This is the fourth post of a series in which I'm trying to build a framework to evaluate aging research. Previous posts:
1. A general framework for evaluating aging research. Part 1: reasoning with Longevity Escape Velocity
2. Aging research and population ethics
3. Impact of aging research besides LEV
In the first section, I propose a method to scout for impactful and neglected aging research. This method is comprised of two steps: Identifying what is necessary to achieve LEV and, among what is necessary, identifying what is most neglected. This differs from the Open Philanthropy Project's approach of ignoring impact derived from Longevity Escape Velocity. A preliminary evaluation, made through including all research on the hallmarks and using lifespan.io's Rejuvenation Roadmap to identify neglected projects, leads us to identify genomic instability, telomere attrition, epigenetic alterations, deregulated nutrient sensing, loss of proteostasis, and mitochondrial dysfunction as neglected and important areas of research. Other neglected research must be scouted in other equally important areas that have already been identified by Open Philanthropy, such as improving delivery methods and developing better biomarkers.
In the second section, I take Open Philanthropy's and Aubrey de Grey's stance about considering interventions targeting "aging in general", such as caloric restriction or metformin, as having low tractability and impact. What remains after this first skimming is translational research focusing on the hallmarks, basic non-translational research, and enabling research, such as developing new tools and delivery methods. When prioritizing inside these areas, tractability should be considered only after having first considered neglectedness while trying to maximize scope by looking at research that is necessary for reaching LEV. Otherwise, a relatively small gain in tractability would sacrifice an extreme amount of impact and neglectedness. This is true because the hardest problems in the field are often the most neglected, but if they are necessary for achieving LEV, they will be solved later, and by accelerating them, we can impact the expected date of LEV the most.
A method for evaluating neglectedness
In its medium investigation on the cause area of aging, the Open Philanthropy Project identified some scientific advances that it believes would provide years of healthy life extension but still within the range of natural lifespans:
- Preventing the accumulation of epigenetic errors associated with aging or restoring more youthful epigenetic states in cells.
- Solving the problem of senescent cell accumulation.
- Reversing stem cell exhaustion.
- Learning how to use induced pluripotent stem cells (IPSCs) to regenerate and/or replace tissues and organs damaged by aging and aging-related diseases.
It has also identified research avenues useful for the attainment of the goals stated above:
Common obstacles to achieving the goals stated above include lack of ability to selectively deliver agents to desired cell types, measure and control the epigenetic state of cells, and understand and control differentiation and functioning of stem cells (plausibly closely related to the previous item). Therefore, progress on these more general themes may assist with extending healthy lifespan. Other types of relatively general research may also be helpful or necessary for substantial extension of healthy lifespan, such as general progress in neuroscience, improved biomarkers for various aspects of aging, and/or improved model organisms for aging.
By exploring funding and projects in this cause area, it also found two specific neglected interventions:
We have a limited sense of the absolute and relative neglectedness of the various categories of research discussed in this report. However, our scientific advisors identified specific unfunded projects related to the following themes:
- Understanding the mechanism(s) driving regeneration associated with heterochronic parabiosis: Experiments have indicated that the blood of older animals can have deleterious effects on younger ones, and that the blood and organ functioning of younger animals can improve the functioning of old ones, though to date the hypothetical increase in healthy lifespan has not been tested. Understanding the biology responsible for the observed effects might eventually lead to interventions that address health problems associated with aging.
- Aging and epigenetics: Documenting correlations between tissue-specific epigenetic states and signs of aging with a longitudinal cohort study and/or systematic examination of cadavers of people dying at various ages could yield valuable information that could lead to treatments to address aging-related health issues.
Open Philanthropy's way of proceeding is a fruitful one: identifying general impactful avenues and then searching for specific unfunded and underfunded projects.
