Our paper "Effect heterogeneity and variable selection for standardizing causal effects to a target population" has just been publised in the European Journal of Epidemiology at https://link.springer.com/article/10.1007/s10654-019-00571-w . While the journal's version of record is behind a paywall, a preprint is available on arXiv at https://arxiv.org/pdf/1610.00068.pdf.
This paper argues for my very deeply held belief that we can make significant advances in quantitative reasoning for medical decision making by thinking more closely about effect heterogeneity and how this relates to the choice of effect scale.
Over the course of the last 7 years, external validity and generalizability have become increasingly hot topics in statistical methodology and computer science. In particular, a lot of progress has been made by Judea Pearl and Elias Bareinboim, who introduced a framework based on causal diagrams that can be used to reason about how to take causal information from one setting (for example: a randomized trial) and apply it in a different setting (for example: a clinically relevant target population).
The key questions of interest are: How do we know whether such extrapolation is even possible? How do we determine what information we need from the study, and what information we need from the target population, in order to extrapolate the findings? How do we put this information together in order to obtain a valid prediction for what happens if the intervention is implemented in the target population?
Pearl and Bareinboim's framework for answering these questions is, of course, mathematically valid. However, in my opinion, their approach also throws the baby out with the bathwater. In particular, we argue that instead of attempting to extrapolate the magnitude of the effect (i.e. a measure of the "size" of the difference between what happens if the drug is taken, and what happens if the drug is not taken), they attempt to look at the people who were assigned to receive the intervention in the study, and extrapolate their distribution of outcomes to the target population without any reference to how that distribution differs from what happened to the people who were randomized to the control condition.
Theoretically, this approach will work if the extrapolation procedure can account for every cause of the outcome whose distribution differs between the people who were in the study, and the people you are trying to make predictions about. However, since the set of causes of the outcome is very large, it is very unlikely that it is possible to measure all of them. Moreover, it is very likely that we do not even know what the causes of the outcome are. Our inferences then become subject to potential uncertainty which arises from the auxiliary assumption that we know what to control for.
Consider a situation where scientists have conducted a randomized controlled trial in men, on the effects of homeopathy on heart disease. The scientists find that homeopathy has no effects in men, and wonder whether this finding can be extrapolated to women. If the scientists attempt to answer this question using Bareinboim and Pearl's framework, they will be forced to conclude that no extrapolation can be made, unless they are willing to claim that they know all the causes of heart disease that differ between men and women, and have been able to measure every one of these causes in all the patients in the study.
In contrast, we suggest that scientists who want to extrapolate their findings and make predictions outside of the study should attempt to quantify the size of the effect - that is, by how much the outcomes in the people who were randomized to receive the intervention differ from the outcomes in the people who were randomized to the control condition. This effect size could then potentially be used as the basis for extrapolation. Such an approach would correspond much closer to how external validity and extrapolation has traditionally been understood in the medical literature.
In the real world of clinical medicine, doctors are usually given information about the effects of a drug on the risk ratio scale (the probability of the outcome if treated, divided by the probability of the outcome if untreated). With information on the risk ratio, a doctor may make a prediction for what will happen to the patient if treated, by multiplying the risk ratio and patient's risk if untreated (which is predicted informally based on observable markers for the patient's condition).
The problem with this approach is that there are multiple scales on which to quantify the magnitude of the effect. Other possible scales for measuring effects include:
- The odds ratio, which applies a transformation to the risk
- The survival ratio, which uses the probability of survival (1-p) instead of the probability of death (p)
- The risk difference (which uses an additive scale instead of a multiplicative one)
Unless the intervention has no effect, the empirical predictions will not be invariant to the choice of scale. This is, of course, a serious problem for principled clinical decision-making, but as we will show, it is not necessarily an impossible one.
Despite the scale dependence of the reasoning procedure, the risk ratio is in many cases the only summary of the effect size that is made available to clinicians, whether they get their information from journals, clinical guidelines or online resources for clinical information. Given that the reasoning procedure is not scale-invariant, the universal reliance on the risk ratio may plausibly lead to suboptimal medical decision making in a wide range of clinical scenarios. But, in contrast to the implications of the Bareinboim/Pearl framework, we argue that this does not necessarily mean that we should throw out reliance on parametric effect measures altogether.
