Be Skeptical of Correlational Studies

There is, but there's still value to showing real world examples where 'correlation is not causation' and showing the real explanations (which in the absence of hard randomized trials, can come off as mindless nitpicking and motivated cognition by people who just don't want to accept the correlation*).

* I'm worried about this because looking back over the years of discussion on the dual n-back mailing list, I get the feeling that a lot of people wrote off the methodological criticisms of the n-back studies as basically theoretical 'perfect is the enemy of better' motivated-cognition nitpicking, even about the soundest criticisms like active control groups, until I finally sat down and did the meta-analysis showing the active control group criticism was right on the money.

This is a good thing to read: http://intersci.ss.uci.edu/wiki/pdf/Pearl/22_Greenland.pdf (chapter 22 in Judea's Festschrift). In particular the contrast between Fig. 1 and Fig. 2 is relevant.

What is going on here is that what we care about is some causal parameter, for instance "average causal effect (ACE) : E[Y | do(A=1)] - E[Y | do(A=0)]."

This parameter is sometimes identified, and sometimes not identified.

If it is NOT identified, it is simply not a function of the observed data. So any sort of number you get by massaging the observed data will not equal to the ACE. Naturally, if we try to randomize (which will get us the ACE directly) we will not reproduce what our observational data massage got us.

If it IS identified, then it is the matter of what functional of the observed data equals to the ACE. Maybe if we have treatment A, outcome Y, and a set of baseline confounders, the correct functional is:

\sum_{c} ( E[Y | A=1,c] - E[Y | A=0,c] ) p(c)

This is what "adjusting for confounders" means.

However, maybe that's not the right functional at all! Maybe you have a mediating variable M between A and Y, and the right functional is:

\sum{m} \sum{a'} E(Y | m,a') p(a') P(m | A=1) - \sum{m} \sum{a'} E(Y | m,a') p(a') P(m | A=0)

How do we tell what functional is right? We have to agree on what the right causal graph is for our problem, and then consult an algorithm that will either give us the right functional for the ACE given the graph, or tell us the ACE is not identifiable given the graph we got. This algorithm was what a part of my thesis was about.

There is one important historical example of people ignoring graph structure to their peril. In epidemiology people worry about something called the "healthy worker survivor effect." Say we have workers who work with asbestos, which is a bad chemical. We want to get an idea of how bad it is by running a study. The longer you work with asbestos, the worse your outcome. However, if you are sick, you will probably terminate employment early, which means you will not get more exposure to asbestos. So people who get more asbestos are also healthier. So it might seem based on observational data that even though we suspect asbestos is very bad for you, it seems to have a protective effect on workers. This is the "healthy worker survivor effect."

If we were to draw a simple graph with two time slices for this, we would get:

A1 -> H -> A2 -> D

where A1 and A2 are asbestos exposure, H is health status after A1, and D is death (or not). H and D are confounded by a common cause we do not see H <- U -> D. A1 determines H. If H is bad enough, it will cause the worker to leave, and thus set A2 to 0. A1 and A2 determine D.

What we want here is E[D | do(a1,a2)]. The point is that blindly adjusting for H is incorrect, because of the particular graph structure where H arises. H is a standard confounder for A2, but is NOT a standard confounder for A1 (H is what is called a "time-varying confounder.") So you need to use a particular form of adjustment called "g-computation":

\sum_{h} E[D | a1,a2,h] p[h | a1]

If you use the standard adjustment

\sum_{h} E[D | a1,a2,h] p[h]

you will get a biased answer. Jamie Robins wrote a giant 120 page paper in 1986 (that no one ever reads) on (among many many other things) this precise issue:

http://www.hsph.harvard.edu/james-robins/files/2013/03/new-approach.pdf

(edit: the reason you get bias with standard adjustment is because A1 -> H <- U is in your graph. If you condition on H, A1 and U become dependent: this is the so called "Berkson's bias, selection bias, collider stratification bias, or explaining away phenomenon." So standard adjustment creates a non-causal path A1 -> H <- U -> Y between a treatment and the outcome which accounts for part of the magnitude of the effect, and thus creates bias.)