If impact is measured in DALYs saved at the end of life, or mild life extension, then this method of proceeding could be optimal. Nonetheless, I propose another method that makes more sense in light of the measure of impact that I propose in the first post of this series: QALYs saved by making Longevity Escape Velocity come closer.
Open Philanthropy dismisses the possibility of radical life extension in the next decades, but the timeline in which radical life extension will happen doesn't impact the measure of impact that I propose. More importantly, the organization expresses doubts about the desirability of indefinite life extension and its relevance for cost-effectiveness analyses:
We think the best case for this cause involves the prospect of healthy life extension within the range that some humans currently live.
Our default view is that death and impairment from “normal aging” are undesirable. However, we would have some concerns about indefinite life extension, mainly related to entrenchment of power and culture. We don’t have internal consensus on whether, and to what extent, such indefinite life extension would be desirable, and don’t consider it highly relevant to this write-up.
Unlike Open Philanthropy, I think that the majority of the impact of aging research comes from making the date of LEV come closer and from the considerations about LEV in general explained in my first post. The reasons for this should be clear by reading the first and third posts, which are respectively about the impact coming from LEV and the impact coming from preventing DALYs due to age-related diseases.
Regarding Open Philanthropy's concerns about the desirability of "indefinite" life extension: Potential "entrenchment of power and culture" is a negligible inconvenience if compared to the 36,500,000,000 QALYs saved by making LEV come closer by just one year. These figures come up by estimating the length of a life after LEV at 1000 years, although the possibility of it being "indefinite" is undeniable. I think that it's also not clear if Open Philanthropy's concern would be a new problem at all, given that power, in the form of wealth or not, can already be passed from generation to generation. This concern is also offset by considerations about accumulation of knowledge that would be useful for science and other positive sides of eliminating aging discussed in my previous posts. It could also turn out to be irrelevant due to other disrupting technologies coming along before and after LEV is attained.
In principle, ignoring a source of impact is going to produce wrong results, since optimizing for one also influences the others.
Keeping in mind the metric of "QALYs saved by making LEV come closer", what is a better method of evaluating neglected avenues? Here is the strategy I propose:
- Identify what is necessary to achieve LEV.
- Among what is necessary, identify what is most neglected.
This method would cause the most difficult problems, which would be solved last if we didn't inject more funding, to be solved sooner. In this way, we would probably impact the date of LEV the most. Unlike the strategy proposed by Open Philanthropy, here, the focus is on LEV, and this generates different answers.
How do we implement the two steps above? Knowledge of the field is necessary. In a preliminary way, we could consider the general avenues identified by Open Philanthropy as necessary advancements. On their own, they are certainly incomplete, and we may actually want to include each one of the hallmarks of aging as described in the namesake paper. The causality and interference that the hallmarks have on each other is not yet completely understood, but many of them seem to be individually important enough to require a distinct solution in order to achieve LEV, if not multiple distinct solutions per hallmark.
Among the hallmarks identified, how do we identify the most neglected? We could look at unfunded projects, as Open Philanthropy has done, or we could search the literature by keywords and look at which hallmark has less research going on about it. An initial good source for identifying the most neglected is also the Rejuvenation Roadmap, which is curated by the Life Extension Advocacy Foundation. The most neglected should be the hallmarks in the least advanced stages of research. In theory, this could tell us that they are just difficult instead of neglected, but most of the time, these two things go hand in hand. By looking at it, we immediately identify that two out of four of the general impactful areas identified by Open Philanthropy (cellular senescence and stem cell exhaustion) are actually in the most advanced stages of research. This shouldn't be a surprise, since they are, right now, the most fashionable and well funded in the field. Stem cells are probably the most researched topic among the things in the roadmap, and research on senescent cells has exploded in recent years, having seen a surge in private investment on the order of hundreds of millions of dollars (most notably Unity Biotechnology).
