Caloric restriction slows brain aging

Aubrey de Grey ag24 at mole.bio.cam.ac.uk
Fri Jul 7 10:47:25 EST 2000


Randall Parker wrote:

> What are the top 5 or 10 things you'd like to see tried?

They fall into two categories: direct development of the interventions
and conclusive demonstrations that the interventions wouldn't work.  I
consider that the most conclusive experiment showing that a process
does not contribute to mammalian aging during a normal lifetime is to
speed it up and observe no reduction in lifespan.  Such results are
often downplayed - characterised as "negative results", which is really
a misuse of a term that should be restricted to cases where the result
could have occurred just because the experiment was done carelessly.
Also, unlike the other type of conclusive experiment (trying to retard
aging by intervention), the result that is informative actually OCCURS
every so often, whereas successful and reproducible life-extension in
mammals is decidedly hard to come by.

So, what follows is a list of what I see as main candidates for crucial
degenerative processes underlying aging, followed by (a) an experiment
doable now (when I can think of one) that would show it wasn't such a
process, and (b) a project doable now (albeit usually rather ambitious)
that would result in reversal of that process in mice.

1. Accumulation of mutant mitochondrial DNA

Falsification experiment: Mutate an appropriate mtDNA repair and/or
replication gene so as to increase, modestly, the rate of accumulation
of such mutations.  If lifespan is unaffected, mtDNA mutations do not
determine the rate of mouse aging.  This is very close indeed -- see
Ann N Y Acad Sci 893:353-357.  I think all that is needed now is a
somewhat milder mutation than Zassenhaus's group has isolated.

Intervention: Allotopic expression of mtDNA-encoded proteins (making
transgenic copies placed in the nucleus and suitably modified so that
the proteins would get back into mitochondria).  I've discussed this
in the past so I won't go into more details now; it's a big subject
which has been under consideration for 15 years.  See Medline, and
also a review I have in press in Trends in Biotechnology which will
be out in a few months.  I am very confident this could be achieved
in mice in under five years with appropriate funding (say $1m/year).

2. Accumulation of lipofuscin

Falsification experiment: Speed it up by dietary manipulation.  This
has sort of already been done, in that vitamin E deficiency is said
to have this effect (and does not have much effect on lifespan), but
that result is controversial, because others say that the stuff that
accumulated when vitamin E is low isn't real lipofuscin.  I'm hoping
that this will be resolved soon, but very few people work on it at
the moment.

Intervention: I'm currently collaborating with a colleague here in
Cambridge on a very ambitious idea: to find bacteria that can break
down lipofuscin, identify the relevant genes and get them into mice.
The first part is going well - my colleague works on a type of bug
that eats essentially anything (including TNT, for example) and it
seems to eat lipofuscin.

3. Replicative senescence

Falsification experiment: We already know that telomere length does
not limit mouse lifespan (Blasco 1997 etc).  Where this leaves the
replicative senescence theory of aging is with two major hypotheses:
(a) that what matters is telomere length relative to some kind of
marker set down early in embryogenesis, as opposed to absolute
telomere length, and (b) that replicative senescence is not driven
by telomere shortening in mouse, even though it is in humans, so it
might drive mammalian aging in general after all.  Theory (a) is not
completely out of the question, but would be forcefully eliminated
by showing that mouse cells underwent replicative senescence without
telomere shortening: on present data we can't quite say that, but
mouse cells with high constitutive telomerase should be around soon.
Theory (b) would be best tested by exploring what process determines
mouse replicative senescence, proving it does so by eliminating that
senescence (analogous to constitutive telomerase), and then making
it go faster in a live mouse (analogous to the telomerase knockouts).
Then, if lifespan is unaffected we can forget about replicative
senescence as a player in mammalian aging.  Experts on replicative
senescence in mice that I have talked to (the UK is especially
strong in this area) consider this a few-year project (again, with
adequate funding).

Intervention: Doing in vivo what was found to eliminate replicative
senescence in vitro (in mice).  Such therapy in humans is of course
being energetically pursued already, but we still need to do the
mouse experiment in order to assess side-effects.

4. Cell loss (various cell types, including glands)
5. Glycation-induced cross-linking

These are being energetically and successfully addressed (somatic
cell therapy and AGE-breakers, respectively) and I have nothing to
add to what's been discussed extensively here.

6. Accumulation of nuclear mutations not related to cancer
7. Dysregulation of nuclear genes (loss/gain of methylation, etc)

Falsification experiment:  I doubt that it will be possible to
get a true assessment of the role of non-cancer-related nuclear
DNA damage (whether mutations or dysregulation) until we have very
effective anti-cancer interventions in mice.  Angiostatins may
provide that soon; then a number of interventions known to cause
more mutations (such as folate deficiency) will be informative.

Intervention: Nothing presently seems to me to be anywhere near as
feasible for this as for the other types of degeneration discussed
above.  Suggestions welcome....

Aubrey de Grey







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