Shameless linkpost, but I'd really appreciate any LW feedback:

https://milan.cvitkovic.net/writing/longevity/

Citations include @Emanuele_Ascani and @Matthew_Barnett

TL;DR:

  • We shouldn’t overestimate how much we understand aging, and we shouldn’t underestimate how much progress we can make without full understanding.
  • On the margin I agree with Open Phil that basic research and engineering for biotech tools are likely to have the biggest impact on longevity, whether this research is called “longevity research” or not. I’d say this is especially true for tools to do large-scale phenotypic assays. The hard(er) part of building the atomic bomb wasn’t the nuclear physics, it was building the bomb, and I suspect longevity is similar.
  • There are a million problems to be solved in the drug discovery ecosystem that will help achieve human longevity. Solving them may accomplish more for longevity than any direct work on aging at this point.
  • Many problems in the drug discovery ecosystem don’t require primary expertise in biological science. And most of them aren’t specific to longevity and require no explicit association with longevity. This is useful for decoupling longevity progress from the longevity brand.
  • Despite how depressingly underrated longevity research is, technologies directly targeting the experience of suffering are underrated even more, with the possible exception of psychedelic therapy (by tech) and non-addictive painkillers (by pharma). I’d prefer work on neuromodulation, mood adjustment, and new forms of analgesia to be getting as much attention as longevity.
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I disagree with most of this.

You seem to assume that aging has a bunch of root causes. We have a few lines of evidence that this is not the case for most of the core diseases of aging - I talk about this more in The Lens, Progerias, and Polycausality. Two particularly useful lines of evidence:

  • Certain mutations or interventions seem to impact a bunch of core diseases of aging all at once - progerias, for instance. This shouldn't happen if there were lots of independent root causes.
  • Many core diseases/aging markers are correlated even after adjusting for age. Again, this shouldn't happen if there are lots of independent root causes - different diseases/markers with different root causes shouldn't correlate after adjusting for age.

There are a bunch of "theories of aging" in the literature, but most of these do not seem likely to be root causes (although they may have seemed that way years ago). Some examples from your list:

  • Inflammation was never a plausible root cause at all, since it isn't self-sustaining. The inflammaging theory just hypothesizes that inflammation plays some central role, not that it's a root cause.
  • Loss of proteostasis was once hypothesized as a root cause (via an "error catastrophe" positive feedback loop). Now it's pretty clear the catastrophe version of the theory is wrong; proteostasis does get out of whack with age, but aging happens too slowly for it to be a root cause.
  • We now know that most stem cells turn over normally. While counts of such cells can decrease with age, it isn't a root cause; something else must be causing failure of normal turnover and replacement.
  • It now looks like telomere loss with age is mostly due to increased DNA damage rates, not a root cause.
  • We now know that senescent cells normally turn over in ~2 weeks. While their count does increase with age, it isn't a root cause; something else must be increasing senescence rate or decreasing removal rate.

The purpose of research into the causes of aging is not to find more causes; it's to narrow down to the true root cause, and more generally to map out the gears of the system.

The section on targeted vs "phenotypic" approaches builds on the mistaken idea that aging has lots of root causes. For instance:

Phenotypic approaches also seem better suited to finding effective combinations of therapies, for the inelegant reason that biological systems are so interconnected that to find an effective combination therapy we’ll just have to try a lot of combinations. This is important for longevity, since it’s not clear how much partial credit we get for solving any single cause of aging. It may be that each one cured buys us more lifespan and eventually we reach longevity escape velocity. But since dying only requires one cause of death, we may need therapies that simultaneously address all or most causes of aging — even ones we don’t know of yet — before seeing benefits.

We actually do know how much partial credit we get for solving particular diseases of aging, e.g. cancer or heart disease. The answer is "barely any" - someone with age-related cancer is very likely to have heart disease or Alzheimers or some other disease within a few years even if they survive the cancer. However, we have evidence that there is one main root cause for all of these. So curing the root cause of one (not just fixing the symptoms) would probably cure the others as well. This means that combination treatments are unlikely to be very relevant, other than for (temporary) treatment of symptoms.

Also, on this:

The hard(er) part of building the atomic bomb wasn’t the nuclear physics, it was building the bomb, and I suspect longevity is similar.

The only reason that nuclear physics wasn't the hard part of the Manhattan project was that the key pieces had already been figured out, years before. That is not the case for aging, as of today.

Really useful, thank you!  Although you seem to only disagree with two "root cause" errors haha - were there other errors included in "most of this"?

