Bayesian Investor Blog

I wrote this post to try to clarify my thoughts about donating to the Longevity Research Institute (LRI).

Much of that thought involves asking: is there a better approach to cures for aging? Will a better aging-related charity be created soon?

I started to turn this post into an overview of all approaches to curing aging, but I saw that would sidetrack me into doing too much research, so I’ve ended up skimping on some.

I’ve ordered the various approaches that I mention from most directly focused on the underlying causes of aging, to most focused on mitigating the symptoms.

I’ve been less careful than usual to distinguish my intuitions from solid research. I’m mainly trying here to summarize lots of information that I’ve accumulated over the years, and I’m not trying to do new research.

Abstract research

A large number of aging researchers focus on pure science of what causes aging, without much attention to how we might engineer cures.

This makes some sense if we don’t understand aging well enough yet to guess where to look for cures. But advocates often talk as if all knowledge were equally valuable. I prefer to value research in proportion to how likely it is to save lives, so I assign low value to this kind of research.

Aging clocks

Epigenetic clocks deserve some attention, but I didn’t find time to say much about them.

SENS

Aubrey de Grey’s SENS vision claims that we know enough about aging to make plans to intervene on any pathway that might be an important cause of human aging.

This belief is somewhat dependent on the assumption that researchers stopped finding new causes of aging many decades ago because they found all that are there. That seems like the most obvious explanation. But it also seems somewhat possible that researchers stopped finding new causes because the increasing centralization of science discouraged independent thought, or something similar that contributed to the Great Stagnation.

The main downsides are that it will take plenty of time and money to get a full cure for aging. There will likely be some benefits from partial cures, but SENS’ main claim to being the best approach comes from the possibility of a full cure.

I donated a decent amount to the Methuselah Mouse Prize back when it was young, as the funding levels then were small enough that my donations could plausibly have a decent-sized impact on how prestigious Aubrey’s approach looked.

But now SENS progress depends on much larger budgets, and it’s no longer obvious how to donate specifically to the prize fund, and it’s harder to evaluate the competence of any particular research, so I’m not currently donating to any SENS-related projects.

If my charity budget were over $100 million per year, SENS would likely be near the top of my list. But since my actual budget is much smaller, I’m focusing more on smaller charities that are more likely to be overlooked by big philanthropists.

LRI’s approach

LRI intends to focus on mouse studies of simple interventions that have already shown some promise.

This approach looks more like mainstream medical approaches than do most attempts to cure aging.

I expect that the medical establishment has focused too much on simple approaches, mostly single-molecule treatments that target one receptor or metabolic pathway.

Some of that is due to what’s patentable.

Some of that is due to copying approaches from how we repair machines: look for simple problems with simple fixes. That approach is misguided when evolution would have fixed the problem if it were simple[1], and has optimized enough that simple changes are much more likely to break something that to improve it (or maybe medical researchers don’t really believe we’re the result of evolution?).

Some of it might be due to widespread expectations that the low-hanging fruit is gone, and only tiny advances are possible. Or maybe that tiny advances generate as much revenue as major breakthroughs, and major breakthroughs cost more. In my more pessimistic moods, I sometimes worry that most new medicine of the past few decades has been zero-value products that got lucky.

LRI is trying to counteract the bias toward patentable interventions, but seems to be mostly going along with mainstream attitudes of looking for small fixes.

The mainstream has a wide range of attitudes toward biomarkers, and LRI takes one extreme end of that range, distrusting all biomarkers.

It looks superficially faster than the prior two approaches.

Yet I expect some of the time to market will be determined by the length of human trials, and those trials are likely to go faster for the more ambitious approaches. Much of the reason that typical drug trials take a long time these days is that even the best new drugs are only marginally beneficial. If a treatment makes a 80 year-old as healthy as a 65 year-old, the benefits will be obvious enough that trials shouldn’t need to take much more than a month or two in order to produce clear evidence[2]. Whereas LRI seems to be aiming for treatments that are likely to effectively make patients a month or two younger[3]. Those treatments require longer trials and/or much larger sample sizes.

The main downside: it only aims for modest life extension, not close to escape velocity.

The initial stages of LRI’s approach are quicker and cheaper than most aging strategies, but I still see high costs to getting treatments to the stage where humans can benefit from them.

The Bredesen approach

Dale Bredesen’s approach to Alzheimer’s seems likely to help with at least half of all age-related diseases (weighted by their contribution to mortality, so I’m mainly talking about cardiovascular problems and diabetes).

This approach is the opposite of the LRI approach in some significant respects: heavy reliance on standard biomarkers, low reliance on mainstream research methods, and high tolerance for complex models and interventions.

There’s a risk that many of the biomarkers are symptoms, not causes, of age-related diseases, in which case arbitrary interventions to fix the biomarkers would be not too promising.

That risk is somewhat mitigated by preferring interventions that attempt to emulate the conditions under which our ancestors evolved. There’s a decent amount of evidence that many age-related diseases are exacerbated by western lifestyles. So to the extent we guess right about how to reproduce the advantages of ancestral lifestyles, the biomarker improvement ought to be due to fixing the root causes even if the biomarkers are only reporting the symptoms.

So this should combine the best of modern and ancestral environments, to get us to the life expectancies that we’re evolved to have when conditions are good.

Bredesen’s use of complex models and interventions raises some concerns, but my intuition says that his approach has value even if many of the details are wrong.

