The Trouble with Epigenetics, Part 3 – over-fitting the noise
The idea of transgenerational epigenetic inheritance of acquired behaviors is in the news again, this time thanks to a new paper in Nature Neuroscience (who seem to have a liking for this sort of thing).
The paper is provocatively titled: “Implication of sperm RNAs in transgenerational inheritance of the effects of early trauma in mice”. The abstract claims that:
“We found that traumatic stress in early life altered mouse microRNA (miRNA) expression, and behavioral and metabolic responses in the progeny. Injection of sperm RNAs from traumatized males into fertilized wild-type oocytes reproduced the behavioral and metabolic alterations in the resulting offspring.”
Unfortunately, the paper provides no evidence to back up those extraordinary claims. It is, regrettably, a prime example of over-fitting the noise. That is, finding patterns in a mass of messy data, like faces in clouds, and building hypotheses on them after the fact. If any change in any parameter will do, it isn’t hard to find support that “something happens”. I have written about this problem before, exemplified by previous papers from this group. I normally try not to be sarcastic here, but I don’t have time to edit today, so you’re getting raw, unfiltered exasperation this time.
There are some documented examples of transgenerational effects mediated by RNAs in sperm, especially in worms and plants. Almost all of these involve repression of transposon or transgene insertions. This is not believed to be a widespread phenomenon in mammals, however, and you don’t need to (and shouldn’t!) take my word for it – the following is from a very recent review by leaders in this field:
"...epigenetic inheritance is usually—if not always—associated with transposable elements, viruses, or transgenes and may be a byproduct of aggressive germline defense strategies. In mammals, epialleles can also be found but are extremely rare, presumably due to robust germline reprogramming. How epialleles arise in nature is still an open question, but environmentally induced epigenetic changes are rarely transgenerationally inherited, let alone adaptive, even in plants. Thus, although much attention has been drawn to the potential implications of transgenerational inheritance for human health, so far there is little support."
Shutting down a transposon in gametes and the resultant offspring is one thing – it’s a pretty straightforward molecular mechanism, actually. Using such a mechanism to transmit a behavioural change induced by an experience in the previous generation is something else entirely. What that would require is the following sequence of events: animal has an experience, experience is registered by the brain (so far, so good), signal is transmitted to the gametes (hmm, by what?), relevant gene or genes are specifically modified (how? why just those genes?), modification is maintained in the zygote through “genome rebooting” (what, now?), modification is maintained throughout subsequent development of the animal and the brain (really?), but in a selective way so that somehow in the adult it only affects expression in certain brain regions so as to initiate an appropriate behavioural change in the offspring (ah, c’mon, now you’re taking the piss...).
That is why my skepticometer gets pegged by studies that make such claims without documenting or even suggesting a plausible mechanism by which such events could occur. The current paper takes a stab at one part of that, by looking at small non-coding RNAs as a possible mediator. Unfortunately, the paper is… well, let me show you.
The authors use a paradigm which they developed previously (in one of the papers which I criticised here), to induce what they call a traumatic stress. This involves “unpredictable maternal separation combined with unpredictable maternal stress (MSUS) for 3 hours daily from postnatal day 1 through 14 (PND 1–14)”. The pups don’t like that, apparently, and the authors claim they grow up to show “depressive-like behaviours”. I find those behavioural data a bit shaky, but they get much worse in the following generations, when the responses vary in one test, in one sex in one generation and then in another test in the other sex in the next. It all looks like noise to me, and, the authors neither correct for all these multiple tests, nor provide any hypothesis to account for these fluctuating effects.
In their 2010 paper, they looked at DNA methylation of some candidate genes in F1 sperm and F2 brains to see if they could find a molecular mechanism. Here’s the figure:
There are a lot of asterisks on there, indicating some changes that are statistically significant (alone), but you’ll notice how many different measurements they have made and, also, I hope, the lack of consistency in the supposed effects from F1 to F2. Importantly, there is no independent replication – just one big experiment with the stats done on the whole lot at once. It is no surprise that some data points come out as significant. I’m thinking of green jelly beans…
You can see the same kind of thing in the figure below from this recent paper, which also got a lot of media attention: “Parental olfactory experience influences behavior and neural structure in subsequent generations”
In both cases, the data look to me like noise.
