were then randomized to either 80 mg of aspirin daily plus 20 mg of Nexium (esomeprazole) twice daily, or to 75 mg of Plavix alone. They were then followed for a year.

Recurrent upper-gastrointestinal bleeding occurred in 13 patients on Plavix and in only one patient on aspirin-Nexium. The authors’ last sentence: “Our observations do not support the current recommendation that clopidogrel be used for patients who have major gastrointestinal intolerance of aspirin”. The editorial in the same issue also discusses the question of what to do with patients who have had gastointestinal complications while taking aspirin, and says of the ACC/AHA recommendation to replace aspirin with clopidogrel: “The study by Chan et al. clearly indicates that this recommendation is harmful and that such patients should be given aspirin plus a proton-pump inhibitor.”

Not. At least, not exactly.

Patients who have just had a significant upper GI bleed while taking modest or low dose aspirin are clearly at a high risk for rebleeding, particularly if they are not on long-term acid suppression. So if you randomize these patients to either low-dose aspirin plus a PPI or to Plavix alone, it is not terribly surprising that the Plavix-only patients have a higher incidence of recurrent ulcer bleeding. This is a very unsatisfying comparison. On the one hand a drug, aspirin, that is clearly ulcerogenic and also promotes bleeding taken together with a drug that effectively prevents ulcers (omeprazole). On the other hand, a drug (Plavix) that may be less ulcerogenic but is even more likely to promote bleeding and given without any ulcer prevention. This comparison just muddies the waters. This study does not help distinguish the platelet-antagonizing effect of clopidogrel from any direct effect on the healing of ulcers.

Can anything be learned from this study? Mainly that, in patients with aspirin-induced upper GI bleeding who are H Pylori negative, Plavix should not be given alone as an alternative to aspirin plus a PPI.

It would seem that, in these patients, it is relatively safe to prescribe aspirin plus a PPI. Perhaps Plavix plus a PPI would be even safer, but this is pure speculation; this trial does nothing to address this issue one way or the other. What this means for patients who have gastro-intestinal intolerance of aspirin other than upper GI bleeding is unclear. Patients who have a good reason for being on clopidogrel (such as a recently implanted stent) should not be switched to aspirin plus a PPI alone if they have a GI bleed, at least not on the basis of this study.

Clopidogrel is a very popular and quite expensive drug, and I am annoyed by its overly aggressive promotion by drug reps, but this study doesn’t give me any ammunition in resisting its use.

More on CRP

The two NEJM articles on C-Reactive Protein which I commented on yesterday have raised quite a stir.

Gina Kolata’s headline in the NY Times that I saw in my print paper yesterday blared: “Two Studies Suggest a Protein Has a Big Role in Heart Disease“. Today, I went to the Times website to find the exact wording of that headline, and did a quick search for CRP. The search yielded two results pointing to that same article: one had the headline that was worded as above, and a second with a different headline: “Protein Is Factor in Heart Disease, Researchers Say”. Hmm. And today, Kolata has a more subdued article entitled: “A Quandary in Good News“.

The two studies really show only one thing: If you have coronary disease and if you are treated with a statin, then you do better if your CRP is lower (or drops more) than if it doesn’t. That’s it. They do raise a bunch of unanswered questions, however:

  • Is CRP an active participant or just a marker? If it is an active participant, then lowering CRP levels should, indeed, be a direct priority and researchers should be looking at ways to do this. If it is just a marker, then what, exactly, is it a marker for? Is there some other factor that we should be targetting, rather than the CRP?
  • Granted that statin therapy can lower CRP, is it possible to lower it more with more intensive therapy? How much lower? Using what drugs or drug combinations?
  • And even if patients whose CRP’s drop more with statin therapy do better than those whose CRP’s drop less, does this mean that using drug manipulation to push the levels of the “poor responders” down further will guarantee the same outcome?
  • What about non-vascular causes of inflammation? What do those elevated CRP levels mean for cardiovascular prognosis? And are there any non-vascular conditions that lower CRP levels (like CHF can lower sedimentation rates)?
  • If we want to use the CRP to guide our choice of and aggressiveness with therapy, how often should we be measuring it? Find out from your local laboratory what they charge for a lipid panel and what they charge for a CRP. Presumably prices will drop, but it will still be one added expense that will be multiplied millions of times.

