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Authors’ Response

Levy, Paul S. ScD; Deubner, David C. MD; Roth, H Daniel PhD

Journal of Occupational and Environmental Medicine: July 2007 - Volume 49 - Issue 7 - p 709-711
doi: 10.1097/JOM.0b013e3180d09eb0
Letters to the Editor
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RTI International; Research Triangle Park, NC(Levy)

Brush Wellman, Inc.; Elmore, OH(Deubner)

Roth Associates Inc.; Rockville, MD(Roth)

Readers are invited to submit letters for publication in this department. Submit them to: The Editor, Journal of Occupational and Environmental Medicine, 605 Worcester Road, Towson, MD 21286-7834. Letters should be sent as hard copy with an accompanying diskette and should be designated “For Publication.”

To the Editor: The major points made by Schubauer-Berigan et al on our reanalysis1 of the Sanderson et al nested case-control data2 reflect their non-acceptance of an artifact that we found can occur under certain patterns of employment when incidence density sampling is used to match controls to cases and then exposure is lagged for purposes of investigating the effect of disease latency. Because their arguments ignore our findings of this artifact, we reiterate it below before addressing their specific comments.

The above-mentioned artifact does not occur when exposure lagging is not used, and the theoretical foundations on which incidence density sampling is based3,4 do not address what happens when it is combined with exposure lagging. This artifact can be explained without going into detail by noting that when exposure lagging is not used, there is a truncation of exposure measurement for both control and matching case at one point, namely the age at censor (ie, age at death or at last ascertainment if alive) of the case, which by algorithm is always less than or equal to that of the control.

When incidence density sampling is combined with exposure lagging, a second truncation occurs and all exposure for both case and control occurring after the lag cutoff (defined as the age at censor of the case minus the assumed disease latency) is truncated. It is this second truncation that can produce the artifact that, under certain employment patterns, a control having the same exposure as the matching case has a greater chance than the case of having some or all of his or her exposure truncated. The statistical basis for this artifact is shown in the appendix of this response. Its existence was demonstrated in our recent article1 and further supported by findings from a simulation study (Deubner DC, Roth HD, Levy PS. Empirical evaluation of complex epidemiologic study designs. Submitted to J Occup Environ Med) (under review). This being said, we now address the three issues that Schubauer-Berigan et al raise.

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1. Issues Relating to Our Critique of the Logarithmic Transformation.

Our argument (stated on pages 99 and 100 of our article1) is based on the fact that the log transformation of values close to or equal to 0.1 (the surrogate for zero used in the Sanderson et al paper2) transforms them much further away from the central value of the log transformed distribution than the untransformed values are from the central value of the original distribution, thus giving them more impact in the subsequent conditional logistic regression distribution than the original values would have in the analysis using the untransformed exposure variable. We also stated that this would not be a problem if the artifact discussed in the first paragraph of this response did not result in controls having a greater likelihood than cases of having some or all of their exposure truncated owing to this artifact. Their response does not address this artifact and so their critique is based on their ignoring the issues that we raised in our article and reiterated in this paragraph. The material that we present in the Appendix further reinforces what we stated in our article.

With respect to their discussion of whether the exposure-response distribution is best specified by the untransformed or log transformed distribution, it is difficult for us to see how the patterns shown in their discussion of Table 3, in Sanderson et al,2 relating to conditional logistic regression with quantiles of exposure as the covariate implies a power relationship between exposure and response (nor was this or any other explanation given for the use of the log transform in the original article2 other than that the original distribution is skewed and not normally distributed, which is not a requirement for using logistic regression). Also, the findings in the lagged analyses presented in Table 3 of Sanderson et al2 are moot since they are subject to this same artifact mentioned heretofore.

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2. Our “Assertion” that the Older Average Age of Death of Controls Compared with Cases is Problematic in Incidence-density Sampled Cohorts.

We nowhere state in our reanalysis that there is a global problem with the use of incidence-density sampling (aka risk-set sampling) or with the use of age as the time variable. We would not be so presumptuous as to negate a methodology that has been used for many years in numerous epidemiological studies and is based on a sound theoretical framework. As we stated above, however, we could find nothing in the methodological literature specifically addressing its use with exposure lagging. The fact is that simply confining exposure measurement to that which occurred before the latency cutoff point does not negate the methodological issues that we discussed first in our paper and now in this response to the Schubauer-Berigan et al criticisms of our recent paper. Given this artifact, the nearly 9-year mean difference between cases and controls with respect to age at censor is far from trivial.

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3. Criticism that Our Analysis is Restricted to Controls Whose Age at Censor is Within 3 Years of That of the Matching Case.

