Key paper in depression genetics disputed

I wanted to draw attention to a new paper in JAMA recently because it reveals a lot about how conditional most of the statements we make in behavioral genetics are. Every time you hear a news article that says, "Gene for depression found," I want you to think about this case.

Risch et al. performed a meta-analysis on 14 studies that were looking at Serotonin Transporter (5-HTTLPR) genotype and number of stressful life events. These two factors were related to the subsequent risk for developing clinical depression. Their analysis found -- contrary to a very well known study, Caspi et al. -- that there was no association between genotype for this gene and depression risk and no significant interaction between genotype and number of stressful life events.

I think this case is a good example of why we should be skeptical of behavioral genetics studies reported in the news until they have been replicated repeatedly.

Back in 2003, Caspi et al. performed a longitudinal study on roughly a thousand children that looked at the number stressful life events that had happened to them. Stressful life events could include things like losing a job or your parents getting divorced. Then at the age of 26 each of the participants in the study was evaluated for clinical depression according to standardized criteria. Samples were also taken for genetic testing particularly at the gene for the serotonin transporter, 5-HTTLPR. (The choice of the gene to evaluate made sense because many of the drugs we use to treat depression modify activity of the serotonin system in the brain.)

The authors asked: how do a particular genotype of the serotonin gene and stressful life events interact to influence depression risk? Does having a certain genotype PLUS several stressful life events increase your risk?

Their results were stunning primarily because they so clearly illustrated the concept of a gene-environment interaction: the idea that neither your genes nor the environment is sufficient to cause depression; rather, depression results from a confluence of both factors.

Here is an example of their data (from Figure 2 of the paper):


The results show risk of depression (in percent, from ages 18 to 26) as related to whether the participant was mistreated as a child (from the ages of 3 to 11). The participants are broken up according to whether they have two of the short forms of the serotonin transporter gene (s/s), are heterozygotes for the long form for serotonin transporter (s/l), or have two copies of the long form (l/l).

In the absence of childhood mistreatment, there is no difference between the three genetic groups with respect to depression risk. Likewise, if you possess two copies of the long form (l/l) childhood mistreatment does not increase your risk. However, if you possess two copies of the short form (s/s) AND you were subjected to childhood mistreatment, your risk of depression doubles.

This and other data was used to argue that what determines whether an individual will get depression is a gene-environment interaction. Genes confer risk for depression, but only in the presence of stressful life events does a particular genetic makeup manifest.

I want to make something clear through all of this: Caspi et al. is an extremely well done paper. Up until reading this meta-analysis, I considered it the benchmark for these kinds of studies. Even realizing that the findings may have been a false positive, I still respect it. So I don't want to suggest that I am trashing this work.

After Caspi et al., there emerged many other papers that attempted to find gene-environment interactions in the similar way. Primarily this was because Caspi et al. addressed a problem that had been quite prevalent in behavioral genetics: small and non-reproducible effects.

A common problem in studies attempting to relate genetics with a particular behavior is that a particular genotype might only confer a very small risk. Also, behavioral genetics studies are notoriously difficult to replicate. Say you find a significant relationship between gene A and depression. Then you go and try and replicate that finding in another population. A lot of the time, you will find that it is no longer significant in the new population. Sometimes that is because it was a weak correlation, and you don't have enough people in the study. Sometimes it is because in the new population, the genetic background for their other genes masks the effect of gene A on depression. (This is called an epistatic interaction.)

The point is that behavioral genetics studies were dealing with a problem of reproducibility and small effect sizes. Caspi et al. demonstrated a way to identify more significant effects. If you can show that a subset of your population with a particular environmental history, there is an even greater association between the disease and their genotype, you can argue that the interaction between the two potentiated the effect of the gene. It also explains why there was so much trouble finding a significant gene-disease correlations: there were aspects of the population that you were missing.

If you think about it, the concept of a gene-environment also makes a great deal of sense. Let's set aside the fact that biological systems show these all the time for physical traits. (It is a core principle to our understanding of evolution.) An individuals behavior is the consequence of many, many genes and many, many environmental interactions. To say that a single gene could result in a behavior, we would have to assume that it was relatively robust to a variety of environments that the individual might experience -- that regardless of environment, the person would still show the behavior. But this argument belies the extreme variability that is present in human behavior. Even among identical twins there is a great deal of variation in personal preference, environment, and hence the risk for disease.

My point is that you can't take too much of an issue with Caspi et al. for arguing for the existence of gene-environment interactions in producing behavioral outcomes because they make too much sense in light of what we already know about biology.

The problem, unfortunately, came in trying to verify the results of their work.

Risch and colleagues performed a meta-analysis using the original data from 14 studies that had attempted to replicate the findings of Caspi et al. These studies also looked at the roles of stressful life events, genotype at the serotonin transporter gene, and the resulting depression risk. In contrast to the earlier work, the authors found no relationship between serotonin transporter genotypes or the interaction and depression risk. The only significant predictor they found was the number of stressful life events:

In the meta-analysis of published data, the number of stressful life events was significantly associated with depression (OR, 1.41; 95% CI,1.25-1.57). No association was found between 5-HTTLPR genotype and depression in any of the individual studies nor in the weighted average (OR, 1.05; 95% CI, 0.98-1.13) and no interaction effect between genotype and stressful life events on depression was observed (OR, 1.01; 95% CI, 0.94-1.10). Comparable results were found in the sex-specific meta-analysis of individual-level data.

Note that this meta-analysis was performed on about 14 thousand participants from other studies. Hence it has a much greater statistical power than the previous study.

What do we make of this conclusion? How is it possible that such a well-constructed study -- that had become a model for a variety of other studies -- ended up being wrong?

Well, first of all, I should note that the lead author from the original study does not necessarily agree with the findings of this meta-analysis. From the NYTimes coverage:

Others said the new analysis was unjustifiably dismissive. "What is needed is not less research into gene-environment interaction," Avshalom Caspi, a neuroscientist at Duke University and lead author of the original paper, wrote in an e-mail message, "but more research of better quality."

I would say a couple of things:

  1. 1) No one in the coverage I have read of this story -- including the authors of the meta-analysis -- is disputing that gene-environment interactions exist for behavioral phenotypes or that these studies NEED to continue being done. In fact, most of the coverage of this study has shown an very interesting doublethink, denying the accuracy of the original Caspi study findings while singing the praises of its theoretical basis.
  2. 2) This is exactly the type of back and forth that we should expect from behavioral genetics studies. We should have a great deal of reticence when we read about studies like this in the news.

Behavior is affected by many, many genes. No one ever believed that just one gene was going to explain all of depression or any other mental illness. This is primarily why the effect sizes in these studies are so small: because behavior is so polygenic. Furthermore, when you are dealing with small effect sizes in complex systems, you have to prepare yourself for the possibility of sampling error. Caspi et al. was not a small study, but it also should surprise us that an analysis of a larger population yielded different results.

The point, I guess, is that we can simultaneously dispute the relevance of this particular gene, the serotonin transporter, in affecting depression risk while still believing in the concept of a gene-environment interaction.

We just have to be very, very careful when we assert with certainly the association of a particular gene. Results that look too good to be true often are.

Hat-tip: NYTimes


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