102 replies to this topic

[jaydfox]

Rate of replenishment required for various stem cell lines. Blood, skin, gut, etc. Prometheus argues that the rate in the gut is too high, and that without telomerase, the stem cells in the gut will be used up in far less than the 10 years that de Grey suggests.

This has turned into a battle of logic versus studies. Logically, the stem cells in the gut must be turning over every 24-72 hours, since that's how often the cells on the gut lining have to be replaced.

de Grey sidesteps this one:

> do you dispute that the mucosal surface of the GI tract turns over with a
> frequency of 24 - 72 hours?

If you mean the cell division rate of the stem cells that give rise to the mucosal surface (which is the relevant rate), yes I do.

de Grey didn't answer the question of whether the mucosal surface of the GI tract turns over every 24 hours. He answered with his educated opinion on whether the stem cells turn over that often. There remains an unsolved connection between the cells lining the GI tract and the stem cells that give rise to those cells. If indeed the cell lining turns over every 24 hours, and the stem cells turn over once a month, then there is an obvious disconnect here. de Grey sidestepped the issue.

de Grey turns to a study that, by his interpretation, indicates that gut stem cells do not divide any faster than skin or blood stem cells. It's a difficult study to ignore. It says nothing about the turnover rate of the GI tract lining. However, it does very strongly imply that the stem cell base lasts as long as the blood and skin stem cell lines.

I say stem cell "base", because we can't tell from this study if the original stem cells in the GI tract are indeed holding out as long as the blood and skin stem cells. The turnover rate (if indeed 24-72 hours) implies that the GI tract stem cells should be exhausted. So, we are left with multiple possibilities.

(1) The turnover rate is NOT 24-72 hours. This would require throwing out all previous studies that indicate this. Not a pretty option.
(2) The turnover rate does not reflect the division rate of GI tract stem cells. In other words, the stem cell does not have to divide every time a new cell is created on the "mucosal surface of the GI tract". I could offer my own hypothesis on how this works, but I'll let the experienced biologists address this one.
(3) The GI tract stem cells are being replenished from a secondary source. Actually, de Grey hinted as much:

One possibility that has yet to be excluded is that crypts are in fact maintained by the occassional sequestration of a blood stem cell from the circulation.

Personally, given the evidence of the study, I'm leaning towards (2) or (3). At any rate, if the study can be trusted, and if the same biology applies in humans, then I don't think we need to worry about the gut stem cells being depleted in 10 years. Prometheus? What is your interpretation of the study that de Grey keeps referencing?

[jaydfox]

By the way, I'm still working my way through Potten's paper, so I apologize if I'm asking questions that were already answered.

[jaydfox]

"Sub-SENS". de Grey summarizes it rather succinctly, but the issue is far more complex in my opinion. I think de Grey and Prometheus need to come to an agreement on what that term means, to facilitate further debate.

If I have appeared negative about any ideas of others (whether they be alternative ways to do as well as the therapies I currently advocate or whether they be "sub-SENS" therapies that are not claimed to be able to get us to escape velocity)...

Okay, "sub-SENS" can be taken to mean a lot of things. So I would like to start with the simplest definition of "sub-SENS" and its correlate, "SENS-worthy":

sub-SENS: "therapies that are not claimed to be able to get us to escape velocity."
SENS-worthy: "therapies that are claimed to be able to get us to escape velocity."

A note of technical clarification. "Escape velocity" in this context refers to getting us to the point where medicine is advancing fast enough to stay ahead of mortality rate increases, preferably for middle-aged people (at least some arbitrary age, e.g. 40 or 55). In other words, should medicine stop advancing (not regress, just cease to get better), then escape velocity is lost. Escaping the mortality well is more complex than escaping the gravity well, in that escaping gravity can be accomplished with a single large impulse, whereas escaping mortality requires constant "thrust", i.e. improvements that reduce our non-zero mortality rates.

Another note of clarification. a single therapy (such as moving mtDNA to the nucleus) may not in itself be SENS-worthy. That is, taken by itself, such a therapy will not get us to escape velocity. Therefore, it is really a suite of techniques that is SENS-worthy, and individual components are called SENS-worthy if, by removing them, the remaining suite is insufficient to achieve escape velocity. In other words, an individual component may not be sufficient to achieve escape velocity, but it is necessary for a given suite.

Okay, if de Grey and Prometheus cannot agree to these definitions, then we need to come up with definitions that they both agree to. Without such agreement, debate of what is SENS-worthy is next to impossible.

