The publication asymmetry: What happens if the New England Journal of Medicine publishes something that you think is wrong?

After reading my news article on the replication crisis, retired cardiac surgeon Gerald Weinstein wrote:

I have long been disappointed by the quality of research articles written by people and published by editors who should know better. Previously, I had published two articles on experimental design written with your colleague Bruce Levin [of the Columbia University biostatistics department]:

Weinstein GS and Levin B: The coronary artery surgery study (CASS): a critical appraisal. J. Thorac. Cardiovasc. Surg. 1985;90:541-548.

Weinstein GS and Levin B: The effect of crossover on the statistical power of randomized studies. Ann. Thorac. Surg. 1989;48:490-495.

I [Weinstein] would like to point out some additional problems with such studies in the hope that you could address them in some future essays. I am focusing on one recent article in the New England Journal of Medicine because it is typical of so many other clinical studies:

Alirocumab and Cardiovascular Outcomes after Acute Coronary Syndrome

November 7, 2018 DOI: 10.1056/NEJMoa1801174

BACKGROUND

Patients who have had an acute coronary syndrome are at high risk for recurrent ischemic cardiovascular events. We sought to determine whether alirocumab, a human monoclonal antibody to proprotein convertase subtilisin–kexin type 9 (PCSK9), would improve cardiovascular outcomes after an acute coronary syndrome in patients receiving high-intensity statin therapy.

METHODS

We conducted a multicenter, randomized, double-blind, placebo-controlled trial involving 18,924 patients who had an acute coronary syndrome 1 to 12 months earlier, had a low-density lipoprotein (LDL) cholesterol level of at least 70 mg per deciliter (1.8 mmol per liter), a non−high-density lipoprotein cholesterol level of at least 100 mg per deciliter (2.6 mmol per liter), or an apolipoprotein B level of at least 80 mg per deciliter, and were receiving statin therapy at a high-intensity dose or at the maximum tolerated dose. Patients were randomly assigned to receive alirocumab subcutaneously at a dose of 75 mg (9462 patients) or matching placebo (9462 patients) every 2 weeks. The dose of alirocumab was adjusted under blinded conditions to target an LDL cholesterol level of 25 to 50 mg per deciliter (0.6 to 1.3 mmol per liter). “The primary end point was a composite of death from coronary heart disease, nonfatal myocardial infarction, fatal or nonfatal ischemic stroke, or unstable angina requiring hospitalization.”

RESULTS

The median duration of follow-up was 2.8 years. A composite primary end-point event occurred in 903 patients (9.5%) in the alirocumab group and in 1052 patients (11.1%) in the placebo group (hazard ratio, 0.85; 95% confidence interval [CI], 0.78 to 0.93; P<0.001). A total of 334 patients (3.5%) in the alirocumab group and 392 patients (4.1%) in the placebo group died (hazard ratio, 0.85; 95% CI, 0.73 to 0.98). The absolute benefit of alirocumab with respect to the composite primary end point was greater among patients who had a baseline LDL cholesterol level of 100 mg or more per deciliter than among patients who had a lower baseline level. The incidence of adverse events was similar in the two groups, with the exception of local injection-site reactions (3.8% in the alirocumab group vs. 2.1% in the placebo group).

Here are some major problems I [Weinstein] have found in this study:

1. Misleading terminology: the “primary composite endpoint.” Many drug studies, such as those concerning PCSK9 inhibitors (which are supposed to lower LDL or “bad” cholesterol) use the term “primary endpoint” which is actually “a composite of death from coronary heart disease, nonfatal myocardial infarction, fatal or nonfatal ischemic stroke, or unstable angina requiring hospitalization.” [Emphasis added]

Obviously, a “composite primary endpoint” is an oxymoron (which of the primary colors are composites?) but, worse, the term is so broad that it casts doubt on any conclusions drawn. For example, stroke is generally an embolic phenomenon and may be caused by atherosclerosis, but also may be due to atrial fibrillation in at least 15% of cases. Including stroke in the “primary composite endpoint” is misleading, at best.