Schubauer-Berigan et al assert that our restriction of controls to those whose age at censor is within 3 years of that of the matching case violates assumptions for using conditional logistic regression when incidence density sampling is employed and of its cohort study analog, Cox proportional hazard regression. There is, to our knowledge, nothing stated in the literature that one can’t perform analysis on subgroups of the risk set on which the controls are selected so long as the findings are extrapolated to the appropriate target population. In this instance, our subgroup is those controls that are more closely matched (ie, within 3 years of the age at censor) with the matching case. Our rationale for doing this is, again, that it helps reduces the effects of the artifact in lagged analysis caused by the broad matching on age at censor used in the original nested case-control study.2 The criticisms point out that our analysis in Table 4 did not control for certain covariates that are confounders. This is true but it is also true of the conditional logistic regression performed in Sanderson et al2 and we wanted our own analysis to be univariate similar to that in the Sanderson et al paper2 so that they can be directly compared.

The criticisms point out year of birth as a confounder and we have found age at hire as a confounder. Both of these are confounders in the epidemiological sense because they are associated with both exposure and with case/control status. Schubauer-Berigan et al state that they have submitted a manuscript showing that when year of birth is controlled for, average and maximum exposure remain associated with lung cancer (we assume that this analysis is based on all cases and controls since they criticize our subgroup analysis).

In response to the above criticisms, we performed analysis restricting, as before, controls to those whose age at censor is within 3 years of that of the matching case and including year of birth as a covariate. We obtained for maximum exposure an exposure-lung cancer odds ratio equal to 1.11 (95% CI = 0.95–1.29) and for average exposure an odds ratio equal to 1.14 (95% CI = 0.97–1.34). These are only slightly higher than the respective odds ratios equal to 1.06 (95% CI = 0.92–1.22) and 1.11 (95% CI = 0.95–1.31) shown in Table 4 of our article. In all instances, these odds ratios overlap unity and they remain much lower than the odds ratios of 1.20 shown in Sanderson et al.2

We disagree with the statement made by Schubauer-Berigan et al that “It is not appropriate to simultaneously adjust for age at hire because of its high correlation with birth year, and the lack of an a priori rationale for hire age as a source of confounding.” Since age at hire is the age at which workers first are exposed to beryllium, there is indeed an a priori rationale for testing whether it is a possible confounder. However, the point is moot since we made no attempt to control for both simultaneously in any of our analyses.

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4. “Minor” Errors.

Schubauer-Berigan et al state we have incorrectly flagged the index study P values in our Table 1. This is correct and is unfortunate, because part of our purpose was to initiate a conversation on the methods in the nested case-control study2 and how the artifact creates case-control differences when exposure is lagged. Incorrectly flagging these P values suggests the artifact is less strong than it is. Schubauer-Berigan et al point out that the 1993 IARC decision did not rely on the index study. We agree with this. It relied on another NIOSH study, by Ward et al5 published in 1992.

Paul S. Levy, ScD

RTI International

Research Triangle Park, NC

David C. Deubner, MD

Brush Wellman, Inc.

Elmore, OH

H. Daniel Roth, PhD

Roth Associates Inc.

Rockville, MD

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References

1. Levy PS, Roth HD, Deubner DC. Exposure to beryllium and occurrence of lung cancer: a reexamination of findings from a nested case-control study. J Occup Environ Med. 2007;49:96–101.
2. Sanderson WT, Ward EM, Steenland K, Peterson MR. Lung cancer case-control study of beryllium workers. Am J Indust Med. 2001;39:133–144.
3. Langholz B, Goldstein L. Risk set sampling in epidemiological studies. Stat Sci. 1996;11:35–53.
4. Lubin JH, Gail MH. Biased selection of controls for case-control analyses of cohort studies. Biometrics. 1984;40:63–75.
5. Ward E, Okun A, Ruder A, Fingerhut M, Steenland K. A mortality study of workers at 7 beryllium processing plants. Am J Indust Med. 1992;22:885–904.
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Appendix

Notation: A = age at censor of case; A′ = age at censor of control; L = assumed disease latency time; AL = latency cutoff point; ae = age when first employed for case; ae = age when first employed for control; at = age at termination of employment for case; at = age at termination of employment for control; D = atae = duration of employment for case; D′ = atae = duration of employment for control.

For the cases, some exposure will be truncated if at > AL, and analogously for the controls, some exposure will lag if at > AL. From these two relations, the following probability statements follow:

For the controls,

From relations (1) and, (2) if ae > ae, a control employed for the same duration as the matching case has a higher probability of having at least some exposure truncated than the matching case.

©2007The American College of Occupational and Environmental Medicine