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lukeprog comments on Causal Diagrams and Causal Models - Less Wrong
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Thanks!
This seems like a big problem for inferring "no causation" from "no correlation." Is there a standard methodological solution? And, do researchers often just choose to infer "no causation" from "no correlation" and hope for the best, or do they avoid inferring "no causation" from "no correlation" due to the fact that they can't tell whether the faithfulness assumption holds?
Well, in some sense this is why causal inference is hard. Most of the time if you see independence that really does mean there is nothing there. The reasonable default is the null hypothesis: there is no causal effect. However, if you are poking around because you suspect there is something there, then not seeing any correlations does not mean you should give up. What it does mean is you should think about causal structure and specifically about confounders.
What people do about confounders is:
(a) Try to measure them somehow (epidemiology, medicine). If you can measure confounders you can adjust for them, and then the effect cancellation will go away.
(b) Try to find an instrumental variable (econometrics). If you can find a good instrument, you can get a causal effect with some parametric assumptions, even if there are unmeasured confounders.
(c) Try to randomize (statistics). This explicitly cuts out all confounding.
(d) You can sometimes get around unmeasured confounders by using strong mediating variables by means of "front-door" type methods. These methods aren't really well known, and aren't commonly used.
There is no royal road: getting rid of confounders is the entire point of causal inference. People have been thinking of clever ways to do it for close to a hundred years now. If you have infinite samples, and know where unobserved confounding is, there is an algorithm for getting the causal effect from observational data by being sneaky. This algorithm only succeeds sometimes, and if it doesn't, there is no other way in general to do it (e.g. it's "complete"). More in my thesis, if you are curious.
Thanks again.
One more question, since this is your field. Do you happen to know of an instance where some new causal effect was discovered from observational data via causal modeling, and this cause was later confirmed by an RCT?
Well, I think smoking/cancer was first established in case control studies. In general people move up the "hierarchy of evidence" Kawoomba mentioned. At the end of the day, people only trust RCTs (and they are right, other methods rely on more assumptions). There is another good example, but let me double check before posting.
With case control studies you have the additional problem of selection bias, on top of confounding.
I thought there were still no actual RCTs of smoking in humans.
Right, you can't always RCT in humans. But a causal mechanism + RCTs in animals biologically close to humans is convincing for something like lung cancer where minor differences among mammals shouldn't matter much (although e.g. bears have evolved some crazy stuff to deal with all that fat they eat before hibernating).
I think you are entirely optimistic. I recently pointed out that the research indicates that animal studies routinely (probably usually) do not transfer, and as it happens, animal smoking studies are an example of this, according to Hanson. So the differences are often far from minor, and even if there were cancer in the animal studies, we could infer very little from it.
Out of curiosity, do you smoke?
No.
I find much to agree with in Hanson's writings, but in this case I just don't find him convincing. One issue is that cancer is a scourge of a long-living animal. One hypothesis is that smoking causes long term cumulative damage, and you might not see effects in mice or dogs because they die too soon regardless. There is also the issue that we have a fair idea of the carcinogenic mechanism now, so if you think smoking does not cause harm, there also needs to be a story how that mechanism is foiled in humans.
His interpretation, or his evidence? I point this out because it looks to me like your position has shifted from "the smoking / lung cancer link is established by RCTs in animals" to "even though RCTs don't establish the smoking / lung cancer link for animals, we have other reasons to believe in the smoking / lung cancer link for humans."
So: heads I win, tails you lose? If the studies had found smoking caused cancer in animals, well, that proves it! And if they don't, well, that just means they didn't run long enough so we can ignore them and say we "just don't find them convincing"...
You don't think there were plenty of 'fair ideas' of mechanisms floating around in the thousands of animal studies and interventions covered in my animal studies link? Any researcher worth his degree can come up with a plausible ex post explanation.
Your thesis deals only with acyclic causal graphs. What is the current state of the art for cyclic causal graphs? You'll know already that I've been looking at that, and I have various papers of other people that attempt to take steps in that direction, but my impression is that none of them actually get very far and there is nothing like a set of substantial results that one can point to. Even my own, were they in print yet, are primarily negative.
The recent stuff I have seen is negative results:
(a) Can't assign Pearlian semantics to cyclic graphs.
(b) If you assign equilibrium semantics, you might as well use a dynamic causal Bayesian network, a cyclic graph does not buy you anything.
(c) A graph representing the Markov property of the equilibrium distribution of a Markov chain represented by a causal DBN is an interesting open question. (This graph wouldn't have a causal interpretation of course).
As far as I can tell, epidemiology and medicine are mostly doing (c), in the form of RCTs (which are the gold standard of medical evidence, other than meta-reviews). There are other study designs such as most variants of case-control studies and cohort studies which do take the (a) approach, but they aren't considered to be the same level of evidence as randomized controlled trials.
Quite rightly -- if we randomize, we don't care what the underlying causal structure is, we just cut all confounding out anyways. Methods (a), (b), (d) all rely on various structural assumptions that may or may not hold. However, even given those assumptions figuring out how to do causal inference from observational data is quite difficult. The problem with RCTs is expense, ethics, and statistical power (hard to enroll a ton of people in an RCT).
Epidemiology and medicine does a lot of (a), look for the keywords "g-formula", "g-estimation", "inverse probability weighting," "propensity score", "marginal structural models," "structural nested models", "covariate adjustment," "back-door criterion", etc. etc.
People talk about "controlling for other factors" when discussing associations all the time, even in non-technical press coverage. They are talking about (a).
True, true. "Gold standard" or "preferred level of evidence" versus "what's mostly conducted given the funding limitations". However, to make it into a guideline, there are often RCT follow-ups for hopeful associations uncovered by the lesser study designs.
I, of course, know all of those. The letters, I mean.
"No subtle confounders" and "increasing sample size (decreases relevance and likelihood of such special cases)" would have m-answered your previous z-comments. (SCNR)