Lawlor, Debbie A.
From the MRC Centre for Causal Analyses in Translational Epidemiology, School of Social and Community Medicine, University of Bristol, Oakfield House, Oakfield Grove, Bristol, United Kingdom.
Supported by the MRC Centre for Causal Analyses in Translational Epidemiology, the UK Medical Research Council (G0600705), and the University of Bristol.
Editors' note: Related articles appear on pages 138 and 151.
Correspondence: Debbie A. Lawlor, MRC Centre for Causal Analyses in Translational Epidemiology, School of Social and Community Medicine, University of Bristol, Oakfield House, Oakfield Grove, Bristol, BS8 2BN. United Kingdom. E-mail: firstname.lastname@example.org.
The paper in this issue by Rajaleid et al1 concludes that “synergism between small size at birth and high adult body mass index (BMI) supports the thrifty phenotype hypothesis.”1 This is a large and well-conducted case-control study that attempts to shed light on the causal mechanisms linking small birth size with later increased risk of coronary heart disease (CHD), by testing a “biologic interaction” between birth size and BMI in their relation to CHD.
In the 2 decades since David Barker2 first demonstrated an inverse association between birth weight and later CHD, there have been numerous attempts to understand what this association means in terms of underlying mechanisms and its public health relevance. The fetal origins hypothesis, originally proposed by Barker, pointed the finger at maternal undernutrition during pregnancy, with the public health implication that prevention of CHD (still one of the biggest killers and causes of morbidity globally) should focus on good nutrition of women in pregnancy or during their reproductive years.2 During the ensuing years, Hales and Barker3 developed this suggestion into the thrifty phenotype hypothesis. This hypothesis suggests that poor maternal nutrition in pregnancy, resulting in fetal undernutrition, “prepares” the developing fetus for a life of thrift. If, however, postnatally the in utero undernourished individual experiences a life of nutritional plenty, they are maladapted and at particular increased risk of CHD.3 Underlying biologic mechanisms for this hypothesis have been suggested and include developmental plasticity and epigenetic processes.4,5 This hypothesis has some support from the findings in many epidemiologic studies that the association of lower birth weight with increased risk of CHD and CHD risk factors is enhanced by, or only apparent after, adjustment for later BMI. However, this observation cannot prove the thrifty phenotype hypothesis.6 It also remains possible that the observed associations of birth size with CHD is explained by residual confounding.7
Rajaleid et al1 set out specifically to test the thrifty phenotype hypothesis. They did so by examining the “biologic interaction” between birth size and later adult size in their association with acute myocardial infarction. As their conclusion implies, they found an interaction and interpreted this as providing evidence for the hypothesis. Several points are worth considering in regard to this conclusion—the most important of which is just what “biologic interaction” means and whether this concept has any value in epidemiology.
One of the enjoyable parts of preparing this commentary has been going back over some of the many book chapters and papers on this topic. It is interesting to note that, in their introduction to the chapter on interactions in the second edition of Modern Epidemiology, published in 1998, Rothman and Greenland imply that the controversy and debates around what was meant by biologic and statistical interaction were largely resolved: “The ensuing literature identified a number of distinctions and concepts whose delineation has helped shed light on the earlier disagreements, and has pointed the way to further elaboration of concepts of interaction.”8 A brief look at the very recent volumes of just this one journal (Epidemiology) suggests that they were being overly optimistic.9–14 While reading these papers, an obvious opener for this commentary that sprang to mind was “a rose by any other name …,” but Jay Kaufman beat me to that.11 A suitable alternative might be “you say tomahto, I say tomato … you say biologic, I say it is no different to statistical … let's call the whole thing off.”
The term “biologic interaction” was first coined by Rothman,15 who defined it as deviation from additivity in risk differences for 2 causal risk factors. Statistical interaction is generally understood as deviation from what would be expected from the joint effect of 2 risk factors, under the assumption that they are independent, and is dependent upon the model scale—ie, whether the model is additive (assessing mean or risk differences) or multiplicative (assessing ratios). So what makes “biologic interaction” special or different from the more general term is that it is used only on the additive scale (risk or mean differences) and has strong assumptions of causality.