The downsides: it requires lifestyle changes that are sometimes large and restrictive; it doesn’t aim to increase maximum lifespan, but holds a decent hope of quickly adding a few years to life expectancy, and of improving the quality of life for the elderly.

This approach probably could make more productive use than any others of a few tens of millions of dollars of additional funding, but it’s gotten enough attention that it seems more likely than most other approaches to get increased funding soon. Still, it’s far enough from the mainstream that it wouldn’t take much of a mistake for funders to shun it.

I don’t currently see a good way to donate money to advance this approach.

There’s the Buck Institute, which had some involvement in Bredesen’s work. But I’ve heard Buck’s current president, Eric Verdin, speak, and I didn’t see signs that he’s eager to support Bredesen’s approach. He seems more likely to focus on low-controversy research, and doesn’t seem to share Bredesen’s sense of urgency to get help to people.

I presumably could donate to Bredesen’s company. I don’t have clear intuitions about how effective this would be. I’m uncertain whether I’m irrationally skeptical about donating to a profit-oriented company.

Human studies versus rodent studies

So, how desirable is LRI’s focus on mouse studies?

Mouse studies don’t have a great track record for translating to human drugs.

There’s some reason to hope that that’s due to mouse studies having used poor conditions. Caged mice have unnatural environments (cold stress, and the lack of burrow-like protection from predators might cause some anxiety).

Modern humans seem to have environments that are approximately as unnatural, but in somewhat different ways. How much overlap is there between the two types of unnatural stress? That seems hard to answer.

LRI is committed to avoiding the cold stress problems, so there’s hope that future mouse studies will be more informative.

Still, the value of mouse studies depends heavily on guesses about how similar mouse aging is to human aging.

There’s a good deal of variation between species in the symptoms and timing of aging. On the other hand, genes that contribute to aging seem to be conserved across species. That combination seems confusing.

Why does evolution permit aging to happen?

Different theories of why aging evolved have different implications for how similar mouse aging is to human aging, with somewhat different implications for the relevance of rodent studies.

The leading spandrel theory, antagonistic pleiotropy (AP), suggests that there’s evolutionary pressure to avoid aging, which should be proportional to the fraction of the population that dies of age related causes (often well over 25%). Maybe that looked consistent with aging mechanisms that are stable over long evolutionary periods when we thought a gene needed to remain active for life, but now that we see frequent changes in gene expression, it seems hard to explain why we don’t evolve better old-age gene expression, given plenty of time.

So I’d expect AP to predict that a medium fraction of human aging is due to mutations that are new since primates and rodents diverged, although there’s a lot of uncertainty about that prediction.

The disposable soma theory does seem more consistent with aging working roughly the same in all mammals, but it has serious problems with explaining the benefits of calorie restriction and exercise, so I don’t take it very seriously.

What about programmed aging theories?

The more serious models suggest multiple aging mechanisms, to deter genes with short-term benefits from quickly evolving a longer lifespan at the cost of whatever it was that created selective pressure for aging (population stability, diversity, and/or evolvability).

Programmed aging suggests that aging mechanisms are somewhat likely to be conserved across distantly related species, although it seems likely that some of them would be actively turned off or modified by evolution in the longer-lived species.

So they seem to imply that a full cure for mouse aging is likely to work well for humans. A partial cure for mouse aging is harder to evaluate. Did the cure just redo what evolution did when moving from mouse lifespans to human lifespans, since what was easiest for evolution was also easiest for medical researchers? If so, most such partial cures would do poorly in humans.

So, remember that I said aging genes were conserved across species? It’s a bit more dramatic than I let on:

We identified 64 genes that can extend lifespan when inactivated postdevelopmentally. More than 90% of the genes we identified are conserved from yeast to humans.

Putting this all together, my intuition says that for simple treatments that modestly delay aging in mice, there’s something like a 5% to 25% chance that any particular one will work well in humans.

Conclusion

Here are my attempts to compare the approaches (most of these numbers are crude intuitive guesses):

	importance (hoped-for QALY’s)	tractability	neglect	Probability of success (given the indicated funding level)
basic research	10^10	low	low	10% ($20 billion)
SENS	10^10	low	medium?	50% ($20 billion)
Clock	10^10?	low-medium?	medium?	20% ($1 billion?)
LRI	10^8	medium	high	40% ($2 billion)
Bredesen	10^9	medium?	medium?	75% ($200 million)

There are enough uncertainties about aging that multiple approaches ought to be getting more funding than they currently get.

LRI is promising enough that someone ought to be funding it. For small donors who focus on aging, LRI currently looks like the best option. But my intuition says that there’s a decent chance that I’ll find a better option in a few years. So I’m wondering whether it would be better to delay any decision.

I’m currently guessing that I can find better charities outside of the aging area, although the rate at which x-risk charities are becoming well-funded leaves me uncertain as to how much longer that will be true.

Writing this hasn’t been helpful at deciding where to donate. Maybe it will elicit some feedback which will help, or will help others decide where to donate.

Footnotes

[1] – even if evolution is actively selecting for aging, it would likely do so in a way that makes it hard for an organism to find a quick way to cheat, much like there are mechanisms to deter organisms from easily abandoning sexual reproduction for asexual reproduction.

[2] – there’s probably something that will in practice cause more delay than this; I don’t know enough to evaluate how much that varies between approaches.

[3] – or which need to be taken for a decade in order to show a medium-sized benefit. I’m pessimistic about the value of developing that kind of treatment, as I expect that there are better alternatives.