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.


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.1

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”).2 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.”3 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 state4 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.5 Interventions on the epigenetic state of mice have shown results consistent with the points previously stated6 but we anticipate that multiple aspects of inducing “epigenetic rejuvenation” would be challenging.7
  • 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.8 We imagine that selectively killing senescent cells might become possible through a number of generic strategies.9 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.10 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.11 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.12

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.13

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.14

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 2015.15 In the 2015 budget request, $510 million per year is tagged as “neuroscience” and $177 million per year is tagged as “aging biology.”16 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);17 the Glenn Foundation ($11 million total in grants in 2014);18 the SENS Foundation ($1.5 million in grants and $5 million in total expenses in 2014);19 the American Federation for Aging Research ($7.7 million in grants and $10 million in total expenses in 2015);20 the Larry L. Hillblom Foundation ($6 million in grants and $6.8 million in total expenses in 2015).21 The Ellison Foundation is leaving the field.22

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);23 Human Longevity, Incorporated ($300 million in investment);24 Unity Biotechnology ($119 million in investment, currently focused on senescent cell removal);25 Alkahest ($53.5 million in investment, focused on neurodegeneration and interventions related to heterochronic parabiosis);26 and Ambrosia (investment figures not readily available online).27

Another overview of funding in this area, made in 2015, is available here.28 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.29 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

Document Source
AFAR 990 for 2015 Source
Alkahest, About page Source
Ambrosia website Source
American Diabetes Association, Type 1 Diabetes Source
Baker et al. 2016 Source
Buck Institute 990 for 2014 Source
Calico Press Release 2014 Source
Chen et al. 2016 Source
Conboy et al. 2005 Source
Cosgrove et al. 2014 Source
Crunchbase, Human Longevity Source
Crunchbase, Unity Biotechnology Source
Farr 2013 Source
Friedman and Friedman 2002 Source
Glenn Foundation 990 for 2014 Source
Horvath 2013 Source
Horvath et al. 2016 Source
Koyuncu et al. 2015 Source
Hillblom Foundation 990 for 2015 Source
López-Otín et al. 2013 Source
Lowe 2017 Source
Nelson 2015 Source
NIH Categorical Spending 2016 Source
NIH FY 2015 Congressional Budget Justification Source
Ocampo et al. 2016 Source
Pitchbook, Alkahest Source
Sandberg and Bostrom 2008 Source
Sen et al. 2016 Source
SENS Foundation 990 for 2014 Source
Social Security Administration, Period Life Table, 2013 Source
Sweatt 2010 Source
Taimen et al. 2009 Source
Trounson and DeWitt 2016 Source
Villeda et al. 2011 Source
Wikipedia, List of the verified oldest people Source
Zealley and de Grey 2013 Source

  • 1. Nick Beckstead and Claire Zabel reviewed the materials produced by our advisors. Claire Zabel chose a page of their report at random and carefully checked as many claims on it as she could. We concluded that any inaccuracies were relatively minor.
  • 2. See next footnote for citation.
  • 3. “Aging is characterized by a progressive loss of physiological integrity, leading to impaired function and increased vulnerability to death. This deterioration is the primary risk factor for major human pathologies, including cancer, diabetes, cardiovascular disorders, and neurodegenerative diseases. Aging research has experienced an unprecedented advance over recent years, particularly with the discovery that the rate of aging is controlled, at least to some extent, by genetic pathways and biochemical processes conserved in evolution. This Review enumerates nine tentative hallmarks that represent common denominators of aging in different organisms, with special emphasis on mammalian aging. These hallmarks are: genomic instability, telomere attrition, epigenetic alterations, loss of proteostasis, deregulated nutrient sensing, mitochondrial dysfunction, cellular senescence, stem cell exhaustion, and altered intercellular communication. A major challenge is to dissect the interconnectedness between the candidate hallmarks and their relative contributions to aging, with the final goal of identifying pharmaceutical targets to improve human health during aging, with minimal side effects.” López-Otín et al. 2013, abstract.
  • 4. Meaning non-genetic state of chromosomes that affects gene expression.
  • 5. When asked for an illustration of the evidence for this, Heather Youngs, one of our scientific advisors, offered the following quotes and comments:

