How to evaluate neglectedness and tractability of aging research

This is the fourth post of a se­ries in which I’m try­ing to build a frame­work to eval­u­ate ag­ing re­search. Pre­vi­ous posts:

1. A gen­eral frame­work for eval­u­at­ing ag­ing re­search. Part 1: rea­son­ing with Longevity Es­cape Velocity

2. Aging re­search and pop­u­la­tion ethics

3. Im­pact of ag­ing re­search be­sides LEV


In the first sec­tion, I pro­pose a method to scout for im­pact­ful and ne­glected ag­ing re­search. This method is com­prised of two steps: Iden­ti­fy­ing what is nec­es­sary to achieve LEV and, among what is nec­es­sary, iden­ti­fy­ing what is most ne­glected. This differs from the Open Philan­thropy Pro­ject’s ap­proach of ig­nor­ing im­pact de­rived from Longevity Es­cape Ve­loc­ity. A pre­limi­nary eval­u­a­tion, made through in­clud­ing all re­search on the hal­l­marks and us­ing lifes­’s Re­ju­ve­na­tion Roadmap to iden­tify ne­glected pro­jects, leads us to iden­tify ge­nomic in­sta­bil­ity, telomere at­tri­tion, epi­ge­netic al­ter­a­tions, dereg­u­lated nu­tri­ent sens­ing, loss of pro­teosta­sis, and mi­to­chon­drial dys­func­tion as ne­glected and im­por­tant ar­eas of re­search. Other ne­glected re­search must be scouted in other equally im­por­tant ar­eas that have already been iden­ti­fied by Open Philan­thropy, such as im­prov­ing de­liv­ery meth­ods and de­vel­op­ing bet­ter bio­mark­ers.

In the sec­ond sec­tion, I take Open Philan­thropy’s and Aubrey de Grey’s stance about con­sid­er­ing in­ter­ven­tions tar­get­ing “ag­ing in gen­eral”, such as caloric re­stric­tion or met­formin, as hav­ing low tractabil­ity and im­pact. What re­mains af­ter this first skim­ming is trans­la­tional re­search fo­cus­ing on the hal­l­marks, ba­sic non-trans­la­tional re­search, and en­abling re­search, such as de­vel­op­ing new tools and de­liv­ery meth­ods. When pri­ori­tiz­ing in­side these ar­eas, tractabil­ity should be con­sid­ered only af­ter hav­ing first con­sid­ered ne­glect­ed­ness while try­ing to max­i­mize scope by look­ing at re­search that is nec­es­sary for reach­ing LEV. Other­wise, a rel­a­tively small gain in tractabil­ity would sac­ri­fice an ex­treme amount of im­pact and ne­glect­ed­ness. This is true be­cause the hard­est prob­lems in the field are of­ten the most ne­glected, but if they are nec­es­sary for achiev­ing LEV, they will be solved later, and by ac­cel­er­at­ing them, we can im­pact the ex­pected date of LEV the most.

A method for eval­u­at­ing neglectedness

In its medium in­ves­ti­ga­tion on the cause area of ag­ing, the Open Philan­thropy Pro­ject iden­ti­fied some sci­en­tific ad­vances that it be­lieves would provide years of healthy life ex­ten­sion but still within the range of nat­u­ral lifes­pans:

  • Prevent­ing the ac­cu­mu­la­tion of epi­ge­netic er­rors as­so­ci­ated with ag­ing or restor­ing more youth­ful epi­ge­netic states in cells.

  • Solv­ing the prob­lem of senes­cent cell ac­cu­mu­la­tion.

  • Rev­ers­ing stem cell ex­haus­tion.

  • Learn­ing how to use in­duced pluripo­tent stem cells (IPSCs) to re­gen­er­ate and/​or re­place tis­sues and or­gans dam­aged by ag­ing and ag­ing-re­lated dis­eases.

It has also iden­ti­fied re­search av­enues use­ful for the at­tain­ment of the goals stated above:

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.

