(Crossposted from Hourglass Magazine: https://hourglass.bio/blog/2018/9/27/cost-effectiveness-of-aging-research-why-solve-aging-part-3)
Is aging research a cost-effective way of preventing death and illness? How does it compare to medical research more generally, or to medical treatment, or to treatment of infectious diseases in poor countries?
This post is going to try to answer that question, in a quantitative but very approximate fashion.
If you want to play with the numbers for yourself, you can check out the spreadsheet or Guesstimate model.
Dr. Owen Cotton-Barratt of the Future of Humanity Institute and the Global Priorities Project has written a series of essays on the cost-benefit prioritization of “problems of uncertain difficulty” -- that is, problems where the amount of resources needed to solve them might be anywhere between many orders of magnitude, with roughly equal probability. Should you spend resources on researching these hard problems today?
Well, it depends on how tractable the problem is (how far along we are towards solving it), how much benefit solving it would offer us, and how neglected the problem is (how much has already been invested into it.)
Our model for the benefit of immediate investment said that the benefit was of size kB/z. The three terms here line up pretty well with the components of the three factor model. The scale of the problem is expressed by B, the size of the benefit. The neglectedness gives us the term 1/z, the reciprocal of the amount of investment so far. And the remaining term, k, measures the tractability of the problem.
Cotton-Barrett has a quantitative argument for why the tractability of the problem shouldn’t matter much to our willingness to invest in it:
Are there any lessons to be drawn from this? One is that tractability may matter less than the other two factors. Under the box model discussed, we have k*= p/(ln(y/z)), where y is some level of resources such that we believe there is a probability p of success by the time y resources are invested. We might like to consider k= θk*, where θ is a factor to adjust for deviation from the box model. Then k itself decomposes into three factors: p, the likelihood of eventual success; 1/(ln(y/z)), which tracks time we may have to wait until success; and θ, which expresses something of whether we are currently in a range where success is at all plausible.
If the problem is something that we believe is likely to be outright impossible, like constructing a perpetual motion machine, then p will be very small and this will kill the tractability. If the problem is necessarily hard and not solvable soon, like sending people to other stars, then the box model will be badly wrong (or is best applied with our current position not even in the box), so θ can kill the tractability. But if it’s plausible that the problem is soluble, and it might be easy — even if might also be extremely hard — the remaining component of tractability is 1/(ln(y/z)). Because of the logarithm in this expression, it is hard for it to affect the final answer by more than an order of magnitude or so.
As an application of this model, the Global Priorities Project estimates that research into the neglected tropical diseases with the highest global DALY burden (diarrheal diseases) could be 6x more cost-effective, in terms of DALYs per dollar, than the 80,000 Hours recommended top charities.
They also estimate, using the same model, that medical research as a whole is being underinvested in. They estimate the cost-effectiveness of medical research as a whole at $8000/QALY -- worse than the best interventions for global poverty (at $50/QALY) but significantly more cost-effective than most health interventions funded by the NHS (going up to about $50,000/QALY).
Now let’s use that same model to look at aging research.
Cost-Benefit Estimates of Aging Research
The model Cotton-Barratt recommends for first-pass Fermi estimates is
Expected benefit = p B/(z log(y/z))
Where B is the benefit in the case of success, z is the current spending, and p/log(y/z) is the tractability, or the probability p of achieving the goal once we’ve spent a given multiple y of the current resource spend z.
How does this apply in the case of aging?
We imagine that a successful aging intervention will shift the DALY burden of age-related disease later, for concreteness let’s say by ten years starting at age 50.
So a 60-year-old will have the disease risk of a present-day 50-year-old, a 70-year-old will have the disease risk of a 60-year-old, and so on. If we denote by D_50 the expected DALY burden of age-related disease on a 50- to 60-year-old and N_50 the number of 50- to 60-year-olds in the world, the benefit of an aging intervention is:
B = N_60 (D_60-D_50) + N_70 (D_70-D_60) + N_80 (D_80-D_70) + N_90 (D_90- D_80).