As mentioned, the most neglected problems seem to be the most difficult. This is usually true, because they are too risky to pursue for publicly funded research and too early stage for private investment. However, since they will be the ones that will be solved later in time, they are the ones that will constitute the last barriers for achieving LEV. Therefore, if accelerated, they will actually bring LEV closer in time.
If we look at the Rejuvenation Roadmap, we can identify these as the most neglected areas: Genomic Instability, Telomere Attrition, Epigenetic Alteration (rightly identified by Open Philanthropy), Deregulated Nutrient Sensing, Loss of Proteostasis, and Mitochondrial Dysfunction.
But how to evaluate the most neglected topics not described in The Hallmarks of Aging, such as improving delivery methods or developing better biomarkers? Open Philanthropy rightly identified these as important topics, and they are probably necessary for reaching LEV, especially considering that generic therapies that, together, would plausibly address almost every hallmark involve somatic gene therapies that are currently unavailable. In this case, the strategy of looking for important unfunded projects, coupled with a similar approach as the one we use for the hallmarks (searching how many papers there are about each single topic) could be a good strategy. Again, expertise in this field is needed.
What is more tractable in aging research, and why tractability starts to lose value after a certain point
There seems to be one key consideration about tractability in aging research: addressing aging in general is much more difficult than adopting a divide et impera approach. Quoting Open Philanthropy's piece:
While it is conceivable that there could be treatments addressing aging “in general” (e.g., addressing all or a large proportion of associated symptoms via a single mechanism), such treatments have not been conclusively demonstrated and may not be possible. There are approaches that have been hypothesized to fit in this category, such as caloric restriction. While some of these have been tested in model systems, they have not been tested in humans for the purpose of extending healthy lifespan, and we would guess that they would not have radical effects on healthy lifespan if they were tested (but plausibly could be substantially positive).
Such interventions target basic mechanisms of aging that are the cause of the damages of aging. Similar approaches are drugs that mimic caloric restriction, or that seem to affect multiple metabolic pathways related to aging, such as the drug metformin. These kind of drugs have small effect sizes, and they delay the onset of age-related diseases. They are difficult to understand due to the intricacy of metabolic pathways and the many unknowns about metabolism in general. Addressing aging by "tinkering" with metabolism is currently not a tractable avenue. In fact, Open Philanthropy focuses on research avenues outside of this area. This is also the argument that biogerontologist Aubrey de Grey makes in favour of the "maintenance approach" to aging: addressing its basic damages (hallmarks) using periodic maintenance, such as by addressing stem cell exhaustion, using senolytics to get rid of senescent cells, etc. instead of focusing on the pathways that originally led to them (the seven damages of his SENS approach are very similar to the nine described in The Hallmarks of Aging). The maintenance approach also theoretically provides rejuvenation - removal of damage - instead of just slowing down its accumulation.
Starting from this common ground, we can focus on what remains:
- Translational research focusing on the hallmarks.
- Basic non-translational research.
- Enabling research, such as developing new tools and delivery methods, even if it isn't strictly classified as aging research.
What is more tractable inside these three categories? This depends on the specific project evaluated. Trying to locate sub-subareas of tractability in advance is probably not that useful.
However, should we really be focusing on tractability beyond the first skimming? I believe that now these two metrics should have priority:
- Neglectedness, which correlates with hardness.
- How necessary the given research is for LEV, which drives impact.
Tractability should be considered after picking the most neglected and necessary projects. Here's why:
As observed earlier, in this area, neglectedness and tractability seem to correlate negatively with each other. This could have a few reasons: the more difficult a given research project is, the riskier it becomes and its results will be particularly far in the future. If a project is too risky and too slow, it will not attract public or private funding and will not be generally attractive to researchers. This is usually the case for hard and ambitious basic research, which is too risky for public funding and too early stage to be profitable for a company. This creates a landscape in which harder problems are neglected. The only way to finance this kind of harder and long term research seems to be through philanthropy.
