Cool study, but no lifespan effects bro

— Everyone, including myself until recently

The aging field has historically focused on the twin aims of longer and healthier lives. As a trend, interventions that extend lifespan also tend to improve health whereas the opposite is not true. I suspect that some would even consider lifespan extension in some model organism as one of the necessary conditions to call something a promising aging drug. This heuristic has limits.

When I wrote the Longevity FAQ I reviewed a number of interventions. When doing so, I was looking at various effects on health, and lifespan extension. If I found something that did not extend lifespan, I would be less interested, it would be like a second class intervention. Ultimately longevity implies long life right? Something that extends lifespan by 20% sounds more exciting that something that causes various improvements in health but no increase in lifespan. And also interventions that improve lifespan also tend to improve healthspan anyway, so shouldn't we use lifespan as a heuristic to know what works and what doesn't, a "higher bar" for us to be interested in an intervention? Kind of, but I'll argue here that thinking too much about that in the short term can severely limit what can be accomplished in the longer term. What we want are interventions that extend lifespan (and healthspan) for the right reasons, that is by reversing or slowing aging, and doing so in ways that scale and compound with other interventions.

I have written elsewhere about what I consider aging to be, and what aging is heavily hints at the fact that no one drug will comprehensively target aging; instead different drugs will impact a subset of aging mechanisms. To get lifespan increases, one can also target a narrow subset of those, so narrow that said intervention wouldn't deserve to be called an aging drug.

Consider mice. Mice are not little humans (citation needed), but they present all the hallmarks of aging and kinds of damage accumulation that are also present in humans, which is not true for C. elegans or Drosophila, so they make for a decent model to study most aspects of aging, even if they are far from replicating human aging. Most (50-90%) mice in a reasonably large cohort will die of various kinds of cancer, typically lymphomas (Seluanov et al. 2018).

This observation implies that lifespan extension in mice requires an intervention that addresses cancer directly or indirectly.

Mice on some form of well targeted and effective treatment for cancer will live longer, but otherwise should age normally, indeed treating cancer with chemotherapy or immunotherapy as expected prolongs lifespan in mice (Bekesi et al., 1976; Straus et al. 1973, Hotz et al. 2021). I have not been able to find work that tests various functional measures besides lifespan, but my expectation is that, especially for the latter BioNTech paper, these therapies are extending lifespan almost exclusively via delayed oncogenesis, and should not show any reversal or delay of aging.

Cancer drugs are lifespan-extending drugs, but not aging drugs, except for the fact that one way to slow down cancer is to slow down cell growth or downregulate protein synthesis: unsurprisingly, rapamycin and broadly mTOR downregulation (As the key ITP hits all seem to do; and some senolytics like dasatinib are chemotherapies) slow down cancer progression (Hidalgo, 2000; Law 2005), so the effects of the broad class of interventions that are at least in part mTOR-dependent may just be anti-cancer drugs. To be sure: mTOR downregulation does have cancer-independent effects that are also very robust across model organisms, rapamycin also works in C. elegans which doesn't have cancer among its causes of death. What seems relatively clear is if these interventions are working to extend lifespan, they almost surely must be doing so via slowed tumor progression or occurrence. Perhaps there are some immune or inflammation effects as well, and there is some work suggesting that the age-related increase in cancer incidence is exclusively or mostly due to immune decline, but I think this is probably not the case: DNA mutations matter and no known anti-aging intervention reverses these (Lifelong treatments upregulating DNA repair should help though). In fact, some interventions could make them worse! DNA mutations accumulate with age and perhaps partially reprogramming these cells tips them over into cancer, as noted by Tamir Chandra here.

mTOR downregulation-dependent interventions will generally increase both lifespan and health span, that we already know. For other modalities this is not necessarily clear. These studies using senolytics (Xu et al., 2018 or Qixia et al. 2021) showed improvements in various functional parameters like treadmill endurance or grip strength, but the presence of dasatinib (a chemotherapeutic agent) or PCC1 (a compound the paper notes may have anticancer effects) means that the lifespan effects could have come from directly targetting cancer. If we look at transgenic models of ablation of senescent cells like Baker et al. 2012 or Wang 2021 these two papers don't show lifespan effects (They didn't look at that), only various health improvements. And that's fine! As it happens, removing senescent cells using these transgenic models that don't involve anything remotely looking like anti-cancer drugs can extend lifespan (Baker 2016). It would be interesting to know the exact mechanism! But it could have turned out not to be the case. Should we then discount senolytics as an interesting anti-aging therapy, throwing away the health benefits? Obviously not: If working as intended they are removing senescent cells, one of the hallmarks of aging.

[1]. They need a meme consultant to find better names lol

The reason I am writing this essay is that I'm optimistic about partial reprogramming. As of today, partial reprogramming (Or as the cool kids at Altos call it1, rejuvenation programming) has not been shown to extend lifespan in wildtype mice, the closest we have is Ocampo 2016, extending lifespan in progeroid mice. A common critique of this great paper is that "it was not wildtype mice, all you're doing is curing progeria"; and indeed the progeria mice die of progeria not cancer, so the reprogramming effects on lifespan in that paper are coming from ameliorating progeria. Ok! But the healthspan effects must be coming from reversing some of the damage that progeria causes, and progeria does recapitulate some aspects of natural aging (Ashapkin et al., 2019). Now we know that reprogramming also works for health in regular mice, from some more recent work (Wang 2021; Rodriguez-Matellan 2020; Chondronasiou 2022). But maybe it does nothing for cancer. Maybe it makes cancer worse! But the health effects are still real!

