Kaufman, Jay S.a; Glymour, M. Mariab
From the aDepartment of Epidemiology, Biostatistics, and Occupational Health McGill University, Montreal, Quebec, Canada; and bDepartment of Society, Human Development, and Health, Harvard University, Boston, MA.
Supported by funding from the Canada Research Chairs program (to J.S.K.) and from the American Heart Association (to M.M.G.).
Editors' note: Related articles appear on pages 98 and 107.
Correspondence: Jay S. Kaufman, Department of Epidemiology, Biostatistics, and Occupational Health, McGill University, 1020 Pine Ave West, Montreal, Quebec H3A 1A2, Canada. E-mail: email@example.com.
Carlsson et al1 assert that the association between BMI and mortality from causes other than coronary heart disease (CHD) arises because of confounding by genes that make some people gain weight and also make these people die sooner. The authors reached this conclusion because they detected within-pair associations between body mass index (BMI) and mortality (all-cause and CVD-specific) in dizygotic (DZ) twins, but not in monozygotic (MZ) twins. The main analytic approach used in this paper was a fixed-effects regression. The authors considered whether, for same-sex twin pairs in which one sibling was heavier than the other at baseline (some 40 years in the past), the heavier twin was more likely to die first. Because DZ twins share 50% of genes and MZ twins share 100% of genes, the authors hypothesize that “if genetic factors were the main explanation for the association between BMI and mortality, we would expect to find an association within DZ twins, where genetic confounding is only partially controlled, whereas no association … between BMI and mortality would be expected in MZ pairs.”
This is a clever approach, but we don't believe that the authors' conclusion is well-supported by the data and analyses presented. We have several areas of concern: the design is very sensitive to unexamined assumptions; the extreme selection implicit in the co-twin sample used for the fixed-effects analysis may have induced survivor bias; the fixed-effects approach may impose an additional selection bias; and the generalizability of the results is uncertain. We briefly explain each of these concerns below.
To infer that the different OR estimates observed in the MZ and DZ twins imply genetic confounding, one must invoke the “equal environments assumption,” which is the degree to which twins are exposed to the same environment is exactly the same for MZ and DZ twins. Otherwise, if DZ twins share both fewer genes and also fewer aspects of environment than MZ twins, there would be no way to parse out the 2 classes of influences. Though a common premise in twin research, this assumption appears unlikely to be exactly true.2,3 For example, the genetic similarity of MZ twins may lead to more similar environments through their own behaviors, and the social awareness of their “identical” status may affect the behaviors of parents and others, giving MZ twins more similar experiences than DZ twins. Contemporary debates about this assumption in twin research therefore focus on the quantitative question of how far off this assumption may be, and thus how large the resulting bias.4 Even small violations of this assumption may easily account for differences of the magnitude observed by Carlsson et al1 (eg, ORMZ = 0.99 vs. ORDZ = 1.04).
THE POTENTIAL FOR SURVIVOR BIAS
Beyond the question of whether twins are representative of other births, the co-twin analyses are based on only 27% of the twins identified in the population cohort and 34% of the observations recruited into the study cohort. To be included in the co-twin control analysis, it was necessary that at least one twin in the pair had died. Since only about a third of twin pairs met this criterion, there was strong selection for those factors related to death. For example, selected twins were on average 12.4 years older than those in the full cohort. Many prior studies show that the relation between BMI and mortality attenuates with increasing age,5,6 and this is verified by contrasting effect estimates in the full cohort to those from the co-twin sample in the current study. Obesity researchers hypothesize that this attenuation may be due either to survivor bias or to the influence of confounding by undiagnosed diseases more common in old age, such as cancer or Alzheimer disease, that can induce both weight loss and increased mortality risk.7 Either of these possibilities would potentially bias the results of both the cohort analysis and the fixed-effects analysis using the co-twin subset. The authors have even provided some information pointing to the magnitude of this bias. The estimated effect of a unit change in BMI on all-cause mortality in the full cohort was a hazard ratio of 1.05 across all twins (Table 1). The same analysis in the subcohort selected for the co-twin contrast produces estimates of 1.01 for MZ and 1.02 for DZ twins (Results). There is no additional control for confounding in this analysis, so the change of roughly 70% toward the null is from restriction of the sample alone.
POTENTIAL FOR SELECTION BIAS IN FIXED EFFECTS MODELS
The association between exposure and disease observed in a study sample recruited as a function of the outcome (eg, any case-control design) will misrepresent the source population association if selection is also correlated with exposure through pathways other than the etiologic effect of interest.8 In the co-twin analysis presented in the paper by Carlsson and colleagues,1 this is exactly what has happened: the majority of twins were screened out of the analysis on the basis of either the outcome (one of the twins must have already died) or the exposure (they must have been discordant in BMI at baseline). Most reported BMI values were roughly concordant between twins, with only 21% of MZ twins and 36% of DZ twins differing by more than 2 BMI units. Because the associations will change in the subset due to selection bias, rather than to confounding-reduction alone, both MZ and DZ twins should be affected. Because MZ twins are less likely to be discordant for BMI than DZ twins, this bias could affect the twin groups differently, resulting in divergent ORs for the 2 groups.
