Aging, like many parts of biology, has a surplus of excellent experimentalists but a shortage of good modeling/analysis/theory. LessWrong and the adjacent community have a surplus of people with great modelling/analysis skills, many with an outsider’s interest in aging, so this post outlines a few problems which could fit that skillset. I expect that all of these could be solved to a reasonable degree of certainty with careful modelling and some beyond-high-school-but-not-revolutionary statistics, using already-existing data. For a publication-quality example of the sort of project I have in mind, check out the analysis of Burd et al’s data toward the beginning of this paper, or the modelling in this paper. (I'd also be happy even with something more back-of-the-envelope than these, as long as the approximations made sense and the predictions/assumptions were checked via multiple channels.)
Note that these are all open to the best of my knowledge. I’d be quite surprised to find existing analyses of the sort I have in mind, since it's not the sort of work academic biology usually incentivizes, but it’s not out of the question.
Atherosclerosis: How Much Oxidation?
For a couple decades now, it’s looked like oxidation of lipids (aka fats) is a mediating upstream cause of atherosclerosis - i.e. whatever the root cause of aging is, its effect on atherosclerosis is mostly mediated by lipid oxidation. There’s also been some mathematical modelling of the lipid oxidation -> atherosclerotic plaque formation process.
Obvious next question: what causes the rate of lipid oxidation to increase with age? Obvious hypothesis: reactive oxygen species (ROS), e.g. superoxide and fenton reaction products. ROS play major roles in multiple theories of aging and have confirmed roles in many aging processes, so they’re a natural culprit. But which specific ROS are involved here, and what upstream change causes an increase in concentration of those particular ROS?
I’d like to see someone use models like those linked above to estimate how much lipid oxidation needs to increase to account for age-related development of plaques, then do some back-of-the-envelope calculations on how much we’d expect from specific sources/theories, and compare the two.
For example, one model might be that senescent cells spew ROS, so the age-related increase in senescent cells causes the increase in lipid oxidation. In that case, we’d want to either estimate or find an empirical measurement of ROS production by senescent cells (and which specific ROS are produced), look up the age-related increase in senescent cell count, and then calculate the expected increase in ROS production. (Important note: presumably we want to know about extracellular ROS production, not just ROS production within the cell.) We could also think about variants of this hypothesis - for instance, maybe lipids are oxidized within the senescent cell or its membrane and then exported, rather than being oxidized in the bloodstream, in which case we’d want to find or estimate numbers for that export rate.
Another model might focus more exclusively on fenton chemistry - the iron-catalyzed production of ROS directly from peroxide. Then we’d want to look up estimates of fenton reaction activity in the bloodstream, as well as age-related changes in iron levels and peroxide concentrations, and see how the expected change in ROS production compares to the numbers needed to account for atherosclerosis.
Yet another model would be the mitochondrial free radical (MIFRA) theory. Aubrey de Gray’s book laid out a pathway by which cells with mutant, non-functional mitochondria could continue to live, but would export large amounts of radicals. There is data available on the number of cells with mutant mitochondria (and even on which mutations are present), so presumably one could estimate the expected change in radical production by such a mechanism, and compare it to the numbers needed to account for atherosclerosis.
Finally, changes in antioxidant concentrations could be useful to look at. I doubt that they’re actually the main causal mechanism here, but any age-related change in antioxidant levels would multiply the impact of any other mechanism, so depending on how much precision we can get we might need to account for antioxidant changes in order to make the numbers add up.
There's some evidence that senescent cells can induce senescence in healthy neighboring cells ("senescence-induced senescence"). This can’t account for the age-related increase in senescent cells by itself - senescent cells turn over too quickly. If senescent cell counts were in self-reinforcing exponential growth via this mechanism, then aging would take place on a timescale of weeks or months rather than decades. However, senescence-induced senescence could contribute a multiplier effect to some other cause of cellular senescence, one which at first seems too small to account for the age-related increase in senescent cell count.
That said, the multiplier effect can only be so large. The larger the multiplier, the closer the system is to instability (i.e. exponential growth of senescent cells on a timescale of weeks/months). If it’s close to the threshold, then we’d expect to sometimes see a supercritical explosion of senescent cells when some outside stressor happens to push the system past criticality - again, on a timescale much faster than aging. More generally/qualitatively, a system very close to criticality should show a loss of homeostasis on a faster timescale than what we actually see.
Anyway, the main question is, just how big is that multiplier?
Then the next question is: what's an upper-bound estimate on the fraction of senescent cells in an animal which are long-lived (based on e.g. the data here)? We know (from that linked paper) that senescent cells turn over on an average timescale of weeks, but if a small fraction of them are long-lived and there’s a large multiplier from senescence-induced senescence, then the long-lived senescent cells could be a plausible root cause of the age-related increase in shorter-lived senescent cell counts. Is it at all plausible that some type of long-lived senescent cells can causally account for the number of short-lived senescent cells growing with age, or can we ignore that mechanism in our search for a root cause?
The Mitochondria-Senescence Bistable Switch
Probably the most interesting combo of papers I've encountered lately: senescent cells and cells with inefficient mitochondria are probably the same cells. There's a positive feedback loop at the center of it all, so any of genotoxic stress, mitochondrial inefficiency, double strand breaks/telomere loss, or probably other stressors can induce any others of those. There's even potential lock-in mechanisms: selection for deficient mitochondria or activation of transposons. The question is, which factors are the chicken and which the egg?
A relevant conceptual model here is the bistable switch. The cell has two states: normal and senescent. Both states are stable: if there’s a small stress to the system, negative feedback will push it back to normal. But if there’s a sufficiently large stress, then a positive feedback loop kicks in, pushing the system into a new state - until eventually the new state’s control system kicks in and everything stabilizes again.
The challenge is that many different factors can be involved in the positive feedback cycle, and a sufficiently large increase in any one of those can cause the switch to flip (i.e. cause a normal cell to senesce). So, if we see an increase in senescent cells, then we’ll see an increase in genotoxic stress and mitochondrial inefficiency and telomere loss and …. If we experimentally induce any one of those, then we’ll find that it causes the switch to flip - any of them could be causal. But it’s difficult to tease out which change occurred first.
Mitochondrial mutations and transposon activation are two factors with slow enough timescales to potentially account for age-related change, but maybe there's some other we don't know about, or maybe there’s an intermediate fast-timescale cause and the root cause is even further upstream. Any sort of model which untangled causality in this system would be great. Two possible approaches to narrow it down:
- To the extent that senescent cells turn over quickly, the cause of the switch-flip must come from some other cell or extracellular factor. (Though this might include the senescent cell’s parent.)
- Whatever the original cause is, we might expect to see it change more even before the switch flips - i.e. at younger ages, or in non-senescent cells.
… or you might have some other clever idea to tease out the first mover. One way or another, we’d need quantitative analysis to inspire any sort of confidence in the answer; it’s the sort of problem which tends to have subtle failure modes.