Dissent To the Preceding Article

1. When I assumed directorship of the Clinical Center of the National Institutes of Health (NIH) in 1970 I was anxious to establish my firm belief that all physicians engaged in practice and administration should conduct research relatedjo their clinical responsibilities. The Employee Health Department of the whole NIH was under my jurisdiction, and the appearance of the late Linus Pauling's book on vitamin C and the common cold (Ref. 9 in Hemilä's article) suggested a strong need for a well-designed and conducted clinical trial, a nice challenge to an employee health department. Dr. Thomas R. Karlowski was a Clinical Associate in the Department who enthusiastically accepted the challenge. 2. At the time where there was too little biostatistical input into clinical trials in the design stage and we were fortunate to enlist the collaboration of an experienced statistician in one of the Institutes. When the breaking of the blind described below was discovered, he withdrew and requested an anonymity that I have respected because he considered that it was too flawed a study to be published. I disagreed and felt strongly that we had a unique opportunity to publicize a defect that probably occurs quite commonly, but had never been documented in the past. His important contribution is illustrated by the unique stopping rules, a most important part of clinical trials that is seldom acknowledged. The protocol called for the study to be stopped before the estimated necessary sample size was achieved if "(1) the dropout rates from the group treated with ascorbic acid and the placebo groups . . . were . . . significantly different (the level of significance was to be taken at 0.15); (2) the number of persons under study fell below 200; and (3) at six months from the beginning of study the number of colds in the ascorbic acid treated group was significantly greater than the number in the placebo group (level of significance, 0.05)." The study was stopped 9 months after the last subjects had entered, when both the number remaining dropped below the estimated minimal number of 200, and it was apparent that more of the dropouts were in the placebo group (p = 0.10). The wisdom of this move is obvious, and the lesson for other studies is that there is a real advantage, one that overwhelms any mythical disadvantage of multiple looks, of monitoring trial results closely, with emphasis on the direction of the trends as well as how they fit with other related studies. 3. The third aspect of the trial of which I am proud is the very one that Hemilä attempts to criticize: that we did a routine check on the blinding by obtaining answers to a questionnaire, and that we recorded after interviews how many volunteers confessed to cheating by opening the capsules and tasting the contents. In any event Hemilä accuses us of assuming that if the volunteers guessed correctly which group they were in that means that they knew, which is obviously not the case. Hemilä repeatedly ignores our stated caveat that the numbers were too small for reliable retrospective analyses and we are castigated for attempting them in an effort to shed some light on the fact that our study did not confirm what seemed to be the popular conception. He is infuriated by our conclusion that it might well be a popular misconception. 4. As far as I know this was the first use of a 2-by-2 factorial design to investigate prophylaxis and treatment in the same patients. Since there was no suggestion of interaction we combined the two prophylaxis and the two treatment groups to successfully answer both questions with the same patients. Hemilä criticizes us for combining groups without saying why. He apparently does not understand what a 2-by-2 factorial design is.