Now, back to this latest paper. Amidst a load of somewhat peripheral data, the data supporting the two main claims of the paper are the following: First, the authors claim that the maternal separation protocol alters the levels of various small non-coding RNA molecules in the sperm of the F1 mice (the ones whose moms were cruelly taken away). The data for that claim are in Supplemental Figure 2, which I reproduce below. You will see it derives from three pools of mice for the control condition and three pools from the MSUS condition.
I see no consistent pattern of changes here. There looks to be as much variability within conditions as between. (Take MSUS pool 2 out and you wouldn’t be left with much signal, I would wager). I am sure there is some statistical test that would give you a significant result, but if you torture the data enough, they’re bound to try to tell you something.
Their next figure takes some of these specific miRNAs and examines their expression levels in sperm, serum and various brain regions of F1 and F2 mice. Again, the data are all over the place. They’re up, they’re down, they’re not changed. They’re changed in hippocampus but some go in the opposite direction in hypothalamus and none are changed in cortex (Supplementary Figure 10 for those reading along at home).
That’s some noisy noise right there. Notably, they see no changes in sperm of F2, even though the F3 supposedly still show behavioural changes, rather undermining their own case for the link between these two (non-)events.
Their next step is the one that the main conclusion rests on – to show that injection of small RNAs from the sperm of an MSUS F1 mouse into a fertilised oocyte can induce the suite of behavioural changes they (claim to) see in the F2 generation under normal conditions.
Amazingly, they do not actually show those data. We get summary t statistics claiming there are some differences but are not treated to the actual data themselves. So, we can’t evaluate the effect sizes or the underlying variability of the data. Here’s how it reads in the paper:
They do show a supposed effect on metabolism in the MSUS-RNA-injected animals, which is a difference seen in one experiment with 8 animals per group in glucose levels, not at baseline, but after stress. I have no idea what’s going on here or what the hypothesis is supposed to be – are we supposed to expect greater or lower glucose? At baseline or after a stress? Whatever is happening, it’s not consistent between the F1 and the F2 in the traditional paradigm, nor between the traditional F2 and the MSUS-RNA-injected F2.
Finally, we are shown that the levels of one of the miRNAs differs in the hippocampus of the MSUS-RNA-injected F2. Doesn’t look very convincing to me, by itself – it’s the kind of result one might want replicated before publishing, but more to the point: Why that one? What about all the others whose levels fluctuated so happily in the figure shown above?
Overall, there’s no there there. It’s all sound and fury, signifying nothing. I would give it the ultimate insult by saying it’s not even wrong, but it is.
Nevertheless, this paper is sure to be latched onto by the woo crowd who seem to think that epigenetics is some kind of magic. (Now I have that Queen song running in my head - you're welcome). We can change our genes! They’re not our destiny! Toxins cause autism because epigenetics! Hooray!
Evolution appears to have made us mammals very delicate creatures. If you look sideways at a mouse these days you can permanently alter its genes, it seems, along with those of its kids and grandkids. Of course, you’d think another look might change them back if they're so sensitive, but apparently not. I’m sure your genes (ooh, and brain circuits!) have been changed by reading this, for which I can only apologise.
This comment has been removed by the author.ReplyDelete
After I saw some articles about this publication, I was thinking to write a popularized article about it for my blog, dealing with the latest news in science, for a general audience. I have therefore read the cited article, as well as their 2010 paper. And indeed, there are major inconsistencies and "clouds", which you reviewed very nicely (I like the sarcasm :) ). However, taking only males (yes, I know...), there is still a trend for transgenerational transmission of what they call depression, and a change in miRNAs as well. So, right, far for being perfect, and extrapolated, but I believe there is still something interesting here.:)ReplyDelete
Anyway, great blog, and great article, I will come back for sure!
This comment has been removed by the author.ReplyDelete