I read the posts you linked to.  I really like your homeostasis argument - I'll try to add it to my writeup soon.

If I understand you right, you're saying that:
     high degree of correlation between symptoms of aging (even when controlling for age) => one true independent root cause or shared intermediate

But I don't see why the situation can't be closer to a fully-connected graph of many causes, requiring intervention on many nodes.  (To be clear what I meant by "many causes," I'd consider 4+ to be many.)  That's closer to the model I have in my head.  What am I missing here?  

Also, do you have links for your last 3 bullet points? I'd love to follow up on those.

Although you seem to only disagree with two "root cause" errors haha - were there other errors included in "most of this"?

I'm also generally skeptical of the throw-stuff-at-the-wall-and-see-what-sticks approach to pharmaceutical discovery, but that's for separate reasons. In particular, if the stuff doesn't stick, then we don't gain anything; "phenotypic" search requires that we get lucky and hit the target, and doesn't give us any way to "move closer" to a solution based on what we see. That's fine if our search space is small enough (in particular if it's low-dimensional), but biological systems are not that simple.

(I'm also skeptical of the effectiveness of many existing pharmaceuticals found through this sort of search. It reeks of p-hacking potential, and I have little doubt that pharma companies are very good at p-hacking. Although I would also guess that it's gotten less problematic in more recent years, as I hear clinical trial standards have tightened up somewhat. That said, there do seem to be some kinds of interventions which are "easy" to stumble upon, in the sense that there's a ton of things which work - like antiinflammatories or antibiotics.)

I really like your homeostasis argument

Thanks! :)

But I don't see why the situation can't be closer to a fully-connected graph of many causes, requiring intervention on many nodes.  (To be clear what I meant by "many causes," I'd consider 4+ to be many.) That's closer to the model I have in my head.  What am I missing here?

If there's a bunch of causes hooked up to a bunch of effects, then there shouldn't be any reason for all the causes to push the effects in the same directions. It's entirely plausible that two different causes both have some impact on Alzheimers, cancer, osteoporosis, atherosclerosis, arthritis, cataracts, and sarcopenia. But it's pretty suspicious if two different causes both increase the risk of every single one of those things - if we had a complete graph with random weights on all the connections, then some factors should push some diseases up, while others should push down. Instead, we see a variety of mutations/interventions (like progerias, calorie restriction, etc) which all push most of these things in the same direction, which pretty strongly suggests that they're operating through the same pathway.

Statistically, we can think of this in terms of principal components analysis. A fully-connected graph should have lots of strong principal components (after adjusting for age), rather than one component dominating (i.e. effects strongly correlated even after adjusting for age).

Also, do you have links for your last 3 bullet points?

Stem cells are a pain, because there's a bunch of different types and the differences are not small. But I'll give some info for HSCs specifically, since they're relatively well-studied. Here's a decent overview, and here's a turnover measurement; turnover is on the order of once a year. Takeaway: HSCs turn over ~ once per year, so their count should be in equilibrium on a timescale of ~1 year. If the count is decreasing on a timescale much longer than that, then something upstream must either be decreasing their reproduction rate or increasing their removal rate.

I don't have a good link on hand for telomeres, but wikipedia does mention the key puzzle piece: actual telomere shortening rates are around 50-100 bp per cell cycle (in vitro), whereas end-replication should only shorten by 20 bp per cycle; the difference is supposedly explained by shortening due to oxidative stress (though I have not personally checked those numbers). Also of note (though I don't have a link for this): the experiments which show increase in (average) lifespan usually involve continuous telomerase expression; a one-time pulse won't reset the aging clock. That generally means we're treating an intermediate factor, not a root cause.

Here's a particularly excellent paper on senescent cell turnover. Timescale is ~ weeks, so if the count is changing on a much longer timescale than weeks, then either the production rate is increasing or the removal rate is decreasing. Also, much like telomerase, senolytics experiments use continuous administration, not a one-time pulse.

I'm also skeptical of the effectiveness of many existing pharmaceuticals found through this sort of search. It reeks of p-hacking potential, and I have little doubt that pharma companies are very good at p-hacking. 

I think p-hacking is effectively fought with the standard of preregistration and requiring two studies. What's however not effectively fought is goodharting. 

If you have a substance that changes a bunch of things in the body and you find out that one of those things is positive in a very specific case under specific trial conditions you can get the drug approved. 

If you have a substance that changes a bunch of things in the body and you find out that one of those things is positive in a very specific case under specific trial conditions you can get the drug approved.

Yeah, that sounds right. Good point.

