We can all agree that priorities in research for a longer, healthier human life span are far from rational. Among the distorting influences are
- Leap-frogging ahead to medical research in a field where the basic science is not yet fully understood.
- Inertia from a research infrastructure that has been built on the wrong priorities. Both people applying for grants and people evaluating those applications are stuck in an old paradigm.
- Investment capital seeks profits in short-term, low risk projects
- Misunderstanding of the basic nature of aging—a misunderstanding which also has capitalist roots.
Last month, an article in Nature Biotech surveyed the firms that are involved in longevity research, their resources and their strategies.
Until recently, research in aging medicine has been Balkanized into study of atherosclerosis, cancer, Alzheimer’s disease, Parkinson’s, and various smaller projects to study the diseases that affect older people. The idea that we might be able to address all these diseases in one fell swoop if we can alter the fundamental biology of aging is not new, but it has been slow to take hold, and even now, research priorities remain lopsided. Basic research in the biology of aging is absurdly under-funded, when compared to budgets for research on particular diseases. The National Cancer Inst alone has a $5 billion budget, and Big Pharma is investing billions of their own in new chemotherapy agents that may or may not be marginally more effective than the old. Meanwhile, the basic science of aging is studied on a budget estimated to be less than $1 billion. Within that budget for the pure science of aging, I would propose that there are also substantially distorted priorities.
An article in Nature Biotech last month surveyed the private biotech investments in anti-aging technology. We should all pause to celebrate the fact that this field finally has credibility, and is attracting substantial funding. But, in my view, the funding is largely misdirected, and a few projects that I think would be good bets for a major leap in life extension have yet to be funded at all.
Researchers on aging are slowly pivoting from treating aging as a disease or indication to considering it a collection of age-related diseases.
This is the good news. There is an enormous streamlining available when we turn from treating diseases separately to treating the root cause of aging. But there is still a lot of ideology that says, “it can’t be that easy.” This is the bad news.
[Linda] Partridge says “theoretical and practical insights have led to the conclusion that aging is likely to be a highly polygenic trait”. Contributing to aging is a protean list of processes, among them, genomic instability, telomere attrition, epigenetic alterations, loss of proteostasis, deregulated nutrient-sensing, mitochondrial dysfunction, cellular senescence, stem cell exhaustion and altered intercellular communication.
Partridge’s theory is taken from George Williams’s seminal paper of 1957. He writes in response to Medawar’s program of isolating the root causes of aging in a small number of physiological processes:
Any such small number of primary physiological factors is a logical impossibility if the assumptions made in the present study are valid. This conclusion banishes the “fountain of youth” to the limbo of scientific impossibilities where other human aspirations, like the perpetual motion machine and Laplace’s “superman” have already been placed by other theoretical considerations. Such conclusions are always disappointing, but they have the desirable consequence of channeling research in directions that are likely to be fruitful. [Williams, 1957]
But this perfectly reasonable conjecture of Williams was proven to be dead wrong in the 1990s, as single genes were discovered that offered dramatic life extension in worms. There are now dozens of such genes known, and many of them are genes that need to be disabled, not new genes that need to be added to the genome. In other words, there are powerful, known pro-aging mechanisms that make promising targets for pharmaceutical intervention. Throwing a monkey wrench into an existing metabolic pathway is what Big Pharma knows best how to do (e.g., seratonin re-uptake inhibitors, beta blockers, COX2 inhibitors). What we need is an inhibitor of pro-aging genes.
Rapamycin seems to be the first candidate in this category, and it is being appropriately explored, as reported in this space last week.
Here’s a caveat: The easiest path to life extension is through caloric restriction mimetics. In other words, trick the body into thinking it has less food than it is really eating. Some of the early genetic modifications in worms worked in this way. DAF-2 was an early discovery, doubling life span of worms in Kenyon’s lab when it was partially disabled . The catch is that lab worms are champions of adjustable life span. They are exquisitely adapted to be able to survive months at a time with no food at all, but to die within a few days once they have plenty to eat. Larger animals also live longer when they eat less, but the effect is much smaller. My guess is that CR potentially adds 5-10 years to human life span–nothing to sneeze at, but not the big, dramatic gains we might hope for in the long run. If we find a really, really good caloric restriction mimetic, we might hope to capture most of that 5-10 years.
This is the low-hanging fruit being chased by the lion’s share of private investment in anti-aging medicine today. No doubt, it will be achieved in short order (though it may be decades before we know which strategy works best, because longevity data in humans takes a long time to compile.)