Our suggestion for how to choose the scale has been discussed earlier on Less Wrong (see https://www.lesswrong.com/posts/K3d93AfFE5owfpkx4/counterfactual-outcome-state-transition-parameters ). I am not going to repeat the argument in full here, but I will ask you to consider the following highly stylized thought experiment, which illustrates the underlying intuition:
Consider a randomized controlled trial where the intervention is that everyone is randomized to play Russian roulette once a year. This trial is conducted in Russia. It is found that among those who did not play Russian roulette, 1% of people died over the course of the year. Among the people who played Russian roulette, 18% of people died. We want to extrapolate these findings to Norway, where nobody ordinarily plays Russian roulette and it is known that 0.5% of people die during any year. Our goal is to find out what happens in Norway if everyone took up playing Russian roulette once a year.
Bareinboim and Pearl would suggest taking the risk of death among those who played Russian roulette (18%), controlling for all causes of death that differ between Russia and Norway, and producing an estimate for what happens in Norway if everyone plays Russian roulette. However, due to considerable differences between Russia and Norway in terms of predictors of mortality, this is clearly not feasible in this situation.
If we instead attempt to quantify the effect size in Russia, this can be done on any of the previously discussed scales:
- The risk ratio is
- The risk difference is
- The survival ratio is
- The odds ratio is
Each of these scales will result in a different prediction for what will happen if people in Norway play Russian roulette:
- If we use the risk ratio, we will predict that will die.
- If we use the risk difference, we will predict that will die.
- If we use the survival ratio, we will predict that will survive, meaning that 17.1% will die
- If we use the odds ratio, we will predict that will die.
These predictions differ massively not only in their implications for decision-making but also in their plausibility: Given what we know about Russian roulette, we would expect to see results much closer to 17% than to 9%. So clearly, some of these scales are doing something "right" and other scales are doing something "wrong".
We argue that the key to understanding the implications of this scale-dependence is that only the survival ratio ( ) has a structural meaning: it represents the proportion of empty chambers in the revolver, and therefore produces appropriate, valid predictions. In contrast, the risk ratio () has no possible structural meaning and therefore produces nonsense results.
Any attempt at extrapolation would, of course, have to account for all factors that determine the magnitude of the effect. For example, if Russians are more likely to be drunk when they play Russian roulette, they may be more likely to miss than Norwegians. This may lead to local deviations from effect sizes of , which will have implications for extrapolation. But once you have controlled for all of the factors that determine the magnitude of the effect on a scale that has structural meaning, extrapolation may be valid.
Crucially, we argue that controlling for all determinants of effect size (alcohol? how many chambers are there in typical revolvers in each country?) is much more tractable than controlling for all causes of mortality differences between the countries.
The main idea behind my research agenda is to explore how far we can push this argument in more clinically relevant settings. Next, consider a doctor who is trying to determine the pros and cons of treating a patient with a new drug. Suppose a reliable study on the drug shows that among those who received a placebo, 1% got an allergic reaction over the following 12 months; whereas, among those who received the drug, 2% got an allergic reaction.
The scientists behind the study can either tell the doctor that the risk ratio is , or that the survival ratio is . Both statements are correct, but only the latter has a potential structural interpretation, since it plausibly corresponds to a state of nature where 99% of the population do not have the factors (genes?) that predispose a person to have an allergic reaction if exposed to the drug.
Now consider that this patient also has a severe peanut allergy (which is unrelated to the medical issues that the doctor is treating them for) and lives in an environment where everyone eats peanuts all the time. This patient, therefore, has a 10% baseline risk of getting an allergic reaction over the course of 12 months, even in the absence of treatment with the new drug.
It would be insanity for the doctor to expect that the risk ratio from the study generalizes, and that the patient will have a 20% risk of anaphylaxis if given the new drug. In contrast, it may be meaningful to predict that their risk under treatment is given by . This will correspond closely to what one might expect would happen if the patient belongs to a population that has the same distributions of factors that predispose to the specific drug-related allergic reaction, as the population that was studied in the trial.
For these reasons, I consider it crucial for medical scientists to become aware of the need to put significant effort into reasoning about whether an effect measure has plausible structural meaning in the context of their current research question, before deciding to use it as a summary of their findings which is suitable for use in clinical decision making.
If anyone can spot any flaws in our argument, such feedback would be invaluable information. I invoke Crocker's Rules for all responses to the paper and the post. I would very much appreciate it if this blog post and the paper could be forwarded to anyone who is in a position to evaluate its importance.
Finally, let me note that this paper is the first peer-reviewed academic publication to acknowledge support from the EA Hotel Blackpool in its funding section. The EA Hotel is a project worth supporting; see https://forum.effectivealtruism.org/posts/uyvc6p99vsWFMPZiz/ea-hotel-fundraiser-5-out-of-runway