    “There is an emerging understanding that chromatin is dynamic and is subject to extensive experience- and age-associated remodeling. For example, global loss of DNA methylation in aging, or the hypermethylation of regulatory regions (promoters) of genes associated with accelerated aging, such as the Werner syndrome and lamin A/C genes, has been proposed to control aging and longevity. In addition, the sirtuins, a family of nicotinamide adenine dinucleotide (NAD)–dependent histone deacetylases, link chromatin regulation, cellular transformation, and longevity. And chromatin modifications also regulate telomere-length control, an aging mechanism. These disparate findings suggest a unifying hypothesis: that the accumulation of aberrant epigenetic marks over the life span drives aging-related cellular and physiological changes.” Sweatt 2010.

    “A genome-wide study of senescent chromatin showed that >30% of chromatin is dramatically reorganized in senescent cells, … changes [in histone methylation, an epigenetic modification,] suggest that the senescent state hosts a dynamic and imbalanced chromatin environment that is markedly different from the proliferating state.” Sen et al. 2016.

    Researchers have been able to correlate one measure of epigenetic change (methylation status of CpG islands) with biological age, as distinguished from chronological age. (See figure 6C from Horvath 2013.) That is to say that while there is a general correlation of these marks with chronological age, symptoms associated with aging can be correlated with a state akin to an “accelerated epigenetic age” or vice-versa.

    “First, the epigenetic age of blood has been found to be predictive of all-cause mortality even after adjusting for chronological age and a variety of known risk factors. Second, the blood of the offspring of Italian semi-supercentenarians (i.e. participants who reached an age of at least 105 years) has a lower epigenetic age than that of age-matched controls. Third, the epigenetic age of blood relates to frailty and cognitive/physical fitness in the elderly.” Horvath et al. 2016.

    “[T]he associations between epigenetic age acceleration and mortality did not differ significantly across subgroups of race/ethnicity, sex, BMI, smoking status, physical activity status, or major chronic diseases. The consistency of the associations across multiple subgroups lends support to the notion that epigenetic age acceleration captures some aspect of biological aging over and above chronological age and other risk factors.” Chen et al. 2016.

  • 6. When asked for an illustration of the evidence that supports this point, Heather Youngs, one of our scientific advisors, offered the following quotes and comments:

    “It is as yet unclear whether changes in the activity of epigenetic enzymes influence the expression of critical longevity genes or whether alterations in the longevity genes drive large-scale epigenetic changes in the genome. In lower model organisms, single point mutations in epigenetic enzymes dramatically alter lifespan.” Sen et al. 2016.

    In a mouse model of premature aging,* induction of the factors used to epigenetically reprogram mature cells to a stem-cell-like state** dramatically reduced the symptoms of aging. The symptoms that were restored included cellular measures (specific levels of age-related enzymes, histone modifications, cell structures and DNA damage), as well as symptoms associated with “aging in multiple organs, including the skin, spleen, kidneys, and stomach”, “gross improvement in the appearance of the gastrointestinal tract”, “partially rescued the degeneration of vascular smooth muscle cells”, and “a dramatic increase in median and maximal lifespan.” The reprogramming did not completely cure the mice of their progeroid disease and had other major negative side effects in the mice, which indicates there is still a lot we don’t know. Ocampo et al. 2016.