Is the term “biologic interaction” useful? I think there are several reasons why it is not. First, Douglas Thompson,16 2 decades ago, elegantly demonstrated that many biologic explanations could be invoked for an additive interaction between 2 risk factors; “Unfortunately, choice among theories of pathogenesis is enhanced hardly at all by the epidemiological assessment of interaction.” Second, any good analysis plan is based on prior knowledge and a statistical protocol that is determined prior to starting the analysis. This is another strong assumption, but if we assume all good statisticians/epidemiologists do this, then examining interactions should really be done only with some prior causal assumptions. In that case, if the interaction is explored on an additive scale, how can one decide whether this is “statistical” or “biologic”? At the end of the day, both are determined by use of a statistical model. Third, making causal assumptions about risk factors from observational studies is difficult. Interactions are subgroup analyses that rarely replicate and by and large should be treated with extreme caution.16 Calling a particular approach “biologic” might give false reassurance and make researchers feel that they can ignore the underlying assumptions that they are making about causality. With the possible exception of gene-environment interactions in the context of Mendelian randomization,17,18 such interactions will rarely illuminate causal understanding.16
In their paper, Rajaleid et al1 claim that a “biologic interaction” is being tested. If we refer to Rothman's original definition, this implies the assumption that birth size and BMI are causally related to CHD. Although birth size has been shown to be robustly associated with CHD in many studies from different populations and with adjustment for a wide variety of potential confounding factors,7 few investigators believe that size at birth per se is the underlying causal risk factor. Rather, it is a proxy for an environmental in utero exposure such as poor maternal nutrition,2 or for a genetic variant related to growth and later coronary heart disease,19,20 or indeed the association is explained by residual confounding.7 Likewise, that BMI is a causal risk factor has been questioned.21 In their failure to fully discuss these issues, Rajaleid et al seem to fall into the trap of using the name “biologic interaction” without fully appreciating the limitations of their data to determine biologic mechanisms or causality.16
Caution has to be applied regarding these results, as with any interaction. The authors explore interactions with 3 measurements of birth size (birth weight, birth weight standardized for gestational age, and ponderal index) and 2 measures of later size (BMI and waist circumference); they have measures of BMI at 3 time points, and they examine all of these exposures in different ways—as categories and continuous variables. Therefore, there are multiple tests of interaction. One might have had more confidence had these shown consistency. However, of the many interactions that they test, they identify an interaction only between birth weight standardized for gestational age (comparing the lowest 5% of this variable with the remaining 95%) and BMI (measured at any of the 3 time points, and dichotomized as overweight/obese [defined as ≥28 kg/m2] vs. normal weight). Given these multiple tests, one has to assume that these are chance findings unless replicated. The number of persons who are both small-for-gestational age and overweight or obese is tiny: just 4 (0.3%) of the controls and 20 (2.5%) of the cases. The authors acknowledge that the “biologic interaction” they identify is unlikely to be of public health importance. But they fail to see that, based on such small numbers, in the context of multiple testing and the lack of any consistent interactions in the many different ways that these variables can be cut and mixed (bar this one), this interaction is very unlikely to have any biologic meaning and cannot be used to support the thrifty genotype hypothesis.
Furthermore, the finding of an interaction only with use of low birth weight standardized for gestational age might be explained by selection bias.22 Hutcheon and Platt22 have demonstrated how birth weight standardized for gestational age introduces selection bias because the values are derived from all infants born at that specific gestational age, with no consideration for the weight of the fetuses remaining in utero. It is also a concern that the main effects in this study are not consistent with the now-extensive literature in this area, most of which reports an inverse association of birth weight (with or without adjustment for gestational age) across most of the distribution of birth weight,7 as opposed to the finding in this study of an association only with low (bottom 5%) birth weight for gestational age.
Therefore, while recognizing that the editors of this journal11 have not yet heeded Sander Greenland's10 suggestion that “statistical interaction” be abandoned as a term,10 perhaps they should consider giving no credence to the term “biologic interaction.” At the very least, authors using the term should be explicit about the causal assumptions they are making, and should be asked by editors and reviewers to fully justify these assumptions.
George Davey Smith (University of Bristol), John Lynch (University of South Australia and University of Bristol), and Jonathan Sterne (University of Bristol) made useful comments on an earlier version of this commentary.
ABOUT THE AUTHOR
DEBBIE A. LAWLOR is Professor of Epidemiology in the MRC Centre for Causal Analyses in Translational Epidemiology, University of Bristol. She has contributed work to understanding the life course and genetic epidemiology of obesity, diabetes, cardiovascular disease, and women's reproductive health and in developing methods for improving causal inference in observational epidemiology.
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© 2011 Lippincott Williams & Wilkins, Inc.