Regarding “Parental Genotypes in the Risk of a Complex Disease”

To the Editor: Labuda et al. (2002) have proposed that parental genotypes might play a role in the causation of complex diseases. They seem unaware that this idea has been considered by others (e.g., Lande et al. 1989) and that methods have been developed to test for parentally mediated genetic effects, both for a dichotomous phenotype (Mitchell 1997; Weinberg et al. 1998; Wilcox et al. 1998) and for a quantitative phenotype (van den Oord 2000). Furthermore, some of the assessments made by Labuda et al. miss the mark. They assume (see their fig. 1) that under scenario A, where the offspring genotype is the one that “counts,” the parents of affected children will resemble control parents with respect to the gene under study. This ignores the fact that the genotypes of parents and their children are correlated. Just as the parents of offspring with Huntington disease will differ from population controls in their prevalence of the allele for Huntington disease, parents of offspring who have a complex disease will tend to differ from population controls. Thus, the case-control analyses reported in table 1 of Labuda et al. (2002) are not specific to parentally mediated genetic effects. There are other reasons, biologic and technical, to doubt the interpretation offered by Labuda et al. who suggest that their data support a parent-mediated effect of CYP2E1*5 on risk of childhood acute lymphoblastic leukemia. First, the mechanisms by which the maternal and paternal genotypes would influence offspring phenotype are very different (i.e., in utero environment vs. DNA replication errors that produce genetically abnormal sperm). It thus seems unlikely that the etiology of a given condition would be related to both maternal and paternal effects of a single gene. Rather, similar “effects” of the maternal and paternal genotypes, on the basis of case-control parental data, seem more likely due to the selection of a biased control group or to offspring-mediated effects that have confounded the comparison of the (correlated) parental genotypes. Thus, the data offered by Labuda et al., which show very similar odds ratios for the mother and for the father, may be seen more plausibly as reflecting either a systematic bias in the control group or a chance finding. The final issue is analytic. The odds ratio parameter estimated by the case-control analysis is not the same as that estimated by transmissions. Labuda et al. evidently used a standard method for paired data, calculating the ratio of counts for discordant transmission pairs based on heterozygous parents. This approach estimates the relative penetrance for carriers of a single copy of the variant allele under a gene dose model in which the relative penetrance for two copies is the square of that for one copy. By contrast, in their case-control analysis, Labuda et al. use carrier status, which presumes a dominant model. The paired estimator based on transmissions can be shown to be biased toward 1.0 under such a model. Even if the two analyses were estimating the same parameter, there is considerable overlap in the CIs for the two estimates. For these reasons, the results presented by Labuda et al. (2002) should be seen as providing only very weak evidence for a parent-mediated effect of CYP2E1*5.