This is a writeup of a medium investigation , a relatively brief look at an area that we use to decide how to prioritize further research.

In a nutshell What is the problem? Aging is a major contributor to cardiovascular disease, cancer, diabetes, neurodegenerative diseases, and other causes of death and impairment. Better understanding, and being able to mitigate, the basic mechanisms of aging could therefore contribute to reduced age-related mortality and impairment for a very large number of people. How could the problem eventually be solved or substantially alleviated? We think it’s plausible that age-related diseases and impairments could be alleviated if scientists achieved specific research objectives in a number of areas (prevention/correction of epigenetic errors, senescent cell removal/prevention/reprogramming, reversing/addressing stem cell exhaustion, and organ/tissue regeneration and replacement). This list is not exhaustive and is populated with areas that seem to us to be especially fundamental and/or dynamic and potentially broadly applicable, and therefore seem like plausibly useful areas for subsequent research. We are highly uncertain how large the potential gains might be if the above objectives were achieved, but think several years of healthy life extension (and possibly more) could plausibly be made in the next 10-20 years in some areas (such as senescent cell removal), while areas that could yield substantially greater gains will likely require multiple decades of progress in enabling areas like neuroscience, selective delivery of agents to cells and/or organelles, and epigenetics. However, we don’t have a strong opinion about whether supporting the nearer-term or longer-term objectives is likely to have greater expected benefits per unit cost. Who else is working on it? The NIH reports spending $2.7 billion per year on aging-related research. We are unsure how much of this is relevant to understanding, preventing, and mitigating the basic mechanisms of aging. We are aware of several foundations and nonprofits focused on aging research with collective expenditure around $80 million per year (likely an underestimate of philanthropy in the area). During this investigation, we became aware of several companies explicitly focused on aging with about $1 billion in investment collectively. Open questions include: which themes are neglected; what levels of healthy life extension might be realized if the different research goals are accomplished; and which long-term research directions are most promising and neglected. Table of Contents Our process What is the problem? What currently available interventions can address this problem? How could the problem be substantially alleviated? What are the possible research interventions? Indefinite vs. moderate healthy life extension Who else is working on it? Questions for further investigation Sources



Published: September 2017

Our process

Our scientific advisors, Chris Somerville and Heather Youngs, are biochemists and scientific generalists with no prior expertise in aging research. We asked them to survey the field of aging, divide it into subfields, identify promising projects that were not being pursued, and help us understand the potential impact on healthy lifespan if various potential long-term research projects were successful. The latter question was not discussed in the literature, and we had to approach it very speculatively. We excluded investigation of science mainly relevant only to one specific age-related disease (e.g. research on cancer, cardiovascular disease, and Alzheimer’s) but included some topics relevant to many age-related diseases (e.g. developing the ability to grow organs from induced pluripotent stem cells).

Our advisors conducted literature reviews, spoke with several people in the field, and wrote rough internal memos for other staff to review. This was their main priority for roughly one and a half months.

Nick Beckstead drafted this page and it was reviewed by our scientific advisors and a few other Open Philanthropy Project staff before it was published.

What is the problem?

Aging is a major contributor to cardiovascular disease, cancer, diabetes, neurodegenerative diseases, and other causes of death and impairment (some of which, such as muscular atrophy, loss of teeth, and damage to joints, are so common that they are not generally considered “diseases”). Proposed basic mechanisms are various and have disputed levels of comparative importance, but include “genomic instability, telomere attrition, epigenetic alterations, loss of proteostasis, deregulated nutrient sensing, mitochondrial dysfunction, cellular senescence, stem cell exhaustion, and altered intercellular communication.” Additional potential mechanisms are presented below.

What currently available interventions can address this problem?

There are a large number of symptoms associated with aging. Some are widely recognized as diseases and are subject to a variety of treatments (e.g., neurodegenerative disorders; heart disease); others are not considered “diseases,” and there are generally few if any treatments targeting them (e.g., normal muscular atrophy). 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). We did not carefully consider nutrition and lifestyle interventions (except for caloric restriction) because we have a strong prior that available data is inconclusive and our science team’s expertise is more in the direction of molecular biology and biochemistry than nutrition.