By ex­plor­ing fund­ing and pro­jects in this cause area, it also found two spe­cific ne­glected in­ter­ven­tions:

We have a limited sense of the ab­solute and rel­a­tive ne­glect­ed­ness of the var­i­ous cat­e­gories of re­search dis­cussed in this re­port. How­ever, our sci­en­tific ad­vi­sors iden­ti­fied spe­cific un­funded pro­jects re­lated to the fol­low­ing themes:
- Un­der­stand­ing the mechanism(s) driv­ing re­gen­er­a­tion as­so­ci­ated with het­e­rochronic para­bio­sis: Ex­per­i­ments have in­di­cated that the blood of older an­i­mals can have dele­te­ri­ous effects on younger ones, and that the blood and or­gan func­tion­ing of younger an­i­mals can im­prove the func­tion­ing of old ones, though to date the hy­po­thet­i­cal in­crease in healthy lifes­pan has not been tested. Un­der­stand­ing the biol­ogy re­spon­si­ble for the ob­served effects might even­tu­ally lead to in­ter­ven­tions that ad­dress health prob­lems as­so­ci­ated with ag­ing.
- Aging and epi­ge­net­ics: Doc­u­ment­ing cor­re­la­tions be­tween tis­sue-spe­cific epi­ge­netic states and signs of ag­ing with a lon­gi­tu­di­nal co­hort study and/​or sys­tem­atic ex­am­i­na­tion of ca­dav­ers of peo­ple dy­ing at var­i­ous ages could yield valuable in­for­ma­tion that could lead to treat­ments to ad­dress ag­ing-re­lated health is­sues.

Open Philan­thropy’s way of pro­ceed­ing is a fruit­ful one: iden­ti­fy­ing gen­eral im­pact­ful av­enues and then search­ing for spe­cific un­funded and un­der­funded pro­jects.

If im­pact is mea­sured in DALYs saved at the end of life, or mild life ex­ten­sion, then this method of pro­ceed­ing could be op­ti­mal. Nonethe­less, I pro­pose an­other method that makes more sense in light of the mea­sure of im­pact that I pro­pose in the first post of this se­ries: QALYs saved by mak­ing Longevity Es­cape Ve­loc­ity come closer.

Open Philan­thropy dis­misses the pos­si­bil­ity of rad­i­cal life ex­ten­sion in the next decades, but the timeline in which rad­i­cal life ex­ten­sion will hap­pen doesn’t im­pact the mea­sure of im­pact that I pro­pose. More im­por­tantly, the or­ga­ni­za­tion ex­presses doubts about the de­sir­a­bil­ity of in­definite life ex­ten­sion and its rele­vance for cost-effec­tive­ness analy­ses:

We think the best case for this cause in­volves the prospect of healthy life ex­ten­sion within the range that some hu­mans cur­rently live.
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.

Un­like Open Philan­thropy, I think that the ma­jor­ity of the im­pact of ag­ing re­search comes from mak­ing the date of LEV come closer and from the con­sid­er­a­tions about LEV in gen­eral ex­plained in my first post. The rea­sons for this should be clear by read­ing the first and third posts, which are re­spec­tively about the im­pact com­ing from LEV and the im­pact com­ing from pre­vent­ing DALYs due to age-re­lated dis­eases.

Re­gard­ing Open Philan­thropy’s con­cerns about the de­sir­a­bil­ity of “in­definite” life ex­ten­sion: Po­ten­tial “en­trench­ment of power and cul­ture” is a neg­ligible in­con­ve­nience if com­pared to the 36,500,000,000 QALYs saved by mak­ing LEV come closer by just one year. Th­ese figures come up by es­ti­mat­ing the length of a life af­ter LEV at 1000 years, al­though the pos­si­bil­ity of it be­ing “in­definite” is un­de­ni­able. I think that it’s also not clear if Open Philan­thropy’s con­cern would be a new prob­lem at all, given that power, in the form of wealth or not, can already be passed from gen­er­a­tion to gen­er­a­tion. This con­cern is also offset by con­sid­er­a­tions about ac­cu­mu­la­tion of knowl­edge that would be use­ful for sci­ence and other pos­i­tive sides of elimi­nat­ing ag­ing dis­cussed in my pre­vi­ous posts. It could also turn out to be ir­rele­vant due to other dis­rupt­ing tech­nolo­gies com­ing along be­fore and af­ter LEV is at­tained.

In prin­ci­ple, ig­nor­ing a source of im­pact is go­ing to pro­duce wrong re­sults, since op­ti­miz­ing for one also in­fluences the oth­ers.

Keep­ing in mind the met­ric of “QALYs saved by mak­ing LEV come closer”, what is a bet­ter method of eval­u­at­ing ne­glected av­enues? Here is the strat­egy I pro­pose:

  • Iden­tify what is nec­es­sary to achieve LEV.

  • Among what is nec­es­sary, iden­tify what is most ne­glected.

This method would cause the most difficult prob­lems, which would be solved last if we didn’t in­ject more fund­ing, to be solved sooner. In this way, we would prob­a­bly im­pact the date of LEV the most. Un­like the strat­egy pro­posed by Open Philan­thropy, here, the fo­cus is on LEV, and this gen­er­ates differ­ent an­swers.