Neglected is the potential for much greater gains that go beyond the potential of CR mimetics.
Let’s go back to Partridge’s “protean list” of complicated processes that have to be addressed:
- telomere attrition — This is a primary aging clock, cause of many downstream effects.
- epigenetic alterations — Gene expression changes with age. When we are in our teens, gene expression is modified to halt growth and initiate puberty. When we get old, a similar process leads to a gene expression profile that gradually destroys the body on an accelerating schedule.
- genomic instability — This is DNA damage, and by far the greatest source comes from short telomeres. Telomeres cap the ends of a chromosome and keep it from unraveling. When the telomere is too short, the chromosome becomes unstable. So this may be traceable to #1. => See comment below by Bowles for another mode of genomic instability, this one controlled by epigenetic markers.
- loss of proteostasis — This refers to protein mis-folding, which is observed in Alzheimer’s Disease among other diseases of old age. But proteins are being created and folded and re-cycled all the time. Part of the reason that mis-folded proteins accumulate with age is simply that the body’s repair mechanisms are slowing down. Another part is (my guess) that genes that take care of this function are being down-regulated–in other words, we might trace this problem to #2 as primary cause.
- deregulated nutrient-sensing — This is loss of response to insulin, related to “metabolic syndrome.” I believe this happens under epigenetic control.
- mitochondrial dysfunction — This is the “free radical theory” or “mitochondrial free radical theory”, still invoked despite all the evidence against it. It’s true that we have fewer mitochondria as we age, and that the mitochondria process energy less efficiently. But the activity and the reproduction of mitochondria are under control of the cell nucleus, hence this, too, will prove to be a symptom and not a root cause of aging.
- cellular senescence — barely distinguishable from #1, telomere attrition.
- stem cell exhaustion — primarily caused by telomere attrition.
- altered intercellular communication — hormone signals through the blood are under epigenetic control.
Thus the “protean list” of nine complications derive largely from two ultimate sources: telomere loss and epigenetic reprogramming. These should be our primary targets for anti-aging research.
* A Cell article this week from Elizabeth Blackburn’s UCSF lab suggests that activating telomerase may have rejuvenating benefits over and above its role in extending telomeres.
Companies investing in anti-aging research
The following table is taken from the same article:
|Table 1 Companies commercializing longevity|
|Company (year founded, location)||Focus||Founders (affiliation)||Seminal publication|
|Alkahest (2014)||Translating parabiosis, transfusing young blood into Alzheimer’s patients||Karoly Nikolich, Tony Wyss- Coray||Villeda 2014|
|Calico (California Life Company, 2013)||Research and development into the biology of life span with undisclosed amount of Google funding.||Arthur Levinson, Cynthia Kenyon, David Botstein, Hal Barron|
|CohBar (2009, Pasadena, CA, USA)||Develops mitochondria-derived peptides with pleiotropic effects in age-related conditions (diabetes, cardiovascular disease, Alzheimer’s disease)||Pinchas Cohen (University of Southern California), Nir Barzilai (Albert Einstein), John Amatruda (formerly with Merck), David Sinclair||Muzumdar, 2009|
|Elysium Health (2014)||Consumer health products||Leonard Guarente (MIT)||Mouchiroud 2013|
|Human Longevity Inc (2014)||Combining human genomics, informatics, stem cell advances to solve diseases of aging||Craig Venter, Robert Hariri, Peter Diamandis|
|L-Nutra (2008)||Fasting mimicking and enhancing diets||Valter Longo (USC)||Parrella 2013|
|Metrobiotech (2008)||Compounds that raise NAD+ levels||David Sinclair (Harvard)||Gomes 2013|
|Navitor Pharmaceuticals (2014)||Selective regulation of M-TORC1, raised $23.5 million in series A round of funding||David Sabatini (MIT/ Harvard)||Dibble 2013|
|Proteostasis Therapeutics (2008)||Therapeutics that modulate protein folding and homeostasis; preclinical programs in cystic fibrosis, neurodegenerative diseases $45M raised||Andrew Dillin (UC Berkeley) and Jeffrey Kelly (Scripps Research Institute)||Cohen 2009|
None of these is investigating epigenetic reprogramming, probably because it is too early for commercial investment–no one knows how to do it yet. The only company based on telomerase activation is Sierra Sciences, which is below the part of the chart I reproduced, companies listed as in financial straits. The only company with research based on a changing profile of circulating blood factors is the first, Alkahest.
