We are grateful to Nguyen et al1 and Glymour and Vittinghoff2 for their interest in our research letter3 and for the opportunity to respond to their remarks. Specifically, we focus on the argument raised by Nguyen and colleagues1 that much of the debate in the obesity paradox literature can be attributed to confusion between total and direct effects, as well as the related point made by Glymour and Vittinghoff2 that the selection bias correction described in our letter does not answer the key question surrounding the obesity paradox.
The goal of our letter was to address the multitude of published studies that use a cohort of patients with diagnosed chronic disease (such as heart failure) and attempt to answer the question of whether obesity is protective or harmful in this selected subgroup. By conditioning on disease status through restriction of the study cohort, we reasoned that these articles must necessarily induce collider stratification bias because of the presence of unmeasured common causes of chronic disease and mortality (Figure).
As other authors have previously noted,4 the causal effect estimate sought in these studies is akin to a controlled direct effect:
However, because these are observational studies rather than controlled experiments, the “setting” is not in fact possible, and so an approximation is attempted through measuring current weight, stratifying on observed heart failure status, and controlling for observed confounders. The objective of our analysis was to demonstrate that, by accounting for the differential selection into the heart failure group (HF = 1), it is possible to reverse the apparently protective association between obesity and mortality in the (unobserved) source population. The corrected estimate is therefore no longer like a controlled direct effect but is instead an estimate of the total causal effect of obesity in the hypothetical source population from which the diseased population emerged:
We therefore disagree with Nguyen et al1 that this correction via reweighting can be used to obtain an “unbiased estimate of the direct effect of obesity.” Their reasoning is that the study conditioned on observed HF = 1 status in the design, and so the association between obesity and mortality reflects pathways other than those that operate through the induction of heart failure. However, reweighting by the inverse probability of having heart failure undoes this conditioning and provides a marginal association—not one conditional on having achieved a specific disease status.
We aimed to demonstrate the capacity of an unmeasured common cause of heart failure and mortality to reverse the overall harmful effect of obesity in the diseased subgroup, essentially showing that the controlled direct effect in the HF = 1 stratum can appear protective even if obesity is harmful for every person in the population. The inability to obtain an unbiased estimate of the controlled direct effect in observational data follows from the presence of important unmeasured common causes of heart failure and death, including (but certainly not limited to) genetic factors, cardiorespiratory fitness, inflammatory biomarkers, and lifestyle or psychosocial factors. Valid estimation of the causal controlled direct effect for the HF = 1 stratum would therefore require being able to identify, measure, and adjust for these factors.
Nguyen and colleagues1 further assert that if both the direct and the indirect effects of obesity on the risk of death are in the same direction, one would expect the total effect of obesity to be larger than its direct effect. This statement is true only under a model of monotonic and strictly additive effects.5 Because the whole premise of the supposed paradox is that obesity effects may not be monotonic, these assumptions seem unjustified.
Given the fact that a controlled direct effect is not identified in the original figure,3 Glymour and Vittinghoff2 suggest sensitivity analysis to evaluate whether unmeasured confounders of the heart failure-mortality relationship can potentially explain the change of direction in the stratum-specific association. We agree completely with this approach and have pursued similar calculations.6 Glymour and Vittinghoff2 note that the reweighting correction presented in our letter cannot show that selection bias is the only possible explanation for the obesity paradox because it merely uses external information to recreate the average effect in the total population. The observation that the direction of the association reverses upon reweighting, back to the unselected population, is consistent with collider stratification bias as an explanation for the paradox. It does not preclude the possibility, however, that the effect of obesity on mortality may be truly modified in some subgroups through causal interaction between exposure and their particular set of characteristics. We therefore must agree with these commentators that, while collider stratification can contribute to the obesity paradox, this fact provides no direct evidence against the supposition of qualitative effect measure modification. This represents an important limitation of our letter.3
Realistically, it seems almost certain that some degree of collider stratification bias and effect measure modification must be co-occurring in this situation. The substantive literature on chronic diseases suggests strongly that there are important unmeasured common causes that would confound the controlled direct effect estimate. Therefore, it seems impossible to conceive that conditioning on an intermediate factor, such as diagnosed heart failure, would fail to induce some degree of bias.
Likewise, how could one believe in perfect homogeneity of the causal effect of obesity on mortality? This effect presumably must also be causally modified in some way by characteristics that differ across the disease category strata. Could this effect measure modification be severe enough to flip the direction of the causal effect? The existence of strong collider stratification bias would not in any way detract from this possibility. As in so much of observational epidemiology, we view the world through multiple layers of distortion and obfuscation, for which simplistic models give us only the faintest sense of the underlying structure.7 Therefore, we must also agree with Nguyen et al1 when they posit that “...even after correction for [collider stratification] bias, this paradoxical phenomenon may persist in observational studies of the effect of obesity on mortality among patients with heart failure.”
Although we enthusiastically support the sensitivity analysis approach pursued by Glymour and Vittinghoff,2 we agree that interpretation must remain cautious because the simulation conditions are highly simplified. They posit that selection bias is unlikely to be a complete explanation for the protective obesity association among patients with heart failure because the unmeasured risk factors would have to quintuple the risk of mortality to produce a relative risk of 0.70. This is a sobering observation, but it is based on the impact of a single binary confounder, as they are careful to note. The published result also necessarily included sampling variability and misclassification, not to mention the potential for multiple confounders. The hazard ratios reported by Curtis et al8 would actually overestimate the relative risks, given that one-third of the cohort experienced the outcome. After additional adjustments, Curtis and colleagues8 arrived at a hazard ratio of 0.81 (95% confidence interval = 0.72–0.92). One would not have to add much selection bias to a sampling distribution with this mean and spread before a sizable proportion of the probability mass fell above the null.
Nguyen and colleagues1 suggest that demonstrating a difference between the direct effect of obesity in one intermediate stratum and the total effect in the unselected population does not constitute evidence of an “obesity paradox.” However, we believe that, regardless of the true underlying explanation, it is quite reasonable to refer to a protective association between obesity and mortality in heart failure patients as “paradoxical” because this word has been used many times in the literature to describe exposures that appear harmful (or null) in the total population but protective for a specific stratum.4,9
The intent of our letter was to illuminate a methodological concern that is commonly overlooked in the clinical literature, despite the fact that the perils of conditioning on a variable affected by exposure have been known to epidemiologists for quite some time. The analysis we presented was intended to illustrate that an apparently protective effect observed in a postexposure stratum could result from selection bias, even if the exposure were truly harmful for every person in the population. This fact does not rule out other possible phenomena, including true causal effect heterogeneity. We also agree with both commentaries1,2 when they note that the selection bias correction that weights back to the total unselected population is not a method for obtaining the true stratum-specific causal effect.
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