# Rejoinder: Theorems, Proofs, Examples, and Rules in the Practice of Epidemiology

##### Author Information

From the Departments of ^{a}Epidemiology and Biostatistics and

^{b}Epidemiology, Harvard School of Public Health, Boston, MA.

Supported by National Institutes of Health grant ES017876. The authors reported no other financial interests related to this research.

*Editors' note:**Related articles appear on pages 433 and 440*.

Correspondence: Tyler J. VanderWeele, Departments of Epidemiology and Biostatistics, Harvard School of Public Health, 677 Huntington Ave, Boston, MA 02115. E-mail: tvanderw@hsph.harvard.edu.

The practice of epidemiology relies on general rules of thumb to guide analysis. Such rules include: “control for all common causes of the exposure and the outcome”; “make sure there are at least 10 events (and nonevents) per covariate in a logistic regression model”; “a covariate can be discarded if omitting it does not change the regression coefficient of the exposure by more than 10%”; “if an unmeasured confounder affects both the exposure and the outcome in the same direction, then the bias will be positive; if in opposite directions, negative”; “bias from an uncontrolled common cause of an exposure and an outcome generally exceeds the bias resulting from conditioning on a pre-exposure ‘collider’ variable”; “nondifferential misclassification of an exposure biases effect estimates toward the null”; and “control for a nondifferentially misclassified confounder will give estimates between the crude and true effects.” Some of these rules are on firmer theoretical footing than others. Some are informed by theoretical results, some by simulations, some by years of tried-and-true practice, and many of them by a combination of the above. Without these rules, the teaching and practice of epidemiology would indeed be difficult.

As noted by Greenland in his commentary,^{1} theoretical results or theorems have the advantage of clearly laying out the conditions under which they apply, but they can often be of limited use in practice because the complexities generally encountered in any analysis of real data render their conditions inapplicable. Epidemiologists therefore instead rely on general rules of thumb to guide analysis. Although theorems themselves are usually applicable only in simple settings, they can give rise to rules, the scope of which is sometimes much broader than the confines of the original theorems. For example, Bross^{2} showed that nondifferential misclassification of a binary outcome (or, by symmetry, a binary exposure) will give valid tests for an exposure-outcome association but may reduce their power. Today many epidemiologists use the rule that nondifferential misclassification of an exposure biases effects estimates toward the null.

From the standpoint of epidemiology as an academic discipline, it is of course important to distinguish among proven results, conjectures, the results of simulations, and rules of thumb; among what we know, what we think might be the case, and what seems to be “best practice.” All are important in informing practice and in advancing methodology, but each plays a different role. Simulations can explore complex settings more easily than theorems and are, in general, very important in informing practice and shaping our rules of thumb. In contrast, counterexamples are useful precisely because they can demonstrate that a rule is not universal. In some cases, a counterexample may not ultimately overturn the use of the rule to which it is the exception. For example, it was demonstrated some time ago^{3} that the rule inspired by Bross, “nondifferential misclassification of an exposure biases effects estimates toward the null,” has exceptions if the exposure is not binary. The warning has been reiterated on numerous occasions. And yet, the general rule—without the “binary” qualification—is often cited in applied work. Perhaps this general rule has not been overturned because in many cases, the exposure is binary. Perhaps, it has not been overturned because of its simplicity. Perhaps, it has not been overturned because there have not been sufficiently dramatic examples of exceptions in actual epidemiologic applications. Perhaps, it has not been overturned because ignoring nondifferential exposure “works” fairly well insofar as it preserves, in many common settings though not always, the direction of a trend.^{3}^{–}^{5} Even when counterexamples and qualifications do not alter a rule of thumb, they can serve to alert epidemiologists to cases in which further consideration may be warranted.