Should they agree, then a side effect of this is that the definitions above open up the possibility of a separate suite of techniques which is SENS-worthy, but may or may not include all seven of de Grey's components of his SENS suite. It also leaves open the question of whether de Grey's suite of seven things itself is SENS-worthy, without additional components.

[jaydfox]

One final note: practical considerations MUST be taken into account. A suite may be SENS-worthy from a theoretical perspective, meaning that if applied to a small enough control group (say, anyone with $10 million), it will be sufficient to get that group to escape velocity.

However, if for practical reasons (e.g. facilities, human resources, etc.) it is not possible get at least some percentage of the human populace to escape velocity, then the technique loses points big time.

If another SENS-worthy suite may cost more to research, take 5-10 years longer, but it will be available to a much larger segment of the population, then this fact MUST be taken into consideration.

Alternatively, if another suite (such as one including a plan for nuclear DNA maintenance, e.g. through "overexpresison of key DNA repair/maintenance (kDRM) factors") could cost less, be researched faster, be available to a larger segment of the population, but it is not as effective as de Grey's 7 points, this is irrelevant if it gets us to escape velocity sooner. That's a big "if". But remember, escape velocity as defined in this debate (which, in all fairness, I haven't waited for either party to accept this definition) is not curing aging, it's getting us to the point where medicine is advancing as fast as or faster than mortality rates.

After all, de Grey's 7 points are not meant to be the final step in biomedical advancement, and he admits as much. Therefore, if a less-thorough suite brings a greater percentage of the world's populace to escape velocity, and hence saves more lives, then further advancements (including a more thorough suite including de Grey's seven points) can be the second generation SENS, thus preserving escape velocity.

[ag24]

Hi all -- got an unexpected spare moment and a wireless connection.

Jay: well done, you have thoroughly understood what I've been saying about allotopic expression. Your new question about which mitochondria in a given cell receive the protein is an excellent one. Answer: Most nuclear-coded mitochondrial proteins (including all those that are subunits of respiratory chain complexes) are directed to mitochondria by short amino-acid sequences attached to the start of the protein, which are removed after import. It was established a decade or two ago that these targeting sequences can be attached to any old protein and cause it to be imported into mitochondria (so long as it's not too hydrophobic). Exactly how an individual mitochondrion activates and deactivates its import machinery to turn import on and off is not well understood, but it is clear that when import is occurring it is not specific for a subset of mitochondrial proteins; rather, everything nearby that has the signal sequence is imported.

Stem cells: right, there is a key thing you don't know about the cell division dynamics of tissues that are maintained from stem cells. In all such tissues, your possibility (2) is true, and in a big way. The stem cells themselves divide relatively rarely, giving rise (on average) to one daughter that is still a stem cell and one that is on the first step to becoming a differentiated cell. That latter cell then divides several times, and each time both daughters are a bit more differentiated than the mother was. So you end up with a big population of new differentiated cells for each individual division of a stem cell. The details of this (such as how many of these "transit amplifying" divisions there are) can of course vary hugely from one tissue to another, and also are very hard to analyse directly, hence the fragile assumptions Potten had to make (to which I briefly referred earlier).

SENS/subSENS/escape velocity: very well put. Your definition of a suite of SENS-worthy things is spot on. You're also quite right that a SENS-worthy suite can (in theory and very probably in practice) be made SENS-worthy sooner or more cheaply by the addition of components that would be unlikely to make the difference between the suite bein g SENS-worthy at all versus not being. I focus on the therapies that I see as having a fair probability of being make-or-break for escape velocity, but that's only because I can't focus on everything.

Prometheus: my position is that the hardest thing about allotopic expression is the delivery of the modified genes, not the identification of how they should be modified prior to delivery. I've understood you to be identifying aspects of allotopic expression that you believed might be even harder to get right than delivery, and I agree with you that if such aspects existed then there would be a case for pursuing a less effective alternative since it may be perfected sooner. But if (as I claim) no such aspect of allotopic expresion exists, then improving DNA repair is not appreciably harder than allotopic expression, because it also requires gene delivery. Since improving mtDNA repair is unequivocally less effective than obviating mtDNA damage in terms of the retention/restoration of respiration to cells that receive the DNA in question, this means I think pursuing allotopic expression gives better bang for the buck. The same applies in my view to nuclear DNA, for the reasons I've outlined in previous posts in this thread -- slowing damage down is inherently less effective than repairing it, so if we can do both, great, but repair/obviation of damage may not be much harder so should be the main focus. If we add to this the point I mentioned several posts ago that just adding extra doses of one or two DNA repair proteins may not in fact improve DNA repair (because the quantity of these enzymes is unlikely to be limiting, rather their fidelity is) then we must accept that DNA repair enhancement is even less clearly preferable to pursue its obviation.

