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.