What happens in practice is if you try to get the ACE from observed data, you will have too much confounding to get identification by any method (adjustment or anything else, really). So you need some sort of extra "trick." Maybe you can find a good instrumental variable. Or maybe you have a natural experiment. Or maybe you had really good data collection that really observed most important confounders. Or maybe the treatment variable only has observed parents (this happens in observational longitudinal studies sometimes). If you just blindly use covariate adjustment without thinking about your causal structure you will generally get garbage.

I'd very much like to know more about this too. I distinctly recall at least three separate papers by separate authors in different domains that mentioned "adjusting for confounders" on things that I thought would be, so I thought "Oh, it's fine then, they did their thinking properly and there is an effect!". (At times like these I wish I remembered things or kept notes on research papers a fraction as diligently as Yvain or gwern...)

Then I read further because now I'm very interested in why, and upon finding the details of their adjustments, in small print under one of the many tables of Annex F, I discover that the "adjustment" was that they guessed at an effective rate for the confounders and plugged that percentage in their math. "Oh, there must be about 15% more rich people than poor people who go to the doctor for any given condition, so let's adjust the results by that amount and see if things work!"

(I'm exaggerating for dramatization, these guess numbers are rarely "hidden" in this way and rarely this important, but even tiny examples of such piss me off and I get angry at the paper for it every time.)

Is there any conventional wisdom in the stats community about how far to trust these kinds of adjustments?

In my experience there's no general answer other than the observation that if people did NOT adjust for confounders, it's usually a very bad sign. But if they did, you actually have to go read the paper and form your own opinion on whether their adjustments look reasonable, whether they did them correctly, whether they picked the right confounders (or just grabbed whatever characteristics they had handy), etc.

Typically people don't adjust properly because it's against their incentives to do so.

It pretty easy to abuse controlling factors.

As a reader you don't always know how many different ways the people who made a study tried to adjust for different confounders till they got their result.

There are a few, but not many such studies, for obvious reasons. I list at least one in http://www.gwern.net/DNB%20FAQ#flaws-in-mainstream-science-and-psychology and IIRC, the correlation->causation rate was <10%.

"Contradicted and Initially Stronger Effects in Highly Cited Clinical Research" (Ioannidis 2005) is helpful:

Results Of 49 highly cited original clinical research studies, 45 claimed that the intervention was effective. Of these, 7 (16%) were contradicted by subsequent studies, 7 others (16%) had found effects that were stronger than those of subsequent studies, 20 (44%) were replicated, and 11 (24%) remained largely unchallenged. Five of 6 highly-cited nonrandomized studies had been contradicted or had found stronger effects vs 9 of 39 randomized controlled trials (P = .008). Among randomized trials, studies with contradicted or stronger effects were smaller (P = .009) than replicated or unchallenged studies although there was no statistically significant difference in their early or overall citation impact. Matched control studies did not have a significantly different share of refuted results than highly cited studies, but they included more studies with “negative” results.

In the history of medicine, 5 valuable facts about the causes of disease have been established by correlation: smoking => lung cancer, heart disease; sun => skin cancer; HPV is STD; alcohol => rectal cancer. The claim with the 6th most correlation evidence is that alcohol protects from heart disease, but this is controversial.

I'll leave it to you to compute the denominator.

Also, the number 5 is itself controversial. Some people put it at 2.

It's hard to calibrate one's skepticism towards correlational studies without knowing what the relevant base rates are.

The relevant base rates are likely to be much different between different subject domains.

There's a very interesting study that finds that parents with more morning sickness have babies with better neurodevelopmental outcomes (20% had IQ > 130, compared to 7% of those with less morning sickness).

The researchers suggest that for some reason the hormone involved in producing morning sickness also aids child development. It's possible, but a better explanation is the one in your first paragraph - everyone gets exposed to toxins but people vary in how diligent they are in eliminating them, and extra diligence helps.