As to non-cancer nuclear DNA damage, you make a good point re senescent cells, but it would be unjustified to broaden this until/unless it were at least provisionally shown that other types of DNA damage cause actively toxic effects whereby rare affected cells can disproportionately harm their environment. Even for senescent cells the current paradigm (developed by Campisi) is that the toxicity only matters because it promotes carcinogenesis in nearby cells. Cell death as a result of DNA damage is not the accumulation of DNA damage but its removal. Other types of gene expression change, as I've said, do not seem to be a result of DNA damage.

As to altering SENS to include other things, removing the stem cell part of WILT, etc: the partitioning of rejuvenation therapies into the seven existing strands is not claimed to be the only possible one, merely a good one to clarify what's needed overall. Adding "improve DNA repair" is no more appropriate than adding "reduce free radical production" or "reduce glycation" -- these are ways to retard rather than reverse damage accumulation and would make it even harder than it already is for me to communicate the fundamental superiority of partial repair over partial pre-emption.

[jaydfox]

Even for senescent cells the current paradigm (developed by Campisi) is that the toxicity only matters because it promotes carcinogenesis in nearby cells.

I'm not familiar with Campisi, so excuse my ignorance. But it seems like such a statement applies mainly to what might occur in a normal lifetime, since that's all the data we have to go with, right? Can such a blanket statement be applied to cells that have accumulated two or three lifetimes worth of damage, especially since such damage will be occurring at an increasing rate with "age"? Assuming that tumor suppressors would act on senescent cells as much as precancerous one, I guess we could turn up tumor suppressors and rely on stem cell replacement and replenishment, a la WILT/stem cell transplants. (e.g. p53 seems to make the apoptosis switch more of a hair-trigger, from a recent study abstract I read, decreasing cancer rates, but leading to earlier dysfunction through cell loss.) But it's still not addressing the issue of how "bad" non-cancerous DNA damage can be with accumulation.

As to altering SENS to include other things, removing the stem cell part of WILT, etc: the partitioning of rejuvenation therapies into the seven existing strands is not claimed to be the only possible one, merely a good one to clarify what's needed overall. Adding "improve DNA repair" is no more appropriate than adding "reduce free radical production" or "reduce glycation" -- these are ways to retard rather than reverse damage accumulation and would make it even harder than it already is for me to communicate the fundamental superiority of partial repair over partial pre-emption.

From a purely theoretical standpoint I'm somewhat inclined to agree. Given adequate resources and treatments administered as often as necessary (be it every ten years or every other year), we could keep a small study group alive for quite some time, assuming the seven deadly things are in fact comprehensive.

But we're not just trying to sell a theoretical solution (although at this point, a theoretical solution is better than no solution, so please accept my admiration for putting forward a theoretical solution). We must also try to sell a pragmatic solution. We don't need to worry about researching proper exercise, diet, and supplementation, because the market is already doing that. We don't even need to push CR-mimetics, because the market is doing that as well (though to what degree I am not fully aware).

However, increasing expression of kDRM factors (in proper ratios, if that matters) is something that I don't see a lot of research on, except with respect to CR research. Harold has pointed out this shortcoming, and I have yet to see that it will be properly addressed in the near term (since the technology already exists, and the costs with Drosophila would be relatively low, we should be proceeding now, allowing us to focus on the other 7 items when society comes around and the technology base matures). While it may not be an essential component to include in SENS from a theoretical standpoint, any long-term strategy's success will depend on ensuring that important short term strategy's are pursued today.

Given what information I've seen presented, I believe that if we started today on researching "controlled" overexpression of kDRM factors, we could increase the effectiveness of SENS through one or both of the following:
1) Decreasing the frequency which the various SENS treatments will need to be performed/refreshed, thus increasing availability and reducing costs.
2) Allowing escape velocity with most, but not all of the seven tasks of your SENS accomplished.

So although such a path may not be necessary for SENS (a point which I'm not completely convinced of yet, but I remain open to the continuing debate) to work in theory, in all practicality, it would be in your best interest to ensure that such research is conducted. It doesn't need to be done as part of the IBG, as long as it gets done by somebody.