Lots of stuff still to be learned. And lots of phone calls from patients to be fielded.

CRP and statins

Today’s NEJM has two articles on statin therapy and achieved LDL and CRP levels in relation to coronary disease.

The first article, from Harvard, is a substudy of the Pravastatin or Atorvastatin Evaluation and Infection Therapy – Thrombolysis in Myocardial Infarction 22 study (I challenge you to reread the name of this study once and then repeat it from memory). This trial was a 2×2 study of 80 mg vs. 40 mg of atorvastatin and of the antibiotic gatifloxacin vs. placebo, looking at event rates in 3745 patients who had had acute coronary syndromes. In this substudy, LDL levels and CRP levels were evaluated at 30 days after randomization.

Statin therapy reduced LDL levels significantly; CRP levels were also reduced. There was very little correlation between LDL levels achieved and CRP levels achieved. Cardiac event rates correlated independently with both LDL and CRP. In other words, lower CRP levels correlated with lower event rates, independently of achieved cholesterol reduction.

The second study, from the Cleveland Clinic, was also a substudy of another trial, Reversal of Atherosclerosis with Aggressive Lipid Lowering (REVERSAL), which examined atherosclerosis progression using intracoronary ultrasound in patients randomized to 80 mg of atorvastatin vs. 40 mg of pravastatin. Ultrasound was performed and lipids and CRP were obtained at baseline and after 18 months.

The results of this trial were similar to the first: there was little correlation between CRP and lipid levels. Atherosclerosis progression was independently correlated with both LDL and CRP changes between baseline and follow-up.


Now that the homocysteine fad has waned a bit, commercial laboratories are aggressively promoting profitable high sensitivity CRP measurement. It certainly is an interesting concept, since atherosclerosis is not the gradual, pipe-clogging process that it used to be viewed as, but rather a much more dynamic and inflammatory one. Inflammation and CRP are related, and CRP has prognostic value in vascular disease. It may well turn out that targetting CRP levels when deciding on and dosing statin therapy will be just as important as following LDL levels. Perhaps CRP will allow us to forgo statin therapy in some patients and force us to be more aggressive in others.

However, just because statin-treated patients with lower CRP reductions do better than those with lesser reductions does not automatically prove that targetting statin doses to CRP levels will guarantee the same results. What is needed is a clinical trial that demonstrates that patients whose therapy is guided by CRP do as well as patients whose therapy is fixed and high-dose, for example.

Having said that, the increasingly convincing inflammatory theory of atherosclerosis does make measurement and use of the CRP attractive. One more piece of the puzzle.

Coronary revascularization before vascular surgery

Patients undergoing vascular surgery are at higher risk for cardiovascular events. Despite published guidelines, the exact approach to pre-operative cardiac evaluation for these patients varies significantly. The report of a VA cooperative study in last week’s NEJM looked at the value of prophylactic coronary-artery revascularization before elective major vascular surgery.

Patients undergoing elective AAA repair or surgery for PVD of the legs were referred for cardiac catheterization if they were felt to be at increased risk for cardiac complications. The exact reasons for referral were variable and included abnormal thallium stress test and high risk based on clinical criteria. Patients were then eligible for randomisation if they had significant coronary disease of at least one vessel and did not have left main disease, aortic stenosis or an EF less than 20%.

510 patients were randomized to either prophylactic revascularization (CABG or angioplasty, at the discretion of the cardiologists) or no revascularization. In the revascularization group, 99 underwent CABG, 141 angioplasty. After mean follow-up of 2.7 years there was no difference in mortality in the two groups (about 22%).

This is the first study to randomize patients to yes-or-no cardiac revascularization prior to vascular surgery. Given the improvement in medical therapy and the peri-operative use of beta-blockers (84% of patients received them in this study), the result is not surprising but is important.

There are some caveats: patients with left main disease were excluded from randomization. Thus, one cannot use these results to say that there is never a need for pre-operative coronary angiography. Furthermore, no-revascularization prior to vascular surgery is not “never” — 8% of patients randomized to this approach underwent coronary revascularization after their elective surgery.

