Reply to Labrie et al.

It is good to see the results of the mortality analysis of the Quebec Randomized/Controlled Trial (RCT) of screening [1] in a peer review journal so that all those who have been awaiting the details can make informed judgments of the strength of the evidence. Any investigators who find that compliance with the intervention in one arm of an RCT is just 23% are in an extremely difficult situation. Whilst sympathizing with this problem, I am very concerned that this report may 1) seriously mislead clinicians by providing exaggerated estimates of the mortality benefit which can be achieved by screening for prostate cancer, and 2) lead statisticians, epidemiologists, and clinicians to lose some of their respect for randomized clinical trials as the evidential gold standard. The clear focus of this paper is on complex comparisons of subgroups of men whose comparability is not justified by randomization. It is simply not correct to assert that this “first randomized and prospective study on prostate cancer screening shows a 69% decrease in incidence of deaths due to prostate cancer. ” This 69% reduction is from a nonrandomized comparison and, moreover, one which is, as I shall show below, subject to serious and substantial selection bias. It is also false to say that the “analysis is thus made on an intent-to-treat basis from the time of enrollment”— false because the analysis is not “intent-to-treat,” and false too since major problems lie with the identification of the time when the follow-up clock starts ticking. In fact, it is November 15, 1988 for unscreened men in each arm of the trail, but date of first screen for the screened men; it is clear that this makes a major difference, since the respective mean follow-up times are 7.4 and 7.5 years for unscreened men in the invited and control arms but 3.8 and 4.3 years for the two groups of screened men (Fig. 1A). This is the source of the most important selection bias in the present analysis: men in the screened cohorts (groups a and c of Fig. 1A) have the additional selection criteria that they were available for screening and hence were free of diagnosed prostate cancer at a mean time of around 3 years after the time of enrollment of the unscreened men (groups b and d). Since rates of death from (prostate) cancer in an initially disease-free population are strongly associated with year of follow-up for several years, the comparisons of prostate cancer mortality in groups a/b and groups c/d are both subject to large bias which cannot be quantified using the published data. However, crude examination of the Scottish survival data for prostate cancer cases diagnosed 1983– 1986 suggests that differences of follow-up could lead to a 43% reduction in mortality rates in the screened groups. The fact that the two comparisons (a with b and c with d) give similar estimates of the benefit of screening is of no help and no relevance. The quoted figure of 69% benefit is based on these comparisons, is subject to unmeasured bias, and should in our opinion be disregarded. An “intent-to-screen” analysis is required because individuals who choose to accept screening differ from those who do not in many characteristics, including socioeconomic status, perceived health status, and comorbidity. Analyses which compare “acceptors” with “nonacceptors” have yielded inflated estimates of benefit for other cancer screenings [2]. Here [1] the “intent-to-screen” analysis was conducted with more scientific rigor, although the poor compliance rate argues against its results giving a meaningful estimate of the benefit which screening can make. It would have been sensible to retain the exclusion criteria, especially prior diagnoses of prostate cancer, as is standard for screening trials, and we follow this practice below, since full data from the excluded men are not available. The “start-time” problems emerge again, and examination of them will serve (Table I) to illuminate what we have described above. Analyses of the data in Figure 1B as rates of death/1,000 men give, as the authors say, an estimate of 6% benefit in the “invited” arm. However, repeating this analysis as rate/ 1,000 person-years (which is preferable) estimates a 4% higher death rate in the invited arm if the personyears of Figure 1A are used. “Correcting” the personyears in groups a and c to take account of the time from November 15, 1988 to the first screen reconciles this apparent discrepancy.