Fixed-effects designs are an elegant method of controlling for certain unmeasured confounders, but they are not a panacea for all confounding. This model holds constant all factors in the shared environment, but it offers no such reassurance for factors in the individual environment. So if any random event, such as accidentally dropping little Sven on his head at age 2, eventually affects diet, health, or behavior, there is nothing in the present study that distinguishes BMI-mortality associations due to these environmental common causes from those correlations arising from direct causation. Thus, the effect estimates from the co-twin fixed-effects analyses may be confounded by individual-level common causes of BMI and mortality. Many of these sources of confounding, such as incident non-CHD disease, could both reduce BMI and increase mortality risk, introducing a negative bias into the estimated association between BMI and mortality.
Why would MZ and DZ twins differ in the occurrences of such mechanisms? A DZ twin could be heavier as a function of some unique genetic or environmental factor, while MZ twins must differ only due to individual nongenetic factors. Imagine a simple scenario in which individual BMI is entirely determined by 3 factors: a gene that influences BMI but has no direct effect on mortality; individual dietary decisions, which influence BMI but have no direct effect on mortality; and presence of cancer, which influences both BMI and directly increases mortality risk. Among DZ twins in the co-twin subset, all 3 causes would contribute to their BMI differences, and thus cancer would induce a downward bias on the estimated causal effect of BMI on mortality. Among MZ twins, however, only individual dietary decisions or cancer could cause BMI differences, exacerbating the downward bias by inflating the proportion of discordant pairs due to cancer. This is a highly simplified example, but the point holds generally: the twin fixed-effects design will reduce bias only if individual factors confound the association of interest less than genetic factors do. We are aware of no evidence that supports this assumption.
LACK OF GENERALIZABILITY
Setting aside concerns about the internal validity of these findings, the analyses are based on a sample of twins from cohorts in which obesity was rare (BMI >30 kg/m2 was reported by only 3.5% of women and 2.2% of men). Furthermore, generalizability is especially questionable for an exposure as diffusely defined as BMI, which does not correspond to any specific causal pathway.9 The effects of BMI differences attributable to genetic predisposition may very well differ from the effects of BMI differences resulting from food or activity-environment differences. Because there is no reason to assume that the impact of higher BMI achieved through one mechanism is the same as that achieved through another, the comparison between selected MZ and DZ twins may not generalize in any way to the effects of obesity in the general population.
The paper by Carlsson et al1 is a creative analysis of a unique data resource, but it cannot be viewed in isolation from an extensive literature on this topic. Other authors have found clever ways to deal with unmeasured confounding in representative samples through tools such as instrumental variables10 and Mendelian randomization,11 and many of these reports suggest an important causal effect of obesity on non-CHD outcomes. Nonetheless, these approaches, too, rest on assumptions that often cannot be verified from the data at hand. Moreover, it is entirely possible that there is no etiologic effect of small BMI differences reported 40 years ago on non-CHD mortality among selected Swedish twins, even while there truly exists an important effect in unrestricted population samples. Even if entirely valid, therefore, the results of the current study may not reveal much about BMI and mortality in general. They would certainly not suggest that “public health concerns regarding overweight may be overemphasized.” At best, they might only suggest that the potential value of co-twin controlled designs in epidemiologic research may be overemphasized.
1. Carlsson S, Andersson T, deFaire U, Lichtenstein P, Michaëlsson, Ahlbom A. Body mass index and mortality: is the association explained by genetic factors? Epidemiology. 2011;22:98–103.
2. Horwitz AV, Videon TM, Schmitz MF, Davis D. Rethinking twins and environments: possible social sources for assumed genetic influences in twin research. J Health Soc Behav. 2003;44:111–129.
3. Joseph J. The Missing Gene. New York: Algora; 2006;13–36.
4. Mitchell KS, Mazzeo SE, Bulik CM, Aggen SH, Kendler KS, Neale MC. An investigation of a measure of twins' equal environments. Twin Res Hum Genet. 2007;10:840–847.
5. Bender R, Jockel KH, Trautner C, Spraul M, Berger M. Effect of age on excess mortality in obesity. JAMA. 1999;281:1498.
6. Stevens J, Cai J, Pamuk ER, Williamson DF, Thun MJ, Wood JL. The effect of age on the association between body-mass index and mortality. N Engl J Med. 1998;338:1–7.
7. Buchman AS, Wilson RS, Bienias JL, Shah RC, Evans DA, Bennett DA. Change in body mass index and risk of incident Alzheimer disease. Neurology. 2005;65:892–897.
8. Hernán MA, Hernández-Díaz S, Robins JM. A structural approach to selection bias. Epidemiology. 2004;15:615–625.
9. Hernán MA. Taubman SL. Does obesity shorten life? The importance of well-defined interventions to answer causal questions. Int J Obes (Lond). 2008;32(suppl 3):S8–S14.
10. Davey Smith G, Sterne JA, Fraser A, Tynelius P, Lawlor DA, Rasmussen F. The association between BMI and mortality using offspring BMI as an indicator of own BMI: large intergenerational mortality study. BMJ. 2009;339:b5043.
11. Kivimäki M, Smith GD, Timpson NJ, et al. Lifetime body mass index and later atherosclerosis risk in young adults: examining causal links using Mendelian randomization in the Cardiovascular Risk in Young Finns study. Eur Heart J. 2008;29:2552–2560.
© 2011 Lippincott Williams & Wilkins, Inc.