But it's pretty suspicious if two different causes both increase the risk of every single one of those things - if we had a complete graph with random weights on all the connections, then some factors should push some diseases up, while others should push down. Instead, we see a variety of mutations/interventions (like progerias, calorie restriction, etc) which all push most of these things in the same direction, which pretty strongly suggests that they're operating through the same pathway.

It's all about the damage to repair/replacement balance. Birds have higher repair rates, as do NMRs, as do bowhead whales. CR decreases synthesis of proteins that could be damaged while simultaneously (and strangely) upregulating repair. It might be instrumental to look at all the TFs activated by CR.

We actually do know how much partial credit we get for solving particular diseases of aging, e.g. cancer or heart disease. The answer is "barely any" - someone with age-related cancer is very likely to have heart disease or Alzheimers or some other disease within a few years even if they survive the cancer.

That forgets that if you have a solution to cancers that locks up a bunch of other treatments which you currently can't do because they are cancerous. 

Uh, I think loss of proteostasis and increased damage to proteins/lipids can be implicated in all types of age-disease (you could theoretically have perfect genome integrity and loss of proteostasis and aging would still occur, though at some pt the loss of proteaostasis would hit the genome.) Similarly, you can have an organism age without inflammation (think of single-celled organisms), telomere damage, oxidative stress (though oxidative damage is one of the most common forms of damage), or senescence (all of these are just accelerants). More complex organisms just have more ways to get damaged (they also have more sophisticated methods of damage control, especially birds/naked mole rats/bowhead whales)

But reduced ability to maintain the specificity, stoichiometry, and precise control offered by the genome/proteome due to changes in the cell's abilty to synthesize the proteins needed to properly sense perturbations from equilibrium [and being able to properly translate and distribute the proteins that act on such perturbations] - is fundamentally a root cause of aging in all organisms. "Damage" to a proteome (or lipidome) - some of which is sensed throughout the organism - ultimately leads to the other "accelerants" like telomere attrition, stem cell loss, or senescence that further compromise a cell's ability to do proper repair .

>fully-connected graph of many causes

This is probably the best way to "explain" a "cause" even though it isn't great for linguistically compressing causality (or even compressing causality by pearl's notation).

Plausible as a common intermediate cause, but not as a root cause. The proteome generally turns over on fast timescales, so it's in equilibrium on fast timescales. If it's changing on a timescale of decades, then something other than (the fast-turnover parts of) the proteome must be causing that change. 

Well, the root cause is ultimately the accumulation of small kinds of damage and dislocation (like oxidative/carbonylated damage on proteins/DNA or increase of clogged proteasomes/lysosomes or inappropriate DNA adducts) that ultimately do not get corrected. An oxidative damage event in itself is nothing, but when you combine all of the events integrated in a lifetime, amounts of something.

Sure, but the vast majority of damage types are repaired (in the case of DNA) or removed (e.g. when a protein or cell turns over). So the question is which specific damage types are accumulating. Many kinds of damage increase in count with age, but the vast majority of them turn over too quickly to be a plausible root cause.

Damage/dysregulation to the control sites are more central to the network - repair genes/proteins like OGG1/ERCC1 or the upstream control factors of everything or kinases. For whatever reason, expression of most repair genes (and heat shock proteins) goes down with time.

Spliceosomes are esp impt too, as are the upstream genes behind lysosome synthesis (https://en.wikipedia.org/wiki/TFEB) and proteaosome synthesis.

Damage to structural components (like extremely long lived proteins) are harder to repair and simultaneously make it harder for repair proteins to properly localize to places where needed.

It's not a matter of simple downexpression or up-expression - though if I were to bet I wouldn't say that damage to the repair proteins or proteasomes are totally causal - it's just the simultaneously distributed damage of everything that ultimately builds up and I don't think it can be summed into any neat causes other than changed damage to repair ratio.

If I were to bet on one mechanism, it would be repair genes that get jammed/make errors during repair. Statistically speaking, some percent of DNA repair enzymes will screw up the process of repair (or introduce further damage), and liposomes/proteasomes will get traffic jams that are difficult to remove/clear.

Damage/dysregulation to repair genes/proteins like OGG1/ERCC1 or the upstream control factors of everything.