How do we im­ple­ment the two steps above? Knowl­edge of the field is nec­es­sary. In a pre­limi­nary way, we could con­sider the gen­eral av­enues iden­ti­fied by Open Philan­thropy as nec­es­sary ad­vance­ments. On their own, they are cer­tainly in­com­plete, and we may ac­tu­ally want to in­clude each one of the hal­l­marks of ag­ing as de­scribed in the name­sake pa­per. The causal­ity and in­terfer­ence that the hal­l­marks have on each other is not yet com­pletely un­der­stood, but many of them seem to be in­di­vi­d­u­ally im­por­tant enough to re­quire a dis­tinct solu­tion in or­der to achieve LEV, if not mul­ti­ple dis­tinct solu­tions per hal­l­mark.

Among the hal­l­marks iden­ti­fied, how do we iden­tify the most ne­glected? We could look at un­funded pro­jects, as Open Philan­thropy has done, or we could search the liter­a­ture by key­words and look at which hal­l­mark has less re­search go­ing on about it. An ini­tial good source for iden­ti­fy­ing the most ne­glected is also the Re­ju­ve­na­tion Roadmap, which is cu­rated by the Life Ex­ten­sion Ad­vo­cacy Foun­da­tion. The most ne­glected should be the hal­l­marks in the least ad­vanced stages of re­search. In the­ory, this could tell us that they are just difficult in­stead of ne­glected, but most of the time, these two things go hand in hand. By look­ing at it, we im­me­di­ately iden­tify that two out of four of the gen­eral im­pact­ful ar­eas iden­ti­fied by Open Philan­thropy (cel­lu­lar senes­cence and stem cell ex­haus­tion) are ac­tu­ally in the most ad­vanced stages of re­search. This shouldn’t be a sur­prise, since they are, right now, the most fash­ion­able and well funded in the field. Stem cells are prob­a­bly the most re­searched topic among the things in the roadmap, and re­search on senes­cent cells has ex­ploded in re­cent years, hav­ing seen a surge in pri­vate in­vest­ment on the or­der of hun­dreds of mil­lions of dol­lars (most no­tably Unity Biotech­nol­ogy).

As men­tioned, the most ne­glected prob­lems seem to be the most difficult. This is usu­ally true, be­cause they are too risky to pur­sue for pub­li­cly funded re­search and too early stage for pri­vate in­vest­ment. How­ever, since they will be the ones that will be solved later in time, they are the ones that will con­sti­tute the last bar­ri­ers for achiev­ing LEV. There­fore, if ac­cel­er­ated, they will ac­tu­ally bring LEV closer in time.

If we look at the Re­ju­ve­na­tion Roadmap, we can iden­tify these as the most ne­glected ar­eas: Ge­nomic In­sta­bil­ity, Telomere At­tri­tion, Epi­ge­netic Alter­a­tion (rightly iden­ti­fied by Open Philan­thropy), Dereg­u­lated Nutri­ent Sens­ing, Loss of Pro­teosta­sis, and Mi­to­chon­drial Dys­func­tion.

But how to eval­u­ate the most ne­glected top­ics not de­scribed in The Hal­l­marks of Aging, such as im­prov­ing de­liv­ery meth­ods or de­vel­op­ing bet­ter bio­mark­ers? Open Philan­thropy rightly iden­ti­fied these as im­por­tant top­ics, and they are prob­a­bly nec­es­sary for reach­ing LEV, es­pe­cially con­sid­er­ing that generic ther­a­pies that, to­gether, would plau­si­bly ad­dress al­most ev­ery hal­l­mark in­volve so­matic gene ther­a­pies that are cur­rently un­available. In this case, the strat­egy of look­ing for im­por­tant un­funded pro­jects, cou­pled with a similar ap­proach as the one we use for the hal­l­marks (search­ing how many pa­pers there are about each sin­gle topic) could be a good strat­egy. Again, ex­per­tise in this field is needed.

What is more tractable in ag­ing re­search, and why tractabil­ity starts to lose value af­ter a cer­tain point

There seems to be one key con­sid­er­a­tion about tractabil­ity in ag­ing re­search: ad­dress­ing ag­ing in gen­eral is much more difficult than adopt­ing a di­vide et im­pera ap­proach. Quot­ing Open Philan­thropy’s piece:

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).