    * “[T]he premature aging mouse model that carries a G609G mutation in the gene Lmna (LAKI). This mutation leads to the accumulation of a truncated form of lamin A (called progerin), which is responsible for human HGPS [Hutchinson-Gilford progeria syndrome]. LAKI mice are short lived and exhibit accelerated onset of many age-associated physiological phenotypes, including weight loss and alterations associated with aging in multiple organs (e.g., skin, kidney, and spleen).” Ocampo et al. 2016. However, this may not be good model for normal aging. The mutation in lamin A causes an abnormal distribution of proteins in the cell nucleus, resulting in an abnormal shape and abnormal organization of chromatin during mitosis, which limits cell division. Taimen et al. 2009 There is no evidence for this mechanism in normal aging.
    ** Mice were transformed with the “Yamanaka factors”, four transcription factors – Oct4, Sox2, Klf4, and c-Myc (OSKM) – used to create induced pluripotent stem cells from differentiated cells such as fibroblasts. Using this system, researchers could induce short-term, cyclic expression of these factors, presumably increasing the pool of active stem cells in some tissues.

  • 7. Our understanding is that selectively identifying, tagging, and intervening on specific cell types is a major challenge for cancer research and drug delivery research that receives substantial attention and funding (more detail on delivery below). Conversely, we would also guess that a smaller percentage of target cells would need to be impacted for this idea to succeed than for a cancer therapy to succeed. It is also our understanding is that scientists’ ability to specifically control, or even fully record, the epigenetic state of a cell is very limited. We would expect such advances in epigenetics to be very useful in stem cell research and regenerative medicine (e.g. for growing an organ for transplant made from stem cells of the person who will receive it).
  • 8. The above two points reflect our recollections from conversations and review of the literature. For the third, our scientific advisor Chris Somerville wrote the following as an explanation:

    In brief, researchers created transgenic mice that had been modified so that cells that expressed a gene (Ink4a) that is most strongly expressed in senescent cells, could be killed by periodically administering a drug that targeted those cells.* The mice did not exhibit any obvious deleterious effects from having their senescent cells removed, suggesting that drugs that kill senescent cells may have strongly beneficial effects on aging.

    * The Ink4a gene promoter was used to express a protein fusion between a toxic protein (caspase 8) and a drug-binding protein FKBP. Administration of a drug (AP20187) caused the FKBP domain to dimerize and activated the caspase domain to kill the cells expressing the fusion protein.

    “To examine the effect of p16Ink4a-positive cell clearance on health and lifespan, we sequentially established two cohorts of ATTAC transgenic mice (Fig. 2a). The initial cohort was on a C57BL/6-129Sv-FVB mixed genetic background fed a diet containing 9% fat. We note that this diet shortens lifespan compared to diets with 5% fat typically used in lifespan studies (Extended Data Fig. 4a, b and Supplementary Information). The later cohort was on a congenic C57BL/6 background fed a standard 5% fat diet. At 12 months of age, when p16Ink4a+ cells started to accumulate in several tissues (Extended Data Figs 1d and 3a), mice were injected twice a week with AP or vehicle until they became moribund or died of natural causes. Mice separate from the longevity cohorts were examined for a series of age-sensitive outcomes at 18 months, an age at which relatively few mice in each of the cohorts had died. Data for both sexes combined showed that median lifespans of mixed and C57BL/6 AP-treated animals were increased by 27% and 24%, respectively. Median lifespans for each sex separately were also significantly extended in AP-treated cohorts irrespective of genetic background, with increases ranging from 17% to 35% (Fig. 2b, c).” Baker et al. 2016.

  • 9. These strategies include but are not limited to the following: (i) finding an agent that selectively kills senescent cells once inside of them and delivering the agent to a large majority of cells, (ii) finding a way to selectively deliver an agent to senescent cells (there are existing agents that can kill cells once inside of them), or (iii) finding a way to tag the senescent cells for destruction by the immune system (along the lines of cancer immunotherapies). These approaches have much in common with cancer therapies in that they aim to selectively destroy a specific type of cell, but they could plausibly be easier because we believe that killing a moderate fraction of target cells could be useful as an aging intervention but not a cancer intervention. Our understanding is that (ii) would require advances in agent delivery but (i) would not. We raise these generic strategies only as plausible possibilities and do not have confidence in the feasibility or timeline for success of these particular approaches.
  • 10. Our understanding is that the above points are generally accepted by researchers in the field. An abstract of a review paper discussing related themes reads as follows:

