One of the most pervasive problems in the medical literature (and in other subject areas) is misuse and misinterpretation of p-values as detailed here, and chief among these issues is perhaps the absence of evidence is not evidence of absence error written about so clearly by Altman and Bland. The following thought will likely rattle many biomedical researchers but I've concluded that most of the gross misinterpretation of large p-values by falsely inferring that a treatment is not effective is caused by (1) the investigators not being brave enough to conclude "We haven't learned anything from this study", i.e., they feel compelled to believe that their investments of time and money must be worth something, (2) journals accepting such papers without demanding a proper statistical interpretation in the conclusion. One example of proper wording would be "This study rules out, with 0.95 confidence, a reduction in the odds of death that is more than by a factor of 2." Ronald Fisher, when asked how to interpret a large p-value, said "Get more data."
Adoption of Bayesian methods would solve many problems including this one. Whether a p-value is small or large a Bayesian can compute the posterior probability of similarity of outcomes of two treatments (e.g., Prob(0.85 < odds ratio < 1/0.85)), and the researcher will often find that this probability is not large enough to draw a conclusion of similarity. On the other hand, what if even under a skeptical prior distribution the Bayesian posterior probability of efficacy were 0.8 in a "negative" trial? Would you choose for yourself the standard therapy when it had a 0.2 chance of being better than the new drug? [Note: I am not talking here about regulatory decisions.] Imagine a Bayesian world where it is standard to report the results for the primary endpoint using language such as:
- The probability of any efficacy is 0.94 (so the probability of non-efficacy is 0.06).
- The probability of efficacy greater than a factor of 1.2 is 0.78 (odds ratio < 1/1.2).
- The probability of similarity to within a factor of 1.2 is 0.3.
- The probability that the true odds ratio is between [0.6, 0.99] is 0.95 (credible interval; doesn't use the long-run tendency of confidence intervals to include the true value for 0.95 of confidence intervals computed).
In a so-called "negative" trial we frequently see the phrase "treatment B was not significantly different from treatment A" without thinking out how little information that carries. Was the power really adequate? Is the author talking about an observed statistic (probably yes) or the true unknown treatment effect? Why should we care more about statistical significance than clinical significance? The phrase "was not significantly different" seems to be a way to avoid the real issues of interpretation of large p-values.
Since my #1 area of study is statistical modeling, especially predictive modeling, I pay a lot of attention to model development and model validation as done in the medical literature, and I routinely encounter published papers where the authors do not have basic understanding of the statistical principles involved. This seems to be especially true when a statistician is not among the paper's authors. I'll be commenting on papers in which I encounter statistical modeling, validation, or interpretation problems.
Misinterpration of P-values and of Main Study ResultsOne of the most problematic examples I've seen is in the March 2017 paper Levosimendan in Patients with Left Ventricular Dysfunction Undergoing Cardiac Surgery by Rajenda Mehta in the New England Journal of Medicine. The study was designed to detect a miracle - a 35% relative odds reduction with drug compared to placebo, and used a power requirement of only 0.8 (type II error a whopping 0.2). [The study also used some questionable alpha-spending that Bayesians would find quite odd.] For the primary endpoint, the adjusted odds ratio was 1.00 with 0.99 confidence interval [0.66, 1.54] and p=0.98. Yet the authors concluded "Levosimendan was not associated with a rate of the composite of death, renal-replacement therapy, perioperative myocardial infarction, or use of a mechanical cardiac assist device that was lower than the rate with placebo among high-risk patients undergoing cardiac surgery with the use of cardiopulmonary bypass." Their own data are consistent with a 34% reduction (as well as a 54% increase)! Almost nothing was learned from this underpowered study. It may have been too disconcerting for the authors and the journal editor to have written "We were only able to rule out a massive benefit of drug." [Note: two treatments can have agreement in outcome probabilities by chance just as they can have differences by chance.] It would be interesting to see the Bayesian posterior probability that the true unknown odds ratio is in [0.85, 1/0.85].
The primary endpoint is the union of death, dialysis, MI, or use of a cardiac assist device. This counts these four endpoints as equally bad. An ordinal response variable would have yielded more statistical information/precision and perhaps increased power. And instead of dealing with multiplicity issues and alpha-spending, the multiple endpoints could have been dealt with more elegantly with a Bayesian analysis. For example, one could easily compute the joint probability that the odds ratio for the primary endpoint is less than 0.8 and the odds ratio for the secondary endpoint is less than 1 [the secondary endpoint was death or assist device and and is harder to demonstrate because of its lower incidence, and is perhaps more of a "hard endpoint"]. In the Bayesian world of forward directly relevant probabilities there is no need to consider multiplicity. There is only a need to state the assertions for which one wants to compute current probabilities.
The paper also contains inappropriate assessments of interactions with treatment using subgroup analysis with arbitrary cutpoints on continuous baseline variables and failure to adjust for other main effects when doing the subgroup analysis.
This paper had a fine statistician as a co-author. I can only conclude that the pressure to avoid disappointment with a conclusion of spending a lot of money with little to show for it was in play.
Why was such an underpowered study launched? Why do researchers attempt "hail Mary passes"? Is a study that is likely to be futile fully ethical? Do medical journals allow this to happen because of some vested interest?
Similar ExamplesPerhaps the above example is no worse than many. Examples of "absence of evidence" misinterpretations abound. Consider the JAMA paper by Kawazoe et al published 2017-04-04. They concluded that "Mortality at 28 days was not significantly different in the dexmedetomidine group vs the control group (19 patients [22.8%] vs 28 patients [30.8%]; hazard ratio, 0.69; 95% CI, 0.38-1.22; P = .20)." The point estimate was a reduction in hazard of death by 31% and the data are consistent with the reduction being as large as 62%!
Or look at this 2017-03-21 JAMA article in which the authors concluded "Among healthy postmenopausal older women with a mean baseline serum 25-hydroxyvitamin D level of 32.8 ng/mL, supplementation with vitamin D3 and calcium compared with placebo did not result in a significantly lower risk of all-type cancer at 4 years." even though the observed hazard ratio was 0.7, with lower confidence limit of a whopping 53% reduction in the incidence of cancer. And the 0.7 was an unadjusted hazard ratio; the hazard ratio could well have been more impressive had covariate adjustment been used to account for outcome heterogeneity within each treatment arm.