Such in­ter­ven­tions tar­get ba­sic mechanisms of ag­ing that are the cause of the dam­ages of ag­ing. Similar ap­proaches are drugs that mimic caloric re­stric­tion, or that seem to af­fect mul­ti­ple metabolic path­ways re­lated to ag­ing, such as the drug met­formin. Th­ese kind of drugs have small effect sizes, and they de­lay the on­set of age-re­lated dis­eases. They are difficult to un­der­stand due to the in­tri­cacy of metabolic path­ways and the many un­knowns about metabolism in gen­eral. Ad­dress­ing ag­ing by “tin­ker­ing” with metabolism is cur­rently not a tractable av­enue. In fact, Open Philan­thropy fo­cuses on re­search av­enues out­side of this area. This is also the ar­gu­ment that biogeron­tol­o­gist Aubrey de Grey makes in favour of the “main­te­nance ap­proach” to ag­ing: ad­dress­ing its ba­sic dam­ages (hal­l­marks) us­ing pe­ri­odic main­te­nance, such as by ad­dress­ing stem cell ex­haus­tion, us­ing senolyt­ics to get rid of senes­cent cells, etc. in­stead of fo­cus­ing on the path­ways that origi­nally led to them (the seven dam­ages of his SENS ap­proach are very similar to the nine de­scribed in The Hal­l­marks of Aging). The main­te­nance ap­proach also the­o­ret­i­cally pro­vides re­ju­ve­na­tion—re­moval of dam­age—in­stead of just slow­ing down its ac­cu­mu­la­tion.

Start­ing from this com­mon ground, we can fo­cus on what re­mains:

  • Trans­la­tional re­search fo­cus­ing on the hal­l­marks.

  • Ba­sic non-trans­la­tional re­search.

  • En­abling re­search, such as de­vel­op­ing new tools and de­liv­ery meth­ods, even if it isn’t strictly clas­sified as ag­ing re­search.

What is more tractable in­side these three cat­e­gories? This de­pends on the spe­cific pro­ject eval­u­ated. Try­ing to lo­cate sub-sub­ar­eas of tractabil­ity in ad­vance is prob­a­bly not that use­ful.

How­ever, should we re­ally be fo­cus­ing on tractabil­ity be­yond the first skim­ming? I be­lieve that now these two met­rics should have pri­or­ity:

  • Ne­glect­ed­ness, which cor­re­lates with hard­ness.

  • How nec­es­sary the given re­search is for LEV, which drives im­pact.

Tractabil­ity should be con­sid­ered af­ter pick­ing the most ne­glected and nec­es­sary pro­jects. Here’s why:

As ob­served ear­lier, in this area, ne­glect­ed­ness and tractabil­ity seem to cor­re­late nega­tively with each other. This could have a few rea­sons: the more difficult a given re­search pro­ject is, the riskier it be­comes and its re­sults will be par­tic­u­larly far in the fu­ture. If a pro­ject is too risky and too slow, it will not at­tract pub­lic or pri­vate fund­ing and will not be gen­er­ally at­trac­tive to re­searchers. This is usu­ally the case for hard and am­bi­tious ba­sic re­search, which is too risky for pub­lic fund­ing and too early stage to be prof­itable for a com­pany. This cre­ates a land­scape in which harder prob­lems are ne­glected. The only way to fi­nance this kind of harder and long term re­search seems to be through philan­thropy.

Keep­ing in mind the met­ric of im­pact of “mak­ing LEV come closer”, it makes more sense to fi­nance hard and ne­glected prob­lems if they are nec­es­sary for achiev­ing LEV. Th­ese kind of prob­lems will be solved later than oth­ers, there­fore ac­cel­er­at­ing their solu­tion has the most im­pact on LEV’s ex­pected date, which is the largest source of im­pact of ag­ing re­search by far.

Be­cause of the na­ture of the field, if we fo­cused more on tractabil­ity, we would have lit­tle gain of it (vi­su­ally, we would add some of it on top of the one gained by the skim­ming already performed), and, in turn, we would avert some more short-term DALYs. How­ever, by mak­ing this choice, we would lose an ex­treme amount of im­pact, and we would make a big sac­ri­fice in ne­glect­ed­ness, ren­der­ing the trade­off not worth it.

In this area, we will rarely see ne­glected prob­lems that are also very tractable, and while hunt­ing for giv­ing op­por­tu­ni­ties, we should be on the look­out for pro­jects that are very hard, risky, long term, and un­der­funded but, at the same time, nec­es­sary. By go­ing against the sub-op­ti­mal com­mon prac­tice caused by the risk-averse mind­set of the field, we can op­ti­mize re­search.


Cross­posted to LessWrong.