The global DALY burdens for various age-related diseases at different ages, and the world populations at those ages, are available from public statistics, so we can make an estimate of the benefit in terms of DALY gain per year from a successful anti-aging intervention. (This does not even address the issue that anti-aging interventions will also extend life; so it's a conservative estimate.)
What is the current spending level?
We can divide research on age-related disease into general aging research and disease-specific research. If we consider only aging research, then aging research will appear more neglected, and thus more cost-effective; if we consider all age-related disease research (such as cancer research, Alzheimer’s research, etc) aging research will appear less neglected and less cost-effective. We’ll split the difference by treating the amount of aging research as
A + theta O
Where A is aging-specific research, O is research into other age-related disease, and theta is a weight between 0 and 1 to represent how much we think disease-specific research “counts.”
For the DALY burden of the diseases of aging we use the Global Burden of Disease 2016 statistics.
For estimates of the amount of aging spending we use the National Institute of Aging’s 2016 budget, the budgets of various EU research organizations, the R&D budget of Unity Biotechnology, and spending on “senescence” or “regenerative medicine” from the Pharma Cognitive database.
For estimates of the amount of age-related disease spending we use the National Institute of Health’s 2017 budget and the IFPMA’s estimates of 2017 pharma R&D spending.
For experts’ estimates of the tractability of aging spending, we use Aubrey De Grey’s predictions as an optimistic estimate, and the UK Longevity Panel’s predictions as a pessimistic estimate.
We have high uncertainty around all of these numbers, but especially of the amount of aging spending, since there’s no good way to estimate, to my knowledge, how much is being spent in pharmaceutical R&D on aging drugs, and no good data on the amount of aging research dollars spent by private organizations, some of which, like Calico, may be quite well-funded. What counts as “aging research” is also a somewhat subjective judgment; some aging research may not label itself as such, and some research labeled “aging” may actually be disease-specific research not relevant to the underlying biology of aging.
Our estimates of total current aging research spending are $1.8 billion-4.5 billion, and we estimate a log-linear distribution (the modal amount of spending is likely on the low end, close to the NIH’s aging budget, but there may be a long tail allowing for much higher spending, especially if private drug companies have more aging-related R&D than public databases estimate.)
Our rough estimate of total age-related disease spending is $104 billion, and we estimate a normal distribution.
Our estimate of tractability is uniformly distributed between 0.1 and 1, with mean 0.56; this follows the “uncertain chance of success” model in Cotton-Barratt’s calculations.
Our estimate of total benefit from delaying aging by 10 years is 176,800,000 DALYs saved yearly worldwide, plus or minus 30M DALYs, and we assume a normal distribution.
For theta=0 (only aging-specific research counts) the cost-effectiveness is about $42/DALY.
For theta=1 (all age-related disease R&D counts), the cost-effectiveness is about $1050/DALY, more effective than GPP’s estimates of medical research as a whole.
With a very rough and preliminary analysis, it looks like aging research could be comparable or superior in cost-effectiveness to the most cost-effective global health interventions.
GiveWell estimates a cost of $1965 for a gain of ~8 DALY-equivalents, or $437.50 per DALY, from giving malaria-preventing mosquito nets to children in developing countries. These estimates have changed quite a bit over time -- some older numbers from the research literature estimate $14-110 per DALY from mosquito nets.
This means the estimated cost-effectiveness of aging research (even with a conservative value of theta) is solidly competitive with even the best cost-effectiveness numbers for developing-world charities.
Of course, aging research is much more speculative than directly treating or preventing disease by known methods. If you want to buy a sure thing, research of any kind is not a great choice. Additionally, these back-of-the-envelope cost-effectiveness estimates are much more speculative themselves than the abundant empirical research on tropical disease prevention.
Another consideration is that aging is a much bigger problem, in total, than any specific disease. The total DALY burden of the diseases of aging is about 700 million DALYs, whereas the total DALY burden of malaria is about 50 million, or more than 10x smaller.
If you like high-risk, high-return, cost-effective lifesaving projects, then medical research in general may be a good buy, and aging research especially so, because the level of existing funding is so low, and the size of the impact of success is so high.