By casting such a broad net, the investigators seem to be seeking evidence from any of the four elements in the so-called primary endpoint. Instead of being specific as to which types of events are prevented, the composite primary endpoint obscures the clinical benefit.

2. The use of relative risks, odds ratios or hazard ratios to obscure clinically insignificant differences in absolute differences. “A composite primary end-point event occurred in 903 patients (9.5%) in the alirocumab group and in 1052 patients (11.1%) in the placebo group.” This is an absolute difference of only 1.6%. Such small differences are unlikely to be clinically important, or even replicated on subsequent studies, yet the authors obscure this fact by citing hazard ratios. Only in a supplemental appendix (available online), does this become apparent. Note the enlarged and prominently displayed hazard ratio, drawing attention away from the almost nonexistent difference in event rates (and lack of error bars). Of course, when the absolute differences are small, the ratio of two small numbers can be misleadingly large.

I am concerned because this type of thing is appearing more and more frequently. Minimally effective drugs are being promoted at great expense, and investigators are unthinkingly adopting questionable methods in search of new treatments. No wonder they can’t be repeated.

I suggested to Weinstein that he write a letter to the journal, and he replied:

Unfortunately, the New England Journal of Medicine has a strict limit on the number of words in a letter to the editor of 175 words.

In addition, they have not been very receptive to my previous submissions. Today they rejected my short letter on an article that reached a conclusion that was the opposite of the data due to a similar category error, even though I kept it within that word limit.

“I am sorry that we will not be able to publish your recent letter to the editor regarding the Perner article of 06-Dec-2018. The space available for correspondence is very limited, and we must use our judgment to present a representative selection of the material received.” Of course, they have the space to publish articles that are false on their face.

Here is the letter they rejected:

Re: Pantoprazole in Patients at Risk for Gastrointestinal Bleeding in the ICU

(December 6, 2018 N Engl J Med 2018; 379:2199-2208)

This article appears to reach an erroneous conclusion based on its own data. The study implies that pantoprazole is ineffective in preventing GI bleeding in ICU patients when, in fact, the results show that it is effective.

The purpose of the study was to evaluate the effectiveness of pantoprazole in preventing GI bleeding. Instead, the abstract shifts gears and uses death within 90 days as the primary endpoint and the Results section focuses on “at least one clinically important event (a composite of clinically important gastrointestinal bleeding, pneumonia, Clostridium difficile infection, or myocardial ischemia).” For mortality and for the composite “clinically important event,” relative risks, confidence intervals and p-values are given, indicating no significant difference between pantoprazole and control, but a p-value was not provided for GI bleeding, which is the real primary endpoint, even though “In the pantoprazole group, 2.5% of patients had clinically important gastrointestinal bleeding, as compared with 4.2% in the placebo group.” According to my calculations, the chi-square value is 7.23, with a p-value of 0.0072, indicating that pantoprazole is effective at the p<0.05 level in decreasing gastrointestinal bleeding in ICU patients. [emphasis added]

My concern is that clinicians may be misled into believing that pantoprazole is not effective in preventing GI bleeding in ICU patients when the study indicates that it is, in fact, effective.

This sort of mislabeling of end-points is now commonplace in many medical journals. I am hoping you can shed some light on this. Perhaps you might be able to get the NY Times or the NEJM to publish an essay by you on this subject, as I believe the quality of medical publications is suffering from this practice.

I have no idea. I’m a bit intimidated by medical research with all its specialized measurements and models. So I don’t think I’m the right person to write this essay; indeed I haven’t even put in the work to evaluate Weinstein’s claims above.

But I do think they’re worth sharing, just because there is this “publication asymmetry” in which, once something appears in print, especially in a prestigious journal, it becomes very difficult to criticize (except in certain cases when there’s a lot of money, politics, or publicity involved).