How could the problem be substantially alleviated?

This section focuses on imagining, very speculatively, how scientific advances could eventually make it possible to prevent or substantially alleviate some problems associated with aging. Claims not cited are generally based on the internal memos produced by, and subsequent conversations with, our advisors (along the lines of the process described above).

This list highlights some imaginable scientific advances that attracted the interest of our scientific advisors because of their potential to extend healthy lifespan. The first three attracted the interest of our scientific advisors because they appear to address “basic mechanisms” of aging that might account for a large proportion of aging-related symptoms, whereas the last is less basic in this sense but seems especially dynamic and potentially broadly significant. The list is not exhaustive. With those caveats and clarifications in mind, we would guess that healthy lifespan might be extended if scientists eventually were able to:

Prevent the accumulation of epigenetic errors associated with aging, or restore more youthful epigenetic states in cells. Various alterations of epigenetic state are correlated with both chronological age and symptoms of aging, and there are theoretical reasons to expect that these alterations would cause symptoms of aging. Interventions on the epigenetic state of mice have shown results consistent with the points previously stated but we anticipate that multiple aspects of inducing “epigenetic rejuvenation” would be challenging.

Various alterations of epigenetic state are correlated with both chronological age and symptoms of aging, and there are theoretical reasons to expect that these alterations would cause symptoms of aging. Interventions on the epigenetic state of mice have shown results consistent with the points previously stated but we anticipate that multiple aspects of inducing “epigenetic rejuvenation” would be challenging. Solve the problem of senescent cell accumulation. As animals age, senescent cells (i.e., cells which neither grow and divide nor apoptose) accumulate. Research suggests that senescent cells contribute to damaging inflammation and may also suppress tissue regeneration by stem cells. In lab experiments, mice who had a portion of their senescent cells removed lived about 25% longer than mice in the control group that were born at the same time. We imagine that selectively killing senescent cells might become possible through a number of generic strategies. We have a less specific sense of how reprogramming senescent cells or preventing them from becoming senescent in the first place might work, but imagine that advances related to epigenetics (discussed above) or advances related to several of the other directions discussed in this document could be helpful. We mean to raise the above generic strategies only as plausible possibilities and do not have confidence in the feasibility or timeline for success of particular approaches.

As animals age, senescent cells (i.e., cells which neither grow and divide nor apoptose) accumulate. Research suggests that senescent cells contribute to damaging inflammation and may also suppress tissue regeneration by stem cells. In lab experiments, mice who had a portion of their senescent cells removed lived about 25% longer than mice in the control group that were born at the same time. We imagine that selectively killing senescent cells might become possible through a number of generic strategies. We have a less specific sense of how reprogramming senescent cells or preventing them from becoming senescent in the first place might work, but imagine that advances related to epigenetics (discussed above) or advances related to several of the other directions discussed in this document could be helpful. We mean to raise the above generic strategies only as plausible possibilities and do not have confidence in the feasibility or timeline for success of particular approaches. Reverse stem cell exhaustion. Somatic stem cells are induced by factors such as growth, normal senescence, and tissue damage to divide and replenish other cells. As adult humans age, their stem cells appear to become depleted or increasingly less active, which is thought to decrease the body’s capacity to replace and repair damaged tissue. It’s unclear how much of what we call aging is attributable to decreased stem cell activity, and what causes the apparent decrease in stem cell activity, but numerous factors have been implicated. Additionally, as noted above, cytokines released by senescent cells may play a role. We see a few (speculative) possibilities for addressing stem cell exhaustion, and we discuss three of them in a footnote.