The two wild cards are Craig Venter’s Human Longevity, Inc and Google’s CALICO. Both are well funded, and neither has offered details about their research programs. Last year, Venter hired the man who headed Google Translate, signaling a brute force approach, based on theoretical agnosticism: Sequence a million human genomes. Look for patterns, e.g., what do the genomes of people who don’t get Alzheimer’s Disease have in common. In my opinion, this is a cumbersome approach, inspired by successes in information processing, rather than knowledge of biology. As I said, I think aging is controlled by epigenetics, and the largest gains will be made when we learn to re-program the epigenetic profile of an old person to make it look more like a young person.
CALICO, then, is crucial. Their direction is not yet determined, and will be shaped by Kenyon’s vision and beliefs. Kenyon has ambition and a wide-open imagination, and she is open to ideas about programmed aging. We can hope that her extensive experience with worms informs but does not limit her vision.
Historically, Ellison Foundation has been one of the most reliable sources of big bucks for innovative research, with about $400 million in aging-related grants since 1997. But last year, Ellison pulled out of anti-aging research. The Life Extension Foundation (LEF.org) has, by its own accounting, funded research totaling $140 million over three decades. They have been independent of the bureaucratic thinking of the National Institutes, but they have their own biases, favoring natural remedies that can be sold without FDA approval. SENS Foundation, with an annual budget of $4.5M, has grown from the singular vision of Aubrey de Grey, and has all the ambition and also the limitations of Aubrey’s paradigm. To their credit, SENS is looking seriously at long-term projects that show potential for major gains in life span. But, at least from my perspective, they are neglecting the most promising avenues, because Aubrey does not believe it is possible that aging might be controlled by biochemical signaling. The “engineering” approach to fixing what goes wrong is a long, hard road. Peter Thiel has offered the greatest outside support for SENS, and Thiel has also made grants to other anti-aging initiatives.
Historical distortion of aging science by evolutionary theory
In the long run, the greatest damage has been done indirectly, by capitalist ideology that has infiltrated the culture of evolutionary science. From the beginning, Darwin’s theory was hijacked by “social Darwinism” which twisted the theory to create justification for hereditary class privilege in British society. “Fitness” was elided with “financial success”. “Natural selection” became a sanction from Natural Law for income inequality.
In the first half of the 20th Century, Darwin’s theory was re-cast as a modern science, with quantitative measures, equations, and predictions. The work was spearheaded by R.A. Fisher, who happened to be both a prodigious genius in statistical theory, and also an elitist/eugenicist. The version of evolutionary theory that was bequeathed to us was further caricatured by Richard Dawkins as the Selfish Gene. In this version of evolution, the emphasis is on individual competition to the exclusion of cooperation. There is little room for self-sacrifice, and such obviously communal adaptations as sexual reproduction have become inscrutable mysteries.
This kind of theoretical foundation has made the biological community blind to clear and manifest signs that aging is an epigenetic program, akin to growth and deveopment. When you are a teenager, genes are turned on that cause secretions of sex hormones, and reproductive function is awakened. When you are in your 60s and after, another set of hormones is switched on epigenetically, and the body becomes hyper-inflamed, auto-immune, insulin resistant and self-destructive. Most biologists look at these changes and they figure that the body must know what it is doing, that there must be a redeeming positive benefit for these changes, and it would be dangerous to second-guess the body’s wisdom. But the truth is that these late-life epigenetic changes have little benefit, and their predominant purpose is to destroy the body on an accelerating time scale.
Most researchers are busy asking themselves what goes wrong. Neglected is the process plain and clear, where the body is being destroyed by “what goes right”.
It follows that the greatest opportunities for radical anti-aging are to characterize the chemical signals that control aging, and to adjust the signaling environment of an old body to make it more like a young body.
To some extent, this can be accomplished simply by lengthening telomeres, which have a substantial epigenetic reach of their own (TPE). There are knowledgable advocates in the field who think lengthening telomeres is the most important thing we can do. It is certainly the most accessible path, and should be a high near-term research priority.
My candidate for basic research:
Study the Epigenetic Clock that Controls Development as well as Aging
Biological science today does not know how the onset of puberty is timed. We know that epigenetic changes are triggered at an appropriate age, and a few key sex hormones initiate the onset of fertility. What we don’t know is how the body detects that the time has come for this to happen, whether there is an internal clock mechanism, and if so, how it works. To me, this would be one of the most valuable studies in basic science, and I believe that when the epigenetic/developmental clock is understood, the results will carry over directly to understanding of the aging clock. And if we can reset the aging clock, it’s a whole new ballgame.