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.
Dr. Owen Cotton-Barrett 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 estimated 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).
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 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 estimate for aging research 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 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).