Somatic stem cells are induced by factors such as growth, normal senescence, and tissue damage to divide and replenish other cells. As adult humans age, their stem cells appear to become depleted or increasingly less active, which is thought to decrease the body’s capacity to replace and repair damaged tissue. It’s unclear how much of what we call aging is attributable to decreased stem cell activity, and what causes the apparent decrease in stem cell activity, but numerous factors have been implicated. Additionally, as noted above, cytokines released by senescent cells may play a role. We see a few (speculative) possibilities for addressing stem cell exhaustion, and we discuss three of them in a footnote. Learn how to use induced pluripotent stem cells (IPSCs) to regenerate and/or replace tissues and organs damaged by aging and aging-related diseases Progress in getting IPSCs to differentiate into other cell types and organoids may allow repair or replacement of organs such as liver, pancreas (islet cells), lungs, kidneys, spinal cords, eye, and heart, and also some cell types in the brain, and could contribute to management of aging-related diseases affecting these cells/tissues/organs/organoids, including heart disease, diabetes, liver disease, vision loss, ALS, and Huntington’s disease.

We are highly uncertain about, and do not have internal consensus regarding, the potential extension in healthy lifespan that might result if 1-2 of the above objectives were accomplished. Some of us see several years of healthy life extension as the plausible potential upside and others see larger possible gains, but all of us involved in creating this report expect that any increase in healthy lifespan would keep average lifespan within the range of natural lifespans observed in humans today (barring a historically exceptional increase in the rate of scientific progress). We would guess that much more radical life extension would likely require a larger number of successes like these and likely multiple successes that are not listed here, and we accordingly assign it much lower probability in the next few decades (with some caveats). We held this view about the difficulty of radical life extension prior to this investigation. Our findings fit with this prior view, and the investigation did not strongly affect our views on the matter.

Some other themes are also potentially important to aging, but they are covered in this write-up in less detail because we have focused on topics that seemed more basic, dynamic, and/or potentially broadly significant to us. The themes covered in less detail here include: genomic instability, telomere attrition, loss of proteostasis, deregulated nutrient sensing, mitochondrial dysfunction, altered intercellular communication, decline of the immune system, inflammation, neurodegeneration, the microbiome, and damage to individual cells (e.g. antioxidants and DNA repair). We may investigate inflammation and decline of the immune system more thoroughly in the future because these topics caught the interest of our scientific advisors. We compare our list of highlighted topics with a plan proposed by researchers at the SENS Foundation in a footnote.

What are the possible research interventions?

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.

We think substantial progress on many of the themes mentioned above is likely to require decades of work, so our intuition is that long-term, basic research (with an emphasis on tool development) in areas like neuroscience, selective delivery of agents to cells and/or organelles, and epigenetics is likely to be the most important work for making the greatest possible progress relevant to age-related disease and impairment in the long run (though we have a limited sense of which tools and research directions are likely to be most promising and/or neglected). Our reasoning for thinking this work will be more important in the long run can be made clearer by reference to a thought experiment: imagine that 30 years ago, a funder were working toward understanding and mitigating the fundamental causes of aging. Our intuition is that they would want a large share of their effort to go toward supporting very basic work on gene sequencing, microscopy, the areas of cell biology that have led to the field of epigenetics, and topics in cell differentiation that led to the discovery of stem cells - rather than work that might fall under the auspices of “aging research” per se. We suspect something similar is still true today. One observation we can offer in support of this is that many of the important questions relevant to extending lifespan could not even have been asked 30 years ago (e.g. some questions about stem cells and epigenetics).

Some of the themes listed above do not seem to have as many basic obstacles as others. For example, it seems plausible to us that some of the above objectives related to senescent cell removal and heterochronic parabiosis could be achieved in the next couple of decades. In these cases, we don’t have a strong opinion about whether supporting research primarily relevant to these objectives or long-term objectives is likely to have greater expected benefits per unit cost.

Indefinite vs. moderate healthy life extension

We think the best case for this cause involves the prospect of healthy life extension within the range that some humans currently live. In contrast, some people who are interested in the mechanisms of aging have promoted the idea of “curing” aging entirely. Some thoughts on this:

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.

We don’t see promising life science research that would result in indefinite life extension in the next few decades, barring a historically exceptional increase in the rate of scientific progress.

When we consider possible transformative technologies that could result in indefinite healthy lifespan, some staff members think some kind of identity-preserving digital emulation is more likely than radical scientific advancements related to physiological aging, but others are more skeptical about the relevance/feasibility of that idea.