If it were incorporated into SENS, then that in itself would make a statement which might help encourage the scientific establishment to work on the problem by itself, thus obviating the need for the eventual IBG to focus on it. Without incorporating it, I fear it may send a message that it's not worth working on at all.

At any rate, I fear that not incorporating it into SENS has allowed a majority of ImmInst regulars to oppose the creation of a Fly Prize, because they view it as counterproductive to the goal of SENS. In my opinion, there exists a synergy, and a Fly Prize would add much more benefit than any harm that might be perceived. And frankly, besides the very small potential for a small drain in donations to the M Prize (an overstated fear), as well as extra work for ImmInst leadership (which I would gladly bear as much of as I can), I don't see what harm can come of it. And there could be so much to gain.

You have said in the past that, if such a prize could be established, and if it could not be won "boringly", then the small cost in relation to the small chance of benefit was something that you would not oppose. I took that as a pretty decent endorsement, but the community here feels otherwise. That's why I've constantly been trying to drive home the point whenever I can, that Drosophila is very cheap, very short-lived, very prolific, and very small, allowing massive testing on a scale completely impractical in mice. Recent studies have even highlighted this fact, with one accomplishing "shotgun" testing of more than a dozen candidate genes (not of random genes, mind you, but carefully picked candidates). And Harold has pointed to several resources, reports, and studies explaining the genetic relevance of Drosophila and the existence of a high proportion of genetic orthologs.

I'm a little scatter-brained myself, so perhaps all this effort has not been perceived as coherent, but I hope you can appreciate why I feel that nuclear DNA damage is being unadvisedly ignored by the life extension community. I strongly believe that it gives us a better bang for the buck now than research into some of the other areas of SENS (which are waiting for better technology to be developed). The MPrize probably won't yield much in the way of results for the better part of a decade, precisely because of the technological hurdles to be overcome. A Fly Prize could yield results in a few years, results which could be appropriated by the general scientific community, freeing those resources to work on other of the aspects of SENS with a now more-mature technology base.

But laying aside prizes, the IBG would require vast resources and technology yet to be developed. A smaller firm, focussed on kDRM factor expression, could be started with today's technology and a fraction of the resources, and help effect escape velocity perhaps years ahead of a scenario without such research being performed. And such a firm would be a foundation upon which to build the IBG. Or, should the funding and resources for the IBG come together in the next couple years, it could simply be rolled into such an institute from the ground up, as it would be one of the more mature fields to begin with.

[jaydfox]

Even with the scheme of partial stem cell differentiation you mention it would still exhaust the stem/pro-stem/pro-pro-stem etc. pool within 2 months if the mucosa were being replaced every 24 hours due to the absolute 50 or so mitotic limit. This is the greatest impediment, as you say in your paper, to implementing WILT and unless another solution presents itself for stem cell reseeding you will need to come up with a different strategy for dealing with chromosomal mutations.

My personal theory on this is that the original stem cell creates a "pro-stem cell", or whatever we're calling it. This pro-stem cell will then be exhausted in two months, per your logic. Then the original stem cell will have to divide again, producing a new pro-stem cell, which will have slightly less than two months (48 divisions left rather than 49). When that pro-stem cell is exhausted, the original stem cell divides and produces a new pro-stem cell, which has 47 divisions remaining before exhausted.

I have no idea if this is how it works, but it's certainly a simple enough system that can bypass the 50-division rule, and give in effect 49+48+47+... = 49*25= = 1225 divisions. Even at one division a day, with an initial 40-division limit, it would allow a mouse gut stem cell to last most of its lifetime.

But I'm inclined on this one to rely less on logic and more on the study de Grey pointed out (has it been duplicated/validated with variations?), and that study seems to favor de Grey's position. We don't have to understand why the gut stem cells hold out as long as blood and skin stem cells; we only prove whether or not that statement is true. If it's true, then we let the basic science researchers scramble to explain it, but we move on to more important matters. Which is the position de Grey seems to be taking, as he hasn't really offered much explanation as to why the gut stem cells hold out.

[Matt]

oh thanks for the link, A lot of posts since I last checked that forum

[ag24]

Jay wrote: "I'm not familiar with Campisi, so excuse my ignorance. But it seems like such a statement applies mainly to what might occur in a normal lifetime, since that's all the data we have to go with, right? Can such a blanket statement be applied to cells that have accumulated two or three lifetimes worth of damage". Sure -- it's virtually a given that new things will turn up as we reach ever-greater ages. First things first though.

