The Gothenburg breast screening trial (1998)

The publication of the long-awaited results of the Gothenburg breast screening trial1 is important given that it is the first trial to claim a statistically significant benefit among women ages 40-49; the Malmö results2 apply only to women age ≥ 45 years, thus obscuring how much of the benefit is derived from screening women age > 50 years. Given the negative or equivocal results obtained in this age group until now, it is startling that this benefit was observed in a trial with only 25,667 invited participants, just > 50% the number of subjects ages 40-49 years in the Canadian National Breast Screening Study (CNBSS), a trial in which annual mammography and physical examination showed no benefit.3, 4 A fundamental concern with the Gothenberg study is that the randomization procedure is neither clearly described nor apparently successful. The authors state that cluster randomization was used for 18% of the subjects based on year of birth cohorts, and individual randomization was applied to the remaining 82% based on individual birthdates. However, it is unclear what the difference is between these two methods, even though they apparently required different computer software for their execution. If the date (day) of birth defined the allocation, women with identical birth dates would be in the same allocation arm by both systems. Therefore both appear to be a form of cluster randomization, and the trial should have been analyzed by cluster, with computation of the design effect and an appropriate correction of the confidence intervals applied. Because this was not done, the statistical significance claimed for the findings is in doubt. Also of concern is who performed the randomization? Was the individual performing the randomization associated with the process of inviting women to be screened? When randomization is performed on the basis of date of birth the allocated regimen is known in advance, so the system is not blind. What effect did this advance knowledge have on the invitation process? Of greatest concern is that randomization was not successful in producing truly comparable groups. For the authors to claim that 'randomization was effective' on the basis of similar distribution by year of age Table 2 in their article) verges on the ludicrous given that similar distribution of not one but many variables in the CNBSS did not hinder criticism of its randomization process.5-8 There are several indications that the control group in the Gothenburg study had a higher underlying incidence of breast carcinoma than the study group. First, the cumulative incidence of breast carcinoma in the control group exceeded that of the study group at the end of the period of observation by a considerable margin Fig. 2 in the article by Bjurstam et al.). Bjurstam et al.1 explain this by the fact that the first screen in the control group occurred 'a few months' after the last screen of the study group. However, the closeness of the curves throughout the period of observation suggests that this substantial "catch up" is too large to be explained on such grounds. Screening in the early years of the trial should have resulted in a differential in cumulative incidence between the study and control groups far greater than was observed. Second, applying the numbers of carcinomas diagnosed by age at diagnosis to the person-years of observation from Table 6 indicated that the cumulative incidence of breast carcinoma (including in situ tumors, always in excess in a screened group compared with an unscreened group) was identical in the study and control groups at ages 39-49 years (1.53 per 1000 in each group). At age 50 + years the cumulative incidence in the control group (0.82 per 1000) was substantially in excess of the study group (0.59 per 1000). Third, a further indication that the underlying incidence in the control group was higher than in the study group is the authors' statement1 that "the mortality benefit would have been considerably higher if women with a previous breast carcinoma had not been excluded from analysis" because of "increased surveillance in those at higher risk," implying that screening mammography in women with previously diagnosed breast carcinoma has a mortality benefit. Unless we are to believe that the standard of care (use of chemotherapy and hormone therapy) offered in Gothenburg to women in a screening program is substantially higher than that offered to those outside such a program (thus introducing the confounding effect of differential therapy into the analysis of the trial results), a far more rational explanation is that somehow the authors selected more women at risk for death from breast carcinoma into their control group than into their study group. Fourth, there are additional internal data suggesting a much higher underlying incidence in the control group compared with the study group. Detection rates on screening can be computed from the numerators in Table 4 and the denominators in Table 2. The detection rate at the first screen in the study group was only 1.71 per 1000 (compared with the CNBSS detection rate by mammography of 2.54 per 10004). The average detection rate on subsequent screens was slightly higher (1.84 per 1000), although one would expect detection rates at rescreening to be lower than at the prevalence screen. Bjurstam et al.1 explain this as an effect of aging, but it may in part reflect the 18-month interval between screens. The average detection rate by mammography on rescreening in the CNBSS was 1.42 per 1000;4 multiplying by 3/2 to adjust for the 18-month interval in Gothenburg results in an expected rate of 2.13 per 1000. In contrast, the control group detection rate in Gothenburg at their first screen was 4.36 per 1000. This is higher than the expected prevalence at ages 50-59 years of 3.69 per 1000, computed based on the expectation that there would be the same relation between prevalence at ages 40-49 years and 50-59 years as in the CNBSS, in which prevalence by mammography detection at ages 50-59 years was 5.48 per 1000.9 Therefore, age cannot explain such a large difference. Bjurstam et al.1 justify the screening of the control group as somehow correcting for the effect of lead time, overlooking the fact that comparable numbers of cases in both groups only could be expected if the compliance with screening was the same in both groups, whereas it was lower in the control than the study group in Gothenburg. In any case, a randomized trial with breast carcinoma mortality as the endpoint completely discounts the effects of lead time. Breast carcinoma deaths should be ascertained in the total population randomized from the date of randomization to the same termination date in both study and control groups, irrespective of how the breast carcinomas were diagnosed. Although screening the control group was irrelevant for evaluating the effect of screening in the study group, it was useful in that it confirmed that the control group was not comparable to the study group. We conclude that the beneficial effects claimed for 18-month mammography screening in the Gothenburg trial are due to bias, with the control group having an unexplained excess incidence of breast carcinoma, and therefore, not surprisingly, an excess breast carcinoma mortality. Given the problems apparent in the Gothenburg trial, the lack of correction for cluster randomization not only in its analysis but also in many of the other published trials of screening for women ages 40-49 years and the failure to satisfactorily account for the effects of screening women once they reached age 50 years, the recent meta-analysis claiming a statistically significant effect of screening women ages 40-49 years with mammography10 cannot be taken at its face value. We agree with the consensus development panel11 that there is as yet no proven benefit for mammography screening in women age < 50 years and women at these ages should not be misled into believing that there is. Anthony B. Miller M.B.*, Cornelia J. Baines M.D. M.S.C.*, Teresa To Ph.D.*