Nope, they turn over too quickly. You'd have to damage most copies at the same time in order for it to have a permanent effect; otherwise the remaining copies will bring us back to equilibrium. (And even if most copies were damaged at the same time, the whole cell should still turn over, so that would also need to be prevented somehow in order to prevent reequilibration.) If expression is decreasing on a timescale of decades, then something upstream must be changing the equilibrium expression level.

https://www.nature.com/articles/s42255-020-00304-4

Structural genes like the extremely long-lived proteins in nuclear pore complexes don't turn over (similarly, damage to nuclear histone proteins is very difficult to repair). Even small changes in these genes can affect the ability of mRNA and all of the spliceosome proteins to be properly assembled where they're most needed => this gradually sums up to a corrosion of cellular information

They do turn over when the cell turns over, which for most cell types is still way faster than the timescale of aging. They could be a plausible root cause in very long-lived cell types, but I would guess that in long-lived cells they usually do turn over on a timescale faster than decades. This paper, for instance, finds that nuclear pore turnover is slower than turnover of rat kidney cells, but rat kidney cells turn over in weeks IIRC. NPC could turn over in years, and that would still be fast compared to aging.

Is it even possible to map out "root causes" in a complex system (eg maybe Granger causality in neural networks) when the "cause" could be multiple factors that are jointly necessary - none of them sufficient enough to cause the irreversible feedback loop in itself?

You talk a lot about fundamentals and come to a conclusion about what projects should be funded on the margin. It seems to me that to make good calls about what should be funded on the margin we actually have to look about what money on the margin buys. 

It's a bit strange to call for less longevity research spending both complain that the FDA doesn't allow clinical trials when the clinical trial for aging that the FDA did approve is hold back by lack of funding.

With an $41.68 billion NIH budget it seems to me that paying 8-figures for a Metformin trial is on the margin a decent project even if we shouldn't expect that Metformin will add decades of life. 

The SENS Foundation seems to have a yearly budget of <5,000,000$. Funding it's research project with a 8 or 9-figure budget would also make sense to me. 

The talk about the list of limited causes of aging never really makes sense to me. Adult humans don't seem to grow new muscle cells and some muscle cells die over time. Given that the dead one don't get replaced, that seems to me like aging but it's not on the list. The list seems also very driven by molecular biology and doesn't include sensor motor amnesia with I consider on factor of aging. 

Despite how depressingly underrated longevity research is, technologies directly targeting the experience of suffering are underrated even more, with the possible exception of psychedelic therapy (by tech) and non-addictive painkillers (by pharma). 

That seems to me like a strange thing to say. A lot of pharma research goes into developing antidepressiva that help people who suffer a lot suffer less. There are also various people in mainstream psychology who think about how to get people to suffer less. 

The Manhatten project could easily do a test of whether their design worked. With aging we need to have a good enough theory to know whether any proxy measures we use to judge aging are actually good enough proxies or using them as outcomes for drugs is just Goodharting.

My reply comes a bit late since I managed to write a long comment without clicking send and only noticed this now. I will address the errors I see in the TL;DR summary from the POV of a semi-professional biogerontologist:

The disease-based approach to aging this seems to favour is useful, but limited. In fact, if you genuinely want to extend both lifespan and healthspan this excessive focus on the disease-based approach would be inefficient because is inconsistent with everything we know about aging. I would go as far as to say that the disease-based approach may be actively harmful because it takes away resources from genuine aging research.

While aging probably has thousands of causes, or even more*, this does not preclude the existence of major causes that limit lifespan in the near term.  This idea has been popularized by Aubrey de Grey a long time ago and now has reached the scientific mainstream with an emerging consensus about the Hallmarks of Aging (several key pathways and sequelae of aging). We also know that this view is decently well supported in mice and have known so since the late 1990s when Holly Brown-Borg and Andrzej Bartke introduced the Ames dwarf mouse to gerontology. If aging was strictly multifactorial and polygenetic there would be no hope to identify single genes that lead to pronounced lifespan extension, as they did with the long-lived Ames mouse, which is long-lived because of an underdeveloped pituitary and reduced growth hormone levels. This means one simple change to a single pathway can extend lifespan.

Of course, I am biased, since as a biogerontologist I think the biggest gains are to be had from targeting aging directly, although we can have a discussion how well the mouse data translates to humans. (Not well, IMHO, but it is the best we have.)

Sizable lifespan extension we have seen in mice has come, without exception, from interventions that target aging directly through the above discussed “hallmarks”. Just to give three famous examples of life extending treatments: We have Rapamycin, an inhibitor of the mTOR pathway, that became a plausible candidate after this pathway had been implicated in the aging of yeast. Then we have caloric restriction, which was discovered by accident and not by the disease-based approach, but is now known to target a global pathway that promotes tissue maintenance under nutrient stress. Finally, we also have senolytics, drugs that were developed to kill senescent cells, that had been linked with aging after decades of biogerontologic research.