Jay wrote: "We don't need to worry about researching proper exercise, diet, and supplementation, because the market is already doing that. We don't even need to push CR-mimetics, because the market is doing that as well (though to what degree I am not fully aware). However, increasing expression of kDRM factors (in proper ratios, if that matters) is something that I don't see a lot of research on, except with respect to CR research. Harold has pointed out this shortcoming". Indeed -- and I pointed out that the absence of much work on this is not because the benefits of enhancing DNA repair are non-obvious (as the benefits of putting bacterial genes into our cells may be, for example), and thus, by elimination, that it is probably because the obvious ways to actually implement it have not worked. There is no shortage of top DNA damage/repair specialists in gerontology, and it's no accident that one of the very best, Vilhelm Bohr, is an associate editor of Rejuvenation Research. Look him up in PubMed and then decide whether this area is really being ignored.

Jay wrote: "If it were incorporated into SENS, then that in itself would make a statement which might help encourage the scientific establishment to work on the problem by itself, thus obviating the need for the eventual IBG to focus on it. Without incorporating it, I fear it may send a message that it's not worth working on at all." I think that's going too far. By that reckoning I should include in SENS everything that will increase lifespan of a lot of people, whether it be vaccine research, nicotine addiction research, etc. SENS has to be somewhat focused in its scope in order to communicate anything.

Jay wrote: "At any rate, I fear that not incorporating it into SENS has allowed a majority of ImmInst regulars to oppose the creation of a Fly Prize, because they view it as counterproductive to the goal of SENS." Now, this is a different matter entirely. As you say, I made my position clear - support for any fly prize that could not be won boringly. I also pointed this community to the researchers who could advise better than I on the technical details. If that was as ineffective as you say, well, I wasn't following the discussion here but all I can say is that I refuse to be classified as part of the problem.

I see no need to comment forther on gut stem cells as Jay is doing a great job of communicating the potential of appropriate schedules of division of transit amplifying cells to allow stem cells to divide rarely. There is plenty of literature on this.

Prometheus wrote: "upposing that it were possible to technically achieve this feat then the next question to answer is how will this result in a human therapy. That is, how will these modified cells - and I assume they will have to be stem cells - be introduced to the patient? And how do you contrast such a method of cell delivery with using adenoviruses to introduce therapeutic genes (ala DNA repair)?" Delivery of allotopic genes is the same as delivery of genes for DNA repair, whether it be to stem cells ex vivo or by somatic gene therapy.

Prometheus wrote: "Before I embark on the wonders of methylation is there a reason you do not mention it?" It should not take anyone long to discover that I mention it on my site and note that the same logic which implies that nuclear mutations matter only for cancer equally implies that epimutations also matter only for cancer.

Prometheus wrote: "with the mitochondria of fertilized oocytes potentially immortal, and clearly capable of enormous innate self-repair (certainly enough to keep them going for countless generations) should we be not looking at how we can coax somatic cell mitochondria out of their limited lifespan?" Only if we don't already know that the limited lifespan of somatic cell mitochondria is a consequence of the function of those cells -- and it turns out that we do know that. The cell types which are affected by mtDNA mutations are predominantly postmitotic ones. Oocytes are thoroughly purified of mutant mtDNA by the cell division that goes on in oogenesis together with the respiratory challenge that is intrinsic in follicle maturation.

Prometheus wrote: "From cloning experiments we have been able to see that the nucleus from a mature differentiated cell can be reprogrammed to become the nucleus of an embryo. This observation suggests that any cell can theoretically travel backwards in time developmentally to its very beginning. Experiments have shown that this process of altered gene expression, known as epigenesis, is due to altered methylation patterns of discrete DNA regions and that such patterns are reversible. Can this process be harnessed therapeutically to alter the fate of cells trapped in senescent or otherwise dysfunctional states? Not, of course, back to an embryonic state but to a pre-senescent, youthful state. Such an intervention would present the ultimate solution for the aged population by providing a bona fide reversal of aging. Scientists already are tackling cancer by targeting methyltransferases, the enzymes responsible for methylation to reverse a cancerous cell back to normal gene expression levels." Not so simple, unfortunately. Just targeting methyltransferases changes global methylation levels but cannot restore lost methylation patterns. It has some anti-cancer benefits, but not much. SCNT consists of a global resetting of methylation followed by the execution of a natural (and much more intricate than we are anywhere near understanding) program of establishment of methylation patterns appropriate for pluripotent and then multipotent stem cells.