Accupuncture for knee pain (and two other articles)

In the Annals of Internal Medicine due out on December 21 are three “alternative medicine” articles.

The lead article, effectiveness of acupuncture as adjunctive therapy in osteoarthritis of the knee, randomized 570 patients with osteoarthritis of the knee to one of three interventions: a 26 week tapering schedule of acupuncture, sham acupuncture, or six 2-hour group sessions of education. The patients were evaluated at 4, 8, 14 and 26 weeks for improvement in five areas: a pain score, a function score, a global assessment score, a physical health score and a 6-minute walking distance test.

Acupuncture provided statistically significant benefit over sham acupuncture and over the education alone approach at 26 weeks in terms of the pain, function and global assessment scores. The authors conclude: “Acupuncture seems to provide improvement in function and pain relief as an adjunctive therapy for osteoarthritis of the knee when compared with credible sham acupuncture and education control groups.”

I have two comments to make about this paper. First, similarly to my remarks about the paper on effectiveness of vestibular rehabilitation for the treatment of vertigo, I would have liked to see some measure that expresses in plainer english the results of the study. What percentage of patients would, at the end of trial, consider repeating the therapy? How many would consider recommending it to their family or friends? Clearly there is a benefit, but it’s hard to contextualize that benefit, to get a handle on how clinically worthwhile it is.

A second point relates to the results themselves, presented in Table 2 of the paper. The change from baseline for all five measurements is reported for the three groups (true acupuncture, sham acupuncture and education) at weeks 4, 8, 14 and 26. Taking one example, the WOMAC pain score was approximately 8.95 at baseline in the three groups. At week 4, it improved by 2.22 in the true acupuncture group, by 1.98 in the sham acupuncture group and by 0.84 in the education group.

This means that the benefit of true acupuncture over education was 2.22-0.84 = 1.38. Similarly, the benefit of sham acupuncture over education was 1.98-0.84 = 1.14. In this case, if the benefit of true acupuncture over education was 1.38, and that of sham acupuncture over education was 1.14, then one might conclude that 1.14/1.38 = 83% of the benefit of true acupuncture was due to the placebo (sham acupuncture) effect. I realize that this may not be a statistically correct assumption, but I believe it does represent a reasonable approximation. I would love to hear what statisticians have to say about this.

At any rate, I performed the same calculation for the other results given in Table 4, and came up with the following numbers:

  • For the improvement in WOMAC pain score, at weeks 4, 8, 14 and 26, the percentages of the improvement attributable to placebo acupuncture were: 83%, 74%, 55% and 59%.
  • For the improvement in WOMAC function score, at weeks 4, 8, 14 and 26, the percentages attributable to placebo acupuncture were: 43%, 46%, 58% and 52%.
  • For the patient global assessment score, the corresponding percentages were: 50%, 38%, 52% and 0% (no effect from sham acupuncture).

Although these numbers are derived by me and may not be strictly correct, I think they do give an idea that about half of the benefit from acupuncture in this study was due to a generic placebo effect equivalent to sham acupuncture, and about half of the effect was specific to the real treatment. That’s not a bad overall result for acupuncture, considering how important the placebo effect is pain therapy.

Two other articles from the same issue:

Acupuncture versus placebo for the treatment of chronic mechanical neck pain was a single-blind randomized study comparing acupuncture with sham electrical stimulation of acupuncture points (placebo) for chronic neck pain. Although there was a statistically significant benefit of acupuncture over the placebo, this benefit was only of modest degree and felt to be not clinically significant.

More interesting was a clinical prediction rule to identify patients with low back pain most likely to benefit from spinal manipulation. The authors used a clinical prediction rule with 5 components:

  • length of current episode (component positive if < 16 days)
  • symptoms below the knee (absent)
  • level of fear of pain and avoidance of activity (low)
  • presence of hypomobile lumbar spine segments (at least one)
  • internal rotation at the hip (> 35 degrees)

When four out of five of these components were positive (about 1/3 of patients), there was a substantially better outcome with spinal manipulation than with exercise alone and also better than with spinal manipulation in the 2/3 of patients who did not score well on the prediction rule. The only problem I have with the applicability of this study is that the prediction rule was evaluated by a physical therapist. How easy it would be for primary practitioners to successfully perform the same evaluation is unclear to me.

