As shown in recent studies, with an average follow-up of 12.7 years, the meta-analysis using the most current data shows a relative risk of 0.82 (18% fewer breast cancer deaths) when all trials are combined, a relative risk of 0.74 (26% fewer deaths) when only population-based trials are combined (not shown), and a relative risk of 0.71 (29% fewer deaths) for all five Swedish randomized controlled trials. Each point estimate is statistically significant at the 95% confidence level, although the all-trial meta-analysis has the lowest relative risk of breast cancer mortality because of the excess rate of breast cancer deaths in the NBSS-1 in the group invited to screening. The meta-analysis of Swedish trials is included in this comparison because they represent a more homogeneous group and because they include the two second-generation trials (i.e., Gothenburg and Malmö), which applied more advanced screening protocols and observed 44% and 36% fewer breast cancer deaths in the invited groups compared with the control groups.

What is evident in these meta-analyses is that they show very similar mortality reductions among women younger and older than age 50 who were invited to the screening.

The one analysis that stands apart from the others is the all-trial meta-analysis of women in their 40s, in which the size of the NBSS-1 and the excess rate of deaths in the group invited to screening measurably reduce the estimated benefit. Because irregularities in the NBSS-1 have yet to be explained, the consistency of results in the other meta-analyses and the recent results from Gothenburg and Malmö suggest that it is reasonable to regard the potential benefit of screening in younger versus older women as more similar than different, especially if recommended screening intervals are tailored to the age-specific estimated sojourn time.

As mentioned at the beginning of this section, there are notable differences in the cumulative trial mortality trends for women younger and older than age 50, and reasons for this difference have been an ongoing source of debate - long on conjecture but short of a clear explanation. Some have argued that the observed delay in benefit was simply a function of small sample sizes and overall better survival in younger compared with older women.

By this argument, it doesn’t matter when a mortality reduction appears, because screening is beneficial if it averts deaths from breast cancer in the near or long term. However, others have argued that the delayed benefit was a methodologic artifact of trial design, in which mortality reductions attributed to women in their 40s actually were due to diagnoses after age 50 among women randomized in their 40s. Because the analysis of age-specific mortality differences in trials is based on age at randomization (not age at diagnosis), at the time of analysis the group randomized in their 40s includes patients diagnosed after they have had a fiftieth birthday. According to this hypothesis, if a benefit from screening truly begins at age 50, then the observation of benefit for women in their 40s is more apparent than real, because it must be due to the benefit of diagnosing breast cancer after age 50 among women randomized in their 40s.

Thus, a benefit later in the follow-up period would be due to the time required to accumulate the age migration cases. Likewise, for women randomized in their 50s, the benefit from screening was seen earlier in the follow-up period because they were already at an age when mammography is beneficial. In effect, this argument was a call for analysis of trial data by age at diagnosis.

Although it seems logical, analysis of trial data by age at diagnosis has a built-in bias, because the purpose of screening is to diagnosis breast cancer earlier in its natural history, which means, for any individual who develops breast cancer at a younger age than when symptoms would be expected to appear. Because age at diagnosis is influenced by the study intervention (i.e., mammography), it is regarded as a pseudovariable. By introducing lead-time bias, it complicates comparisons between the invited and not-invited group and is therefore methodologically inappropriate. The question of age-specific benefits is important, but to be properly addressed a trial would need to randomize a narrow age range of women (i.e., women aged 40 to 41) to an invited and not-invited group and follow them for the duration of interest (i.e., until age 50), thus avoiding “age-creep.” Still, this question has been pursued.

In 1995, de Koning and colleagues published data from the Swedish Two-County trial arguing that age migration in the group randomized in their 40s could account for 70% of the observed benefit and thus explain the late onset of benefit in this age group. In an accompanying editorial, it was argued that this kind of analysis actually violates the underlying logic of trial data analysis as noted in the previous paragraph, but if it were to be pursued, analysis of actual trial data rather than modeling would be the logical approach. Tabar and colleagues subsequently evaluated Swedish Two-County data by age at randomization and age at diagnosis and observed no support for this hypothesis. In fact, the relative mortality reduction among women randomized in their 40s was greater among women diagnosed before their fiftieth birthday than in women diagnosed after age 50. No support for this hypothesis was observed in a similar analysis of Gothenburg trial data.

Recent analysis of Swedish Two-County data provides a clearer and more clinically intuitive explanation for the delay in benefit observed in the individual trials and meta-analyses based on an assessment of the effect of the trial screening protocols on mortality trends by tumor histology. As described in the section Sojourn Time and the Influence of Early Intervention, the mean breast cancer sojourn time (i.e., potential lead time) is shorter in women younger than age 50 than in women older than age 50.