[John Schloendorn]

Hi guys,
Sorry I am joining this only so late, and many thanks to all the participants! I have met my objective to learn a great deal from your debate, and I'll be happy to try and "sort some things out".

Maybe some classification is useful. I think it's clear to everyone that in order to achieve very long lives, WILT is a mitotic strategy. That is, it is deliberately reducing the lifetime of individual cells, but increasing their turnover, along with (hopefully) the organism's life span. Allotopic expression, on the other hand, is a purely postmitotic strategy, if WILT, or any other relatively rapid cellular replacement scheme is employed as well. (That is, cellular replacement in the broadest sense, including cell therapy, tissue engineering and transplantation.) No one will live a minute longer by having cells that could maintatin their mitochondrial proteins for hundreds of years, if these cells are replaced every decade anyways. I think this was made less than perfectly clear here, as well as on the SENS pages.
(The same holds for holds for enhancing nuclear DNA repair and epimutation repair. In the WILT scheme, telomere length determines longevity. I do not see how enhanced DNA repair could change that.)
Therefore, allotopic expression is needed only in tissues where rapid cellular replacement is out of the question, which is primarily the neuronal fraction of the brain. That means also, allotopic expression must rely on postmitotic gene therapy, with all its current problems and pitfalls. The involvement of mitochondrial dysfunction in many brain degenerative diseases makes allotopic expression particularly promising. What I also like about it is its straightforward implementation and its promise to rejuvenate its target organelle independently of the time of onset of the therapy.

We also should clarify some semantics about WILT: A general anti-cancer strategy is to replace chronologically old cells with young ones. This takes two things: A way to introduce fresh cells, and a way to ablate existing cells. Literally, WILT makes only reference to the latter (small WILT). But, in our casual language, the acronym is normally used to include both (big WILT).
The introduction of fresh cells is not the real matter of debate here. I think we all agree it is necessary. The matter of debate is the utility of small WILT as a cell ablation strategy. (I.e. the issue is not even as big as it may sound to some.)
So far, I would grant one major point to Prometheus, as long as only scientific arguemts are considered: It remains to be assessed by future experiment, how competitive small WILT is in comparison with other cell ablation schemes, such as maker-based tumor-specific ablation or unspecific chemotherapy. Small WILT is probably the most effective ablation strategy, but other cell ablation strategies, which are much less of a hassle, may prove sufficiently efficient. Small WILT may not be feasible due to ALT diversity and/or its genes' possibly critical physiological role. Thus, I would suggest to priorize the cell replacement part of big WILT over small WILT, unless there is a strong reason to believe that the cell replacement part will be developed in time, even without our stimulation. I am presently not qualified to assess this, but Aubrey provided some arguments that go in this direction.
Furthermore, in the footsteps of Prometheus last post, I have a sociological reason to keep WILT as a key SENS proposal at this time: WILT is just extremely cool! It's an eyecatcher. It makes people think "hmm, yeah, this guy even thought something up to defeat cancer, which is radically different from the continuously failing mainstream approaches, how ecouraging!" Clearer seperation of small WILT and cell replacement could help the reader to understand this tree of concepts.

All in all, it seems to me that Aubrey met his objective to show that
[quote]the challenges to allotopic expression and WILT that you mention are less daunting than you suggest, and why the challenges to the alternatives you mention are more daunting than you suggest[/quote]
Prometheus objectives were
[quote]1. Allotopic expression of mitochondrial genes is a proposed method of protecting the
mitochondrial genome from damage that would be technologically more difficult to implement than a more direct means of increasing DNA maintenance/repair such as overexpression of key DNA repair/maintenance genes.

2. It is possible to combat cancer without resorting to the ablation of telomerase expression in every cell of the body.

3. The chief assumption on which the implementation of WILT is based upon, namely the frequency with which certain cells in the body divide, is very likely to be wrong. [/quote]
I think the degree of success was 2>3>1.
2: (see above)
3: [quote]We don't have to understand why the gut stem cells hold out as long as blood and skin stem cells; we only prove whether or not that statement is true.[/quote]
I think it is likely through a low division rate along Aubrey's lines, but WILT may have to prepare for some surprises from the crypt.
1: I can't see any challenge that survived Aubrey's defense. I was not aware of that 1:1 stochiometry thing before. By pointing this out, you wiped my last doubts in the utility of allotopic expression.

Jay:
[quote]But as I must sometimes remind myself, I am not a biologