The Trouble with Epigenetics (Part 2)
In Part 1 of this blog, I considered the various definitions of the term epigenetics and the confusion that can arise when they are conflated. Molecular epigenetic mechanisms modify chromatin structure and provide a means to stabilize a particular profile of gene expression. They also allow that profile to be passed on to a cell’s descendants, through mitosis. For this reason, epigenetic profiles have been called “heritable” (meaning through cell division). It is easy to see how that definition can be extrapolated to the idea that epigenetics could provide a means of heredity from one generation to the next.
This idea has attracted substantial interest, with many people seeming to think it overturns classical genetics (the inheritance of characters based on DNA sequence), and rehabilitates Lamarckian evolution by supplying a respectable molecular mechanism. This view has gained particular prominence of late in the study of behaviour and psychiatry, with the proposal that transgenerational epigenetic inheritance can provide a mechanism of heredity that explains the so-called “missing heritability” of psychiatric disorders.
The idea of transgenerational epigenetic inheritance is that epigenetic marks laid down in the cells of one generation (in response to some environmental factor or experience) can be stably passed through meiosis (into the germ cells) and thus affect some traits in the next generation. This kind of thing is indeed known to happen in some very specific circumstances, which are highly illustrative. This review by Daxinger and Whitelaw gives an excellent, up-to-date synthesis of this field. Most of the known examples involve the establishment of specific chromatin structures at DNA repeats or transposable elements – i.e., it occurs in very particular genomic contexts. In many cases, the transmission of this chromatin state through the gametes depends on an RNA molecule, as opposed to the more traditional DNA or histone protein modifications.
This is a fascinating area of biology (though more an embellishment than an overthrowing of normal mechanisms of inheritance), but is it relevant to psychiatric disorders? In particular, can it contribute to the heritability of such conditions?
Twin and family studies have clearly shown that many psychiatric disorders are highly heritable (with h2 values around 65-70% for schizophrenia and 75-85% for autism). Nevertheless, large-scale studies aimed at detecting DNA differences that contribute to this heritability have not turned up much. At least, this is true for genome-wide association studies (GWAS), which look for differences in frequency of common genetic variants between large numbers of cases and controls. Some people are interpreting the failure to identify specific causal variants as implying that the traits are really not that genetic after all. This is a complete fallacy.
GWAS analyse only the parts of the genome that harbor a common variant or single-nucleotide polymorphism (SNP) – these are positions in the DNA sequence where two forms commonly exist in the population (some might have an “A” base, while others might have a “T” in that position, for example). For autism, large-scale GWAS have not found any replicable SNPs associated with the disease. For schizophrenia, recent (still unpublished) very large GWAS have reportedly found 62 replicated SNP associations, but collectively these still only explain ~3% of the heritability. Does this mean that the observed heritability is really not accounted for by variation in DNA sequence? Not at all.
It has become clear over the last few years that rare mutations make a very large contribution to individual phenotypes, especially to the occurrence of diseases. GWAS do not survey these rare mutations and their failure to fully account for the heritability of the disorders therefore means nothing - really nothing at all - regarding that heritability. These disorders are still just as heritable and that heritability still means that most of the variance in whether people get the disease or not is down to genetic differences (in the DNA sequence). We do not need epigenetics to come to the rescue here. Unless rare mutations are also exhaustively surveyed and found to be unable to collectively account for the observed heritability, there is nothing to explain.
More to the point, even if there were, transgenerational epigenetic inheritance could not explain it. The heritability of these disorders has been estimated mainly from twin studies – these show that monozygotic twins are much more phenotypically similar than dizygotic twins. As the twins in each case share the same uterine and family environment, we can conclude that the reason MZ twins are more similar phenotypically to each other is because they are more similar genetically. The heritability of a trait or a disorder can be estimated from the strength of this effect and is defined as the proportion of phenotypic variance across the population that can be attributed to genetic variance. So, unless the supposed epigenetic marks affect MZ twins more consistently than DZ twins (and there’s no reason why they should), this mechanism provides no explanation for the key observation. Even if epigenetic mechanisms can provide some means of heredity from one generation to the next, that is not what heritability measures.
Moreover, the evidence that epigenetic mechanisms can provide a means of heredity for behavioural traits is not strong. In Part 1 of this blog I cited a few examples where particular experiences have a lasting effect on behaviour of an organism, in part by stably altering gene expression in particular cells in the brain through molecular epigenetic mechanisms. These kinds of effects can indeed be perpetuated across generations, for example, in the well-known observation that stressed female rats have stressed offspring. That is because stress reduces maternal care of the newborns, which is itself stressful and which sets up long-term changes in expression of the glucocorticoid receptor. But this is a behavioural transmission: mom’s behaviour affects offspring’s behaviour – repeat. This is not an example of epigenetic inheritance via the gametes, which is what has been proposed as a possibly important mechanism.
For that to happen, the epigenetic marks laid down in the brain by experience would have to also be laid down in the germ cells, maintained through the genomic “rebooting” that happens in the fertilized zygote (where the vast majority of epigenetic marks are wiped clean), carried through subsequent development, surviving the epigenetic upheavals entailed in the generation of all the embryonic cell-types that are ancestors of the eventual cells in the brain where the effect on this specific behaviour is mediated.