Gehem, Maarten, and Paula Sánchez Díaz. Shades of graying: research tackling the grand challenge of aging for Europe. The Hague Centre for Strategic Studies, 2013.
De Grey, Aubrey DNJ. "Life span extension research and public debate: societal considerations." Studies in Ethics, Law, and Technology 1.1 (2007).
You may find our research on the cost-effectiveness of researching and developing vaccines to be a useful point of comparison, if you have not seen it.
Thanks for including a model! I hope that future Forum posts with cost-effectiveness models do the same (some other posts have, but not all).
I'm confused about the "ten years" figure you chose. I didn't see it mentioned in the Longevity Panel's report, or in de Grey's (though I may have missed something). Why start with that number for the DALY estimation, rather than one year?
It didn't come from either, it came from me, as a benchmark for what seems conservatively possible to achieve in the near-term, and for the size of impact necessary to be plausibly cost-competitive with other causes like global poverty. (If the same amount of funding yielded only one year's delay in the DALY burden of age-related diseases, I think that would make global poverty likely to be a "better buy.")
What are 80,000 Hours' recommended top charities? I think you mean some other organization here.
The entire "magazine" seems to have gone offline. SAD!
Owen's last name is 'Cotton-Barratt'.
Just flagging that GiveWell's view about mosquito net DALYs has changed a lot:
Yes, I'm aware, and thanks for explicitly flagging that.
DALY estimates are obviously fraught, and I understand that they're not exact for any particular charity, but they seem seem relevant to back-of-the-envelope cost-benefit thinking about cause areas.
I don't think you can define aging research so narrowly and get the same expected impact. E.g. De Grey's SENS includes curing cancer as one of many subgoals, and radical advances in stem cell biology and genetic engineering, massive fields that don't fall under 'aging research.' The more dependent progress in an area is advances from outside that field, the less reliable this sort of projection will be.
This is a correct point.
However, I think it's worth noting that the most striking advance in aging research in recent years -- the discovery of senolytics -- came from biogerontologists, including those at the Buck Institute, which is dedicated to aging research. Nearly all studies on lifespan are conducted by researchers who specialize in aging. In that sense, I think it's fair to say that a good deal of aging research comes from specialized aging researchers.
Cancer research, I think, should not be considered aging research, because the vast majority of cancer therapies are not also aging-modifying therapies. If aging research pans out, of course, it will produce ways to prevent or treat cancer, but this will probably not depend very closely on the vast corpus of general cancer research.
Stem cell biology and genetic engineering seem to fall into a different category, as important inputs to aging research as well as to many other types of biomedical research. I don't know if EAs have a general framework for evaluating the cost-benefit tradeoffs of more "upstream" or "basic" or "tool" research compared to "downstream" or "translational" or "applied" research -- obviously the benefits of basic research can be much larger than the benefits of translational research, but the variance is also larger.
At any rate, my (non-quantitative, tentative) belief is that aging-focused translational research is more underfunded than research into multipurpose biological technologies (like genetic engineering or stem cell reprogramming), but this may be changing in the near future.
Hey, this is a great post! I'm really happy to see it, and it was a really nice and unexpected surprise.
I don't know if you have seen it, but I recently published the first post of a (will be) series in which I'm trying to build a framework for evaluating the cost-effectiveness of any given aging research/project: this one.
In your model you only account for DALYs prevented for measuring impact, while I would like to account for many more things: all the considerations arising from the concept of Longevity Escape Velocity (e.g. bringing its date closer by one year could save roughly 36,500,000 lives of 1000QALYs each, using a conservative estimate), DALYs prevented, the economic and societal benefits of increased healthspan (the longevity dividend), the value of information.
I would also like to explore moral considerations that could potentially influence impact, such as if age discounting has to be applied and how population ethics influence the estimates, since at a first glance an impersonal view seems to imply that a sharp downward correction is necessary (although upon further analysis it turns out that this is not the case).
