Multi-center data pooling is highly demanding in time and expertise, and Cardis et al (2005) describing a 15-nation study of low-dose radiation effect on cancer mortality deserve much credit for succinctly reporting in this first paper the results of their important contribution to the field of radiation risk assessment. However, careful acknowledgment of the limitations should be made if conclusions are to be drawn from this one study alone, rather than from the accumulating evidence from many epidemiological studies in various settings (Brenner 2003). Recognizing that the authors may have had to forego detailed discussion for the sake of brevity, we would like to point out some general limitations in the methodology not explicitly discussed in the paper that prevent reaching too definite conclusions. The wording used for the conclusion highlighted in the text box with the caption "What this study adds": "A small excess risk of cancer exists, even at the low doses typically received by industrial workers in this study" seems stronger than the authors' wording: "these results suggest that an excess risk of cancer exists". Few epidemiologists would assert such a conclusion based on excess relative risks on the order of a few percent over the range of exposures actually observed, when it is difficult to defend the validity of excess relative risks an order of magnitude larger in observational studies (Taubes 1995; Lagarde 2003). Specification of the slope coefficient as risk per Sv may imply larger risks and strength of association than actually observed. As most of the study population was exposed below 20 mSv due to a skewed exposure distribution, it would be appropriate to express the linear slope per unit of 10 mSv in order to avoid an illusion of large effects. For all cancers excluding leukemia, this would produce an excess relative risk of 0.010 with corresponding 95% confidence interval 0.001-0.020. Furthermore, such a confidence interval does not account for potential confounding or other sources of bias, so that it should not be inferred that one may be 95% confident in a larger sense that the true effect size is captured within such bounds. Epidemiological methods are neither sensitive nor accurate (and arguably not even appropriate) when relatively small risk increments are expected among the exposed compared to non-exposed. It has been quantified that relative risks of about 1.2 may be plausibly induced by uncontrolled confounding when in fact exposure has no effect on disease (Lagarde 2003), which is larger than those reported in the pooled study (Cardis 2005).

Another source of concern is that control for age using stratification in 5-year intervals can leave substantial confounding as age is strongly related to cancer risk. Improved age adjustment (e.g. modeling the age effect, or using individual records) may be especially critical when cumulative exposure is use to predict cancer risk, since cumulative exposure and attained age are likely correlated. Such correlation would cause the average age, within given 5-years age categories, to be larger for larger cumulative exposure categories and cause confounding due to the effect of differing mean age within exposure categories. Cancer rates increase sharply beyond middle age, so only a few months imbalance in age across exposure categories is sufficient to spuriously induce excess relative risks of the order of a few percent like those reported. It would also be of interest to have information about the size of the excess relative risk when all studies are included, and about the impact of adjustment for socio-economic status in the studies selected for analysis.

Another usual piece of information would be dose-category-specific relative risks. Such category-specific relative risks are essential for evaluating the evidence for a trend, evidence for a dose-response relationship being another important criteria for causality, in addition to strength of association. This would also allow inspection of how the regression line fits the data the over the observed range of exposures. If the association was driven by the few subjects with cumulative doses larger than 50 mSv, the conclusions of the study would not be due to low dose effects as defined by the authors. Furthermore, although the results do not refute the linear no-threshold hypothesis, the paper provides scant insight as to the suitability of alternative (e.g., quadratic or threshold) models or their goodness of fit to the data.

The present comments mainly bear on the important question of whether it is possible, given the methodology, that a spuriously significant effect at low dose was found in absence of a true effect. The issue of whether, assuming there is an effect, bias exists in the size of the estimate, would require separate comment. For example, since more than 90 % of the population was still alive at the end of the follow-up period, proper assessment of the burden of excess cancer in that population may require further follow-up, which would also better allow for necessary induction time. It thus cannot be ruled out that the excess relative risk estimates reported may actually be underestimating the real risks.

Although the number of cancer cases within the low-dose range in the Life Span Study of Atomic-bomb Survivors is also large, we would be reluctant to assess risk estimates on the basis of exposure data truncated to an average of about 20 mSv. The presence of exposures on the order of 1 Sv in the Atomic-bomb Survivor study makes it possible to estimate an excess relative risk per Sv that is unlikely to be caused by the problems of observational studies at low doses, and to compare this with the slopes for various low dose ranges (Preston 2003).

As initially mentioned we believe that Cardis et al . have many analysis results in store they had no space to report and are confident that forthcoming communications will address our call for additional information.

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Competing interests: None declared