MRI for breast imaging

Last week’s JAMA had an article on magnetic resonance imaging of the breast prior to biopsy, which evaluated the performance of MRI imaging in evaluating patients with breast abnormalities. This study found that MRI had good sensitivity but only moderate specificity for detecting cancer. The negative predictive value of MRI was only about 85%, not high enough to obviate the need for biopsy.

In the same issue is an excellent editorial by Monica Morrow from Fox Chase Cancer Center in Philadelphia, Magnetic resonance imaging in breast cancer — one step forward, two steps back?

Dr. Morrow discusses the role of MR imaging of the breast. She notes that at present there are two main scenarios in which MRI is being used: for the screening of women at high risk for breast cancer, and for supplemental evaluation of patients with abnormalities of the breast.

The screening of women at high risk, such as those with BRCA mutations, lends itself to MRI evaluation, because these women are often younger, with denser breast tissue, a situation where MRI has an advantage over conventional mammography.

On the other hand, using MRI to evaluate patients with breast abnormalities (clinical and/or mammographic) is a different matter. As demonstrated in the study, the specificity and negative predictive value of MRI are not sufficient to allow the avoidance of breast biopsy. Nevertheless, MRI is being used more and more in this context. Why? Because of the perception that it is more sensitive and can pick up multicentric lesions better than mammography. Thus, it can be used to make decisions about the appropriateness of local (breast-sparing) treatment.

Here, Dr. Morrow makes an interesting point. Although MRI can pick up multicentric cancers with greater sensitivity than mammography, she argues that the need for mastectomy in these cases is not clear. She draws a parallel to the 1970’s, when breast-sparing surgery was being investigated. At that time, pathologic studies indicated that breast cancer was often multicentric; this was used to argue against the advisability of limited surgery. However, clinical trials showed that as long as the surgical margins were clean, breast-sparing surgery plus radiation of the breast yielded excellent results. Analogously, the detection of multicentric cancers by MRI may push towards mastectomy, but without clinical trials it isn’t clear that this will yield better results.

Breast cancer is out of my area of expertise, but this editorial was short, easy to read and thought-provoking.

The situation Dr. Morrow describes reminds me a bit of a recent development in cardiology, the advent of non-invasive methods for visualizing coronary arteries (CT angiography). Visual evidence is very convincing, and there is a strong urge to act upon what we see. Paradoxically, the ability to visualize coronaries non-invasively may well increase the number of invasive procedures, as the instinct to open up tight lesions will be hard to resist. Whether this will always be the right thing to do is another question.

In both cases, seeing is believing, but belief isn’t always the best basis for action in medicine.

Ablation for atrial fibrillation — author’s reply

In my post about the recent NEJM article on ablation for atrial fibrillation, I commented that “… it is not clear to me how exactly to evaluate a comparison of an ejection fraction in atrial fibrillation (the baseline) with one obtained in normal sinus rhythm…”

The corresponding author of this article, Dr. Pierre Jais, has emailed me this reply:

I would like to thank you for your comments and interesting web site.

I just would like to emphasize that the baseline echographic EF was acquired just after the ablation procedure, in sinus rhythm, to overcome the
limititation you pointed out.

Best regards.

Pierre Jais

I went back to the article, to see if I had misunderstood or misstated the methods. The description of the echocardiographic determination of ejection fraction at baseline is as follows:

Patients were routinely admitted two days before the ablation procedure for baseline evaluation. Treatment with oral anticoagulants, taken by all the patients, was stopped on admission, and treatment with all antiarrhythmic drugs, except amiodarone, was stopped for an appropriate period before ablation. Heart rate and rhythm were monitored with the use of 48-hour ambulatory electrocardiography. Transesophageal echocardiography was performed to rule out atrial thrombi, and transthoracic echocardiography was performed to evaluate cardiac structure and function. Echocardiographic measurement of the left ventricular ejection fraction was standardized with the use of Simpson’s biplane method for all patients during the initial hospitalization and subsequent visits.

From the above description, I don’t think it was unreasonable to assume that the initial EF was determined while the patients were still in atrial fibrillation.

Thus, the author’s reply represents a significant clarification.