Another difference is that I'm trying to build the tools for evaluating specific interventions inside this cause area, and not strictly the cause area as a whole. I'm taking this approach since I believe there are some interventions that would be very ineffective to fund and others that would be extraordinarily cost-effective.
One implication of this is how I will measure tractability and neglectedness: to estimate neglectedness I will probably use the arguments OpenPhilanthropy's made on the topic but with an important addition: it would be informational to list the organisations working on facets of aging that are the least further along in the pipeline that goes from in vitro research to clinical application. We can probably start from the lifespan.io's Rejuvenation Roadmap to build a list of this kind. For evaluating tractability there will be probably some scientific arguments to make.
At the end I will also analyse specific non-profits and interview some people.
In case you want to take a glance on what I'm currently writing, I gave you access to my current drafts (which are not polished at all, but may give you an idea of how I'm proceeding): this, this and this.
P.s: Nine months ago I also made this estimate of the expected cost per life saved of the TAME trial. It's not great, but it may be of interest. It was made before I begun thinking about the framework.
Edit: Are you planning on doing other cost-effectiveness estimates on this topic? Should we unite forces?
I might do more cost-effectiveness estimates, but it's not a top priority -- I'm currently running the Longevity Research Institute, a nonprofit devoted to experimentally testing anti-aging interventions, and I have a lot of object-level work to do there. Definitely happy to consult, make intros, and share my own existing notes whenever you have questions.
Yes, my estimates are a large underestimate of the potential benefit of life-extending therapies if you assume that they extend life at all, rather than just delay the onset of disease-related disability. I wanted to indicate that the impact is large even with rather pessimistic assumptions.
The main question as I see: is current spending of 1 billion-a-year on aging enough to delay aging for 10 years? Aging is a problem of (hyper)exponentially increasing complexity with time. There are probably a few interventions which could give 1-3 years of expected life extension (and aging delay): metformin, vitamin D and green tea, and proper testing of them could cost as few as tens millions of dollars as in proposed TAME study of metformin. This (+chance to survive for other life extending technologies) means much higher cost-effectiveness of such small experiments, as I described in the post. There are several other ways to donate more cost-effectively than directly funding aging research, like lobbying WHO that aging is a disease.
On the other hand, as aging is so quickly grows in time, adding up with small interventions will not give us 10 years delay of aging. So when we speak about 10 years aging delay, costs become much higher, as there is no more low-hanging fruits.
I read an opinion that current aging research may benefit of 10 times increase in spending. But it is still not clear, how much should be spent in this mode to find "a cure for aging". I guestimate that at least a trillion dollars for 10 ten years delay of aging - above the level which we could get via simple (but undertested) interventions, which is 3-5 years.
Now, spending a trillion dollars will give 10 billion people 10 years QALY each, which is only 10 dollars for QALY (assuming that we should not count the price of therapy, as people will pay themselves, and they only need an opportunity for life extension, but not constrained in health spendings).
I believe there are larger effect sizes out there than metformin; metformin has a relatively small effect size on mice compared to other lifespan-modifying interventions, and the TAME trial chose metformin (as Barzilai admits) because it's extremely safe and well-studied, not because it's expected to be the best.
I agree with you; I don't think aging research would be cost-effective at a trillion dollars of total funding. I expect that's hugely more money than necessary.
Surely, there are lager effect sizes there, but they need much more testing to prove the safety and such testing is the most expensive part of any trials. There is a few already safe intervention which could help to extend life, that is, besides metformin, green tee and vitamin D.
Even as a trillion dollar project, fighting aging could be still cost-effective, after we divide the benefit for 10 billion people.
If we speaking on de novo therapies, current price of just one drug development is close to 10 billions, and comprehensive aging therapy like SENS should include many new interventions, so it may be reasonable to estimate that it will be equal to 100 new interventions, and thus trillion dollar price is real. The sum is large but affordable for humanity as whole: total space funding for all history is around this price.
However, it is impossible to get such trillion dollar funding via donations. But EA efforts could be used to attract larger funders, like pension funds, farma, governments, billionaires and insurance companies for funding such projects as they will eventually benefit from the cure for aging.