Our program officer Nick Beckstead offers the following forecast to make the above more precise/accountable: By January 1, 2067, there will be no collection of medical interventions for adults that are healthy apart from normal aging, which, according to conventional wisdom in the medical community, have been shown to increase the average lifespan of such adults by at least 25 years (compared with not taking the interventions). (Subjective probability: ≥93%)

The prediction is called off if some other innovations cause a historically exceptional increase in the rate of scientific progress during this period (such as the development of transformative AI capabilities). The prediction excludes diet, exercise, and lifestyle, as well as existing medical interventions for healthy people (such as currently available vaccines).

Who else is working on it?

The NIH reports spending $2.7 billion per year on aging research in 2015. In the 2015 budget request, $510 million per year is tagged as “neuroscience” and $177 million per year is tagged as “aging biology.” We have heard in various conversations that this research is mainly relevant to addressing particular symptoms associated with widely-recognized diseases (e.g., Alzheimer’s disease), rather than on understanding the basic mechanisms that cause aging. This is plausible to us, but we haven’t seen any convincing evidence for it and we do not take it for granted. We sometimes hear the sentiment that research on aging is neglected because of an attitude that “curing” it isn’t desirable, but we haven’t seen any evidence that the NIH takes that attitude.

A brief Google search revealed the following non-profit organizations working in the space, with all funding totals reflecting amounts dedicated to aging-related research: the Buck Institute ($35 million total annual budget in 2014); the Glenn Foundation ($11 million total in grants in 2014); the SENS Foundation ($1.5 million in grants and $5 million in total expenses in 2014); the American Federation for Aging Research ($7.7 million in grants and $10 million in total expenses in 2015); the Larry L. Hillblom Foundation ($6 million in grants and $6.8 million in total expenses in 2015). The Ellison Foundation is leaving the field.

Some aging-focused companies working in this area that we became aware of in the course of this investigation include Calico ($500 million in disclosed investment and agreed upon potential for $1B more); Human Longevity, Incorporated ($300 million in investment); Unity Biotechnology ($119 million in investment, currently focused on senescent cell removal); Alkahest ($53.5 million in investment, focused on neurodegeneration and interventions related to heterochronic parabiosis); and Ambrosia (investment figures not readily available online).

Another overview of funding in this area, made in 2015, is available here. Our survey of funders, non-profits, and companies in this area is incomplete and is somewhat skewed toward research topics highlighted in this write-up. We have a limited understanding of the pharmaceutical industry’s spending on research and development related to aging.

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.

Questions for further investigation

How neglected are the various themes discussed in this document (e.g. “epigenetics and aging,” “senescent cells,” etc.)? What are the most promising unfunded projects related to these themes?

What is the comparative potential upside of accomplishing the core objectives related to these various themes for extending healthspan?

With what probability and on what timescale could such successes be achieved?

How likely is it that general-application tools and basic research areas that might not be thought of as part of “aging research” (analogous to epigenetics, stem cells, neuroscience, and drug delivery) will be bottlenecks to accomplishing the core objectives described above? What tools and/or research directions under these headings are most neglected relative to their promise, for the purpose of addressing these bottlenecks? What other general-application tools and basic research areas might be important for accomplishing these core objectives? Would interventions focused on these more basic/general themes have greater or smaller effects on the time by which such objectives might be achieved?

What research programs could help scientists discover all aspects of the epigenetic state of cells and make it possible to measure and intervene on those aspects of cells? To what extent are the most important research programs of this nature being pursued already?

How likely is it that advances in drug delivery (including delivery of other agents to cells) would be required for effective senescent cell removal or interventions to correct or prevent the accumulation of epigenetic errors? If such advances are needed, what are these advances? What research programs could lead to these advances? To what extent are the most important research programs of this nature being pursued already?

What are the most important mechanisms of aging that were not investigated in this write-up?

To what extent are the hallmarks of aging traceable to a few basic mechanisms, vs. a large number of distinct mechanisms that could not plausibly be addressed together except by many separate interventions?

Sources