As we note in our paper,^{6} numerous textbooks^{7}^{–}^{9} cite a “partial control result” for binary confounders that for a nondifferentially misclassified binary confounder, the effect estimate adjusted for the misclassified confounder will lie between the true and the crude effect measures. These sources, in general, state this not as a guideline but as an established result. As we have shown,^{6} this “result,” stated in its unqualified form, does not in fact hold, even for a binary confounder, although it will hold if either (i) the binary confounder affects the outcome in the same direction for both the exposed and unexposed or (ii) the effects are computed only for the exposed or only for the unexposed, rather than for the entire sample.^{6} Thus the partial control result, even for a binary confounder, is subject to caveats.

As Greenland^{1} notes (rightly, in our view), the caveats may be of limited relevance in practice. Greenland points out that the risk ratios used in our counterexample are of an order of magnitude that is rarely, if ever, encountered in epidemiology. In the Appendix here, we give another counterexample in which the risk ratios are more realistic. Still, despite this counterexample, it is probably a good idea, in most settings, to adjust for a binary confounder subject to nondifferential misclassification. In most settings, the confounder will likely affect the outcome in the same direction for both exposure groups. When it does not, although the theorem does not apply, the “partial control” pattern will often still hold. When even this fails, the additional resulting bias will likely, in most cases, be small. At most, then, our results flag a case in which analysts may want to give further consideration to the possible implications of misclassification. Our counterexamples probably will not, and perhaps even should not, overturn the partial control result taken as a general rule. Indeed, the operative rule of thumb used in practice probably encompasses confounders that are not binary and even multiple confounders, despite well established counterexamples^{10} in these cases. In actual practice, do we not often—almost always—control for confounders of all sorts subject to measurement error? As rules of thumb go, there can be exceptions, but, overall, the partial control rule is probably a pretty good one. As suggested by Greenland,^{1} the conditions needed for its failure warrant further exploration, but the general rule in many cases works well.

Nonetheless, it seems that what was originally only a common pattern or rule of thumb was taken, for a number of years, as a formal result. It is not entirely clear why or at exactly what point this came to be. The original work of Greenland^{11} in 1980, which is often cited for the partial control result, arguably does not make this general claim. However, certainly by the time of Brenner's 1993 paper,^{10} it was widely assumed that the result had in fact been demonstrated, and textbooks by and large followed suit. The implications of this confusion are certainly not catastrophic, but the sequence of events serves as an interesting case study in the history of epidemiologic methods and the nature of intuition and formal argument. Sharper distinction between examples, conjectures, and rules of thumb on the one hand and established results on the other could have circumvented the mix-up in this case. Simulations, numerical examples, intuitions, and rules of thumb play an important role in epidemiology but, in the absence of a formal analytic argument, should not be interpreted as having established a formal result. The primary intellectual contribution of our paper was to articulate conditions under which the partial control result does hold and to develop proofs. The practical consequences of our results may indeed be limited given that, in this case, the theorems and proofs came after, not before, the general rule of thumb.

## APPENDIX

An important and yet-unresolved question raised by our findings is how common violations of the partial control result are in real-world settings. We do not at this time have an answer to that question, but we do know that counterexamples exist for many different data configurations. In Table A1, we present a counterexample that does not have the highly discrepant stratum-specific risk ratios, which were a feature of the counterexample in our paper. In this example, the risk ratios for the effect of exposure on outcome within levels of the confounder are 1.5 (*C* = 1) and 0.83 (*C* = 0), representing slightly less than a 2-fold difference. The risk ratios for the effect of the confounder on the outcome within levels of exposure are also 1.5 (*A* = 1) and 0.83 (*A* = 0). The risk ratio for the effect of the confounder on the exposure is 0.35. The partial control ordering is violated by a true risk ratio of 0.850, a crude risk ratio of 0.849, and an observed adjusted risk ratio of 0.846. We have found counterexamples with more dramatic violations to the partial control ordering, but each has a large risk ratio for at least one of the relationships between the confounder and the outcome conditional on the exposure, between the exposure and the outcome conditional on the confounder, or between the confounder and the exposure.