    “One of the most obvious characteristics of the aging process is the progressive decline in the regenerative potential of tissues. Adult somatic stem cells are critical for rejuvenating tissues and persist throughout the lifespan of organisms. However, stem cell function declines during the aging process in tissues such as the brain, blood, skin, intestinal epithelium, bone, and skeletal muscle. This demise may contribute to tissue degeneration, organismal aging, and age-related diseases. A series of organismal models have emerged as valuable systems to study stem cell aging in vivo. Here, we review the age-associated changes of stem cells and the different organismal models used to define stem cell aging.” Koyuncu et al. 2015.

  • 11. Potential factors include genomic instability, telomere attrition, epigenetics, loss of proteostasis, mitochondrial dysfunction, and impaired nutrient sensing. See Koyuncu et al. 2015 as a whole, especially the section headings.
  • 12. First, there is some evidence that these cells can be reactivated when certain activating factors are introduced (though biophysical cues may also be needed). For example, aged skeletal muscle stem cells (MuSCs) of mice can be reactivated by transplanting them into a younger microenvironment or an environment containing certain factors.* Rejuvenation of stem cells has also been inferred from the results of heterochronic parabiosis experiments (discussed below), so understanding the factors involved in that phenomenon may lead to useful interventions. Second, inhibitory factors may prevent exhausted stem cells from functioning, and one possibility is that removing these factors would reactivate them. Prevention and removal of cellular senescence could play a role in that. Finally, introducing compatible, non-exhausted stem cells into specific niches in people’s bodies may also address this set of issues. These interventions are speculative, long-term possibilities rather than concrete proposals that can be supported by strong evidence at this time.

    * “Two-thirds of MuSCs from aged mice are intrinsically defective relative to MuSCs from young mice, with reduced capacity to repair myofibers and repopulate the stem cell reservoir in vivo following transplantation….We show that these limitations cannot be overcome by transplantation into the microenvironment of young recipient muscles. In contrast, subjecting the MuSC population from aged mice to transient inhibition of p38α and p38β in conjunction with culture on soft hydrogel substrates rapidly expands the residual functional MuSC population from aged mice, rejuvenating its potential for regeneration and serial transplantation as well as strengthening of damaged muscles of aged mice….The synergistic combination of these biochemical and biophysical cues stimulates the rapid expansion of functional stem cells within the progeny of MuSCs from aged mice to generate a stem cell population with rejuvenated function capable of restoring strength to injured muscles from aged mice.” Cosgrove et al. 2014

  • 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. Based on a combination of conversation with our scientific advisors and survey paper they cited: Trounson and DeWitt 2016. The “Progress in clinical applications of PSCs” section of the paper discusses trials of clinical applications of pluripotent stem cells relevant to these conditions.

    The eventual possibility of organ replacement and replacement of more complex tissues is more speculative and is based primarily on conversation with our scientific advisors.

  • 13. In a document titled “Strategies for Engineered Negligible Senescence,” Zealley and de Grey of the SENS Foundation outlined a plan for engineering people to age negligibly. The plan featured seven topics: cell loss (partially related to “stem cell exhaustion” above), cell death resistance (closely related to “senescent cells” above), cell overproliferation, intracellular junk, extracellular junk, tissue stiffening, and mitochondrial defects.* Two items on our lists are closely related and have similar high-level objectives, but the lists otherwise differ in focus. Another difference is that we do not claim that progress on the topics we identified might be sufficient to make aging negligible in humans.

    * See section headings in the introduction of Zealley and de Grey 2013.