This is more an intuition than an argument, but this scenario seems inherently far-fetched to me. One expects experiences to modify gene expression in the brain, but not in the gametes. Scientists should, of course, be prepared to be surprised and delighted by unimagined discoveries that overturn our preconceptions. On the other hand, a healthy level of skepticism is usually a good idea, especially in cases where such discoveries are not attended by strong evidence.
So, is there any evidence that this can happen? Given the possible confounds attending maternal transmission, several groups have looked for evidence of transmission through the paternal germline. A study by Isabelle Mansuy and colleagues illustrates some of the problems that I see with this literature. This is definitively entitled “Epigenetic Transmission of the Impact of Early Stress Across Generations” and is cited over 100 times, so it has clearly been influential. This study involved stressing a young animal by unpredictably removing its mother for several hours at a time. When these animals grow up they show residual effects of this maltreatment (details below). So far, so good. It is further claimed, however, that this effect is passed on to the next generation and even to the subsequent one, through the male germline. Now, this is an extraordinary claim, one that should require extraordinary evidence. Instead, the bar seems to have been lowered.
I do not mean to pick on this one paper, but it exemplifies a general problem in this field – that of too many researcher degrees of freedom. This refers to studies that are exploratory in nature and that do not define a specific hypothesis to be tested in sufficient detail prior to collecting data. Researchers looking for a difference between two groups may carry out a range of tests and report any test that shows a difference or may decide, after the fact, to look for effects just in one sex or the other, or just in one age group, or just at one time-point, etc., etc. If there is no reason, a priori, to expect the effect to be specific in such a manner, then this is just significance-fishing. If the significance estimates are not corrected for the multiple tests carried out, then they do not accurately convey how surprised we should be by any one finding. (This is the difference between the odds of you winning the lottery and the odds of the lottery being won). See this xkcd cartoon for a great illustration.
The study by Mansuy and colleagues illustrates the cardinal sins of significance-fishing. The male mice that are directly stressed by having their mothers removed show “depressive-like” behaviours on two tests – the forced swim test and the sucrose preference test. These males were then bred to female animals that have not been stressed in any way and the behaviour of their offspring was tested. The result? Females, but not males in the next generation showed a significant difference (p < 0.1) on the forced swim test, but not the sucrose preference test. So, four tests were carried out and one was “significant”. In the next generation (breeding from what were phenotypically normal males), the pattern was reversed! – males showed a difference (p < 0.5, again, only on one test), while females showed none. (Additional tests of sensitivity to stress showed an effect in first-generation females but this time in second-generation females, while males showed no difference). None of these results was corrected for multiple testing, nor is there any putative mechanism or a priori hypothesis to explain the sex-specificity of the effects (which, to any impartial observer, seems like random noise).
Despite the weakness and selectivity of the actual data, the claim in the abstract of this paper is both forceful and sweeping: “Most of the behavioral alterations are further expressed by the offspring of males subjected to maternal separation”. This is clearly not supported by a proper statistical evaluation of the actual observations. Actually, I don’t know if I worded that strongly enough: the data in this paper do not support any conclusion of a behavioural effect being transmitted across generations. That’s better.
The same problems are evident in a recent paper claiming epigenetic transgenerational inheritance of a “cocaine-resistance” phenotype. In this case, it was expected that cocaine exposure in one generation would lead to increased sensitivity to it in subsequent generations. In fact, the reverse was found, and only in one sex. So, the direction of this effect was a surprise and presumably there would have still been a paper if the mice were more sensitive, rather than less. Similarly, there was no a priori expectation of a sex effect or hypothetical mechanism to explain it. If it had only shown up in females, I expect we would have heard about that too. That’s four bites of the statistical cherry.
Adding genomics to these studies (looking at profiles of gene expression or methylation, for example), and highlighting those genes that show a “significant” difference when considered alone, compounds this problem of multiple testing – the poor cherry is just being gnawed on now in the most unseemly fashion.
In general, the evidence of a real behavioural effect being transmitted through males to the next generation is not compelling. These studies also suffer from an additional possible confound – the possibility that interacting with a stressed or strung-out male animal will alter the behaviour of the female, post-mating, so that maternal care is also changed. This would be quite different from the model that some experience causes an epigenetic mark in the male germ cells that, in effect, transmits a “memory” of that experience to the next generation. The best way to test for such an effect is to see if it is really transmitted through the male gametes themselves using in vitro fertilization. One study that did just that found effectively no such transmission (again taking multiple tests into account).
So, while epigenetic mechanisms are implicated in the long-term effects of certain experiences, the evidence that such effects can be transmitted through the germline to subsequent generations is, to my mind at least, extremely weak. And even if they could be, they certainly cannot represent a solution to the mystery of the “missing heritability” for psychiatric disorders. These disorders are as heritable as they ever were and that still implicates differences in DNA sequence. Jut because we haven’t found them yet doesn’t mean we should start looking somewhere else.
Because real genetics.