Keeping in mind the metric of impact of "making LEV come closer", it makes more sense to finance hard and neglected problems if they are necessary for achieving LEV. These kind of problems will be solved later than others, therefore accelerating their solution has the most impact on LEV's expected date, which is the largest source of impact of aging research by far.
Because of the nature of the field, if we focused more on tractability, we would have little gain of it (visually, we would add some of it on top of the one gained by the skimming already performed), and, in turn, we would avert some more short-term DALYs. However, by making this choice, we would lose an extreme amount of impact, and we would make a big sacrifice in neglectedness, rendering the tradeoff not worth it.
In this area, we will rarely see neglected problems that are also very tractable, and while hunting for giving opportunities, we should be on the lookout for projects that are very hard, risky, long term, and underfunded but, at the same time, necessary. By going against the sub-optimal common practice caused by the risk-averse mindset of the field, we can optimize research.
Crossposted to LessWrong.
It seems to me that the inverse can be argued - some other altruistic influences that increase the life expectancy of people, regardless of mortality from aging, increase the cost-effectiveness of working on arriving LEV, and possibly significantly (for example, if I reduce the risks of young people dying not associated with diseases in two times, I increase their life expectancy, most likely by less than a year, but if we have already reached LEV, then I will increase it by about 1000 years).
The first results achieved, which strongly affect DALY, can become a proof of concept and greatly increase funding for other projects - this is one of the key factors to consider. You mentioned this in other posts, I do not know why not in this. In addition, tractability also includes the probability that in this way the problem will not be solved in principle, which means that there may be other more promising methods. Although, of course, if we restrict ourselves to considering only one strategy in which all elements are necessary to achieve a result, it is irrelevant.
But you note very little on such aspects of the possible impact on LEV achievements as the development of artificial intelligence or human intelligence improving technologies, lobbying for laws and popularization, transplantology, nanotechnology, neurobiology, cryonics, futurology and sociology, which can give the best understanding of the reasons for avoiding the fight against death and making better plans for it (taking into account systematic causes that affect scientific and technological progress effectiveness, for example). If you consider all these possibilities, then the technology proposed by Aubrey de Gray will not be the only option to arriving LEV.
Some of these areas, such as futurology, the development of safe AI and human intelligence improving technologies, can be especially attractive, as they positively affect both the achievement of LEV and existential risks.
In your next post, you wrote that aging research may be second or third after X-risk.
But, it seems to me, a comparison of the fight against aging with existential risks such as artificial intelligence is not entirely obvious (although it is most likely true that AI alignment more important in altruistic view). Effective altruists do not yet have an established way to translate existential risks into QALY, so they evaluate them separately. While this is most likely possible and important to do.
Personal-affecting and impersonal views will differ greatly in evaluating the importance of existential risk by QALY, since in the first case we lose only the entire population of humanity, and in the second, all possible people of the future, which could exist many in the Universe. On the other hand, the question is also not limited to this, because for somebody existence of people and consciousness in the Universe may be valuable, but not the value of maximizing the number of these people. And this value will need to be somehow separately evaluated.
In addition, in the case of an impersonal view, one must look at the expected number of people saved when the existential risks change by some amount that will be equal to the difference between the expected values with a new doom probability and an old one. Since the risk will never become zero can't exist influence which value will be equal to all QALYs that are could placed in the remaining time in the Universe.
It would be interesting to solve this problem, but even without taking this into account, I would like aging to be placed in the list.
Nice post! Agreed that hard problems (or at least those that are likely to take more than the usual academic funding cycle to produce results) are likely to be relatively neglected.
It would also be good to consider that interdisciplinary research tends to be hard to fund but often produces outsized results (tool development for basic biology often falls into this category). So some of the hard problems could be more tractable to an interdisciplinary group, but getting funding for one is often impractical. I don't know enough about the priority areas you identify as neglected and important to know which might benefit from an such approach, but specifically allocating some funding for interdisciplinary work could might produce good results in these areas.