  • 14. A discussion of the philosophy and science behind this idea is well outside the scope of this report, but more information is available in Sandberg and Bostrom 2008.
  • 15. See table at NIH Categorical Spending 2016.
  • 16. See table on p. 10 of NIH FY 2015 Congressional Budget Justification.
  • 17. See Buck Institute 990 for 2014.
  • 18. See p. 1, line 25 of Glenn Foundation 990 for 2014.
  • 19. See p.1 lines 13 and 18 of SENS Foundation 990 for 2014.
  • 20. See p.4 lines 13 and 18 of AFAR 990 for 2015.
  • 21. Hillblom Foundation 990 for 2015.
  • 22. “Already awarded grants will continue to receive funds, but the foundation will not make new awards.” @Farr, 2013@.
  • 23. “AbbVie and Calico will each initially provide up to $250 million to fund the collaboration with the potential for both sides to contribute an additional $500 million.” Calico Press Release 2014.
  • 24. “Total Equity Funding[:] $300M in 2 Rounds from 10 Investors” Crunchbase, Human Longevity.
  • 25. “Total Equity Funding[:] $118.79M in 4 Rounds from 6 Investors,” “Unity Biotechnology, Inc. designs therapeutics that prevent, halt, and reverse various diseases of aging. The company focuses on clearing senescent cells; and designs senolytic medicines. Its medicines target vulnerabilities unique to senescent cells to clear those cells from the human body while leaving normal cells unaffected. The company was incorporated in 2009 and is headquartered in San Francisco, California.” Crunchbase, Unity Biotechnology.
  • 26. “Alkahest is developing therapies derived from blood and its components with a focus to improve vitality and function into old age. We are working on treatments for diseases of aging, with an emphasis on cognitive dysfunction and dementia, which are key medical challenges of our generation. The company’s pioneering research has demonstrated that factors in young plasma are able to reverse brain deficits in preclinical models relevant to normal aging and Alzheimer’s disease. Conversely, inhibition of factors that are present in old plasma can improve brain functions in preclinical models of age-related cognitive decline. The Company is conducting clinical studies in patients with different types of dementia and other neurodegenerative diseases. Alkahest is a private company based in San Carlos, CA, with investors including Barcelona, Spain-based Grifols, a global healthcare company and leading producer of plasma therapies, also a collaboration and commercialization partner.” @Alkahest About page@.

    “$53.5M Total Amount Raised,” Pitchbook, Alkahest.

  • 27. “Founded in 2016, Ambrosia studies the effects of transfusions of young blood plasma.” Ambrosia’s website lists several ongoing trials of young blood plasma transfusions. See the links under “Science.” Ambrosia website.
  • 28. Nelson 2015.
  • 29. These experiments have involved heterochronic parabiosis (anatomically joining two organisms of different ages, in this case by surgically joining the circulatory systems of young and old lab mice) and blood exchange. When asked for an illustration of the evidence that supports this point, Chris Somerville, one of our scientific advisors, offered the following quotes and comments:

    In the first modern paper on this topic, proliferation of liver and muscle cells was stimulated in old mice by joining to a young mouse. “Our studies also demonstrate that the decline of tissue regenerative potential with age can be reversed through the modulation of systemic factors, suggesting that tissue specific stem and progenitor cells retain much of their intrinsic proliferative potential even when old, but that age-related changes in the systemic environment and niche in which progenitor cells reside preclude full activation of these cells for productive tissue regeneration.” Conboy et al. 2005. Also see Figure 3, titled “Heterochronic parabiosis enhances proliferation of aged liver progenitor cells and restores molecular determinants of young liver regeneration.”

    In subsequent studies, neurogenesis and enhanced learning was observed in old mice joined to young mice whereas decreased synaptic plasticity was observed in the young mice. “…our data indicate that the decline in neurogenesis and cognitive impairments observed during ageing can be in part attributed to changes in blood-borne factors.” Villeda et al. 2011.

    Our scientific advisors say that much of the proposed work on heterochronic parabiosis could have been done at any point in the last 10 years, but has not been pursued in academia. We are uncertain of the reasons for this, but think it might have to do with the provocative nature of the work. Projects could examine the extent of life extension in mice and seek to determine which specific factors in old blood/young blood cause the observed effects. Methods under development for (mechanically) exchanging blood in animals without parabiosis might allow tests of the effects of blood-donor age on the longevity of blood recipients without the effects of stress caused by the surgical joining of animals.