In contrast, drugs like Aspirin, Simvastatin, Enalapril and many others were tested in mice with no clear biogerontologic rationale behind them and predictably failed to extend lifespan, even though they are obviously amazing from a disease-prevention point of view. 

However, I do agree that biogerontology depends on the existence of a strong biomedical ecosystem. Rapamycin was initially discovered as an immunosuppressant and if not for that, it would have taken longer to find inhibitors of the mTOR pathway (but eventually it would have happened by standard medicinal chemistry). Working in the 1930s Clive McKay, the discoverer of caloric restriction, was perhaps more interested in the basic biology of starvation and malnutrition than finding treatments for aging, etc.

Nothing about age-related multimorbidity makes sense if it not viewed through the lens of biogerontology.

Notes
* for example, you may be able to get 10-30% of lifespan extension by targeting the top 10 causes of aging, then eventually as you want to extend lifespan more and more, other causes of aging would take the spotlight

I should add that much of the most encouraging progress is in the area of xenotransplantation/stem cell transplantation, artificial organs, and neuronal replacement therapy (it's already being done for Parkinson's, though regeneration of the basal ganglia may be easier than regeneration of the entire brain - the https://gage.salk.edu/ lab is particularly good to follow on this). You don't need an entire mimic of the brain's memory or identity to maintain the continuity of consciousness.

https://www.nature.com/articles/s41536-017-0033-0?fbclid=IwAR2N4wjwAhHM3OXfGXV7QUNTUxFB3n275QO8-gDsA7qRkuL3ZeFVIrbyT5o https://www.frontiersin.org/articles/10.3389/fgene.2019.00310/full?fbclid=IwAR0RP6zGAUEBhphqk_t-rtIFEvHAo2c_PbPpmB-pPElnG20Tt1aiDx2vyLc

https://today.tamu.edu/2020/10/23/could-a-nasal-spray-of-nanovesicles-repair-brain-cells/?fbclid=IwAR0KP26TV-m4PWyhPs_PXMKNJIwWDwjulPtWndayJrdiNAqM2reUGgwkVM0

You don't need a full understanding of aging to safely transmit stem cells or tissue from one organism to another, and there are scientists who are working on the immunorejection problem wrt non-allogenic stem cells (eg see https://www.pnas.org/content/116/21/10441?fbclid=IwAR0LXoEBoZ_7THOj3szfW3rpqb-wDMv0xxFHFYcHstZfY3hZl2kDXgYHSuw ). 

Hell, some people [like Dave Asprey] already boldly inject themselves with stem cells (https://blog.daveasprey.com/how-adult-stem-cells-can-help-stop-pain-and-reverse-aging/ ) and while he doesn't know what the hell he's doing (and it seems like the FDA isn't even holding him back from this), the experimentation provides great evidence for the rest of us.

Gradual "chimerism" is an encouraging direction that does not require us to understand all kinds of age-related damage (eg https://twitter.com/biorxivpreprint/status/1314766530765295618 ). "chimerism", broadly speaking, is inclusive of cells "transferring mitochondria" to other cells, cells "transferring telomere to other cells", AAV'ing or CMV'ing genes [like enhanced SIRT6] from centenarians or bowhead whales into humans.

Even glial cells and astrocytes can be "reprogrammed" into neurons (though whether they will retain the information is another issue), and there are ways for cells to "expel" their aggregates/debris to be cleared up or removed by macrophages/astrocytes/cerebrospinal fluid (hell, even the Li-Huei Tsai lab has shown that playing 60Hz frequencies can help remove amyloid plaque from neurons). One of the real questions I have is whether there is a way for a cell to expel all kinds of intracellular junk, including the notoriously impliable lipofuscin and ceroid aggregates (there's a kind of lipid/protein structure that is amenable to being engulfed by exosomes that can clear out the damage). 

it's important to note that bowhead whales can live to 200+ years even without obvious age-associated pathology, and we may be better prodded to build more "robust" mitochondria/cell membranes just by studying them (eg degree of membrane unsaturation seems anticorrelated to longevity in organisms like birds), and we can simply try to make our cell membranes less prone to ROS (one way is to incorporate deuterated PUFAs/omega-3's), which somehow still does not get as much research as claimed [some degree of enhanced deuteration is also helpful for longevity].

Overall you want to maintain the cell's ability to sense damage and to properly reduce this damage before it reaches high levels [genomic damage/mosaicism is the hardest to sense, but this is ultimately a more distal problem than more immediate problems that come from loss of proteostasis]