Another reason to be less excited about Rejuvenation Programming™ is that rapamycin gets you similar effects to those observed in the Ocampo paper in similar progeroid mice (Liao et al., 2016; Ramos et al. 2013). Moreover, although more rarely studied, rapamycin is also able to reverse, not merely slow down some aspects of aging (Flynn et al., 2013; Dai et al. 2014). Lifespan extension and systemic improvement is not something unique to reprogramming in this case.

And yet another reason against is that there are reports of using completely unrelated therapies that obtain effects larger than anything seen so far with reprogramming: As Kevin Perez, a postdoc at the Ocampo lab points out, overexpressing VEGF extends lifespan by 40% and improves health as measured by a number of metrics, in wildtype mice. Why so much interest in reprogramming then!

When assessing how promising an intervention will be in humans we are making guesses. There is no robust model that takes in animal data and spits out a prediction for how it'll work in humans. Various manipulations around the IGF-1/GHR axis have been able to extend lifespan in mice as documented by Laura Deming's FAQ here. However in humans, Lanier syndrome does not extend lifespan (Though it seems to have some health benefits). That is, "if it extends lifespan in mice/worms/flies/yeast" it will do so in humans is a heuristic based on largely theoretical considerations, because so far we have no agreed-on hits, just informed guesses. The reverse is also true: PCSK9 inhibition extends lifespan in humans on the margin (in a very narrow way admittedly) but the effects we can expect in wildtype mice fed a reasonable diet will probably be very weak sauce, because mice just don't die of atherosclerosis.

When assessing whether an aging paper is interesting or promising there is a set of heuristics that is commonly used, based on some prior experience and heaps of theory:

  1. Mice are more similar to humans than worms or flies, so data from mice should be more reliable
  2. Data from outbred mice should be more robust because it avoids potential effects specific to one specific genotype
  3. Lifespan extension in model X should lead to lifespan extension in model Y
  4. An intervention showing more systemic effects is more likely to have some effects in humans, or to translate to another model
  5. If the mechanism is known (if it works for the right reasons, rather than working for whatever reason) then the effect is more likely to be real
  6. Reversal of aging is easier to measure, more impressive than, and harder to attain than, slowing down aging.
  7. If the effect was observed in wild type mice (as opposed to a disease model) then the effect is more likely to be robust

These heuristics tend to be used in the context of the usual longevity interventions: small molecules, or overexpressing existing factors in that species. But as the field moves forward we'll start to do more interesting things:

  1. If a species ages slower in some way, and there is some data on the mechanism, expressing the relevant genes in e.g. mice could lead to the mechanism also working in mice.

Lastly, here is one more heuristic to consider, and the most relevant for reprogramming:

  1. If an intervention makes an old cell identical to a young cell, said intervention is very promising.

Aging of the organism is not just aging of the aggregate of cells that compose it, but if one solves the problem in a single cell, then that goes some way towards solving the problem in general.

Reprogramming is the only intervention that has so far being able to do this. No dose of rapamycin or VEGF or anything else! Reprogramming can take young cells, old cells (Lapasset et al. 2011), or senescent cells (See here), and make them into iPSCs, then back into the cell of origin, and this resulting cell as far as we have looked looks young. In addition to this data, there is also work on how this might be working: if one buys the idea that a significant contributor to mammalian aging is an increase in entropy in the epigenome, and that this is to be undone, we can't hope to manually undo this damage one methylation mark at a time, we need a system that will reset methylation back to what it was when the cell was young, and that system will very likely be derived from current work in OSKM. It's a departure from CRISPR-like approaches where guide RNAs are used to precisely edit a small number of sites. The number of methylation sites that changes with age is large, and it is impractical to edit the entire epigenome site by site: Instead by studying how OSKM works we will likely be able to reap the full benefits of full reprogramming but safely. In the span of a few years we moved from OSKM being a great way to induce tumors (Abad et al., 2013) to inducing tumor-free improvements in health in the papers linked above. In a few more years we will discover novel factors and safer ways to reprogram.

In short, OSKM is more promising than other modalities because we have a working demonstration, and some reasoning as to why it may work, of near-complete reversal of aging in the de-differentiation and re-differentiation protocol, and this proven upper bound is just not there for any other modality. It's important too to pinpoint what reprogramming does not do: DNA mutations would remain, as would ECM crosslinks or various intracellular aggregates that reprogramming might not get rid of. Evolution had to evolve a way to get rid of damage that accumulates with age so that babies are born young, but damage that can be diluted away doesn't need a fix if you're growing an embryo. Unfortunately for us adults, we can't as easily fix damage by dilution.

Altos Labs, NewLimit, Turn, or Retro are making a bet on I assume reasoning similar to what I have here. This reasoning is heuristic and the end result of all this money being poured into reprogramming may end up being just a very expensive proof that after all reprogramming can't be decoupled from oncogenesis and thus we need to abandon it.... but maybe they succeed. And even if they fail, I would be very surprised if in the process of getting there we don't learn new things about aging that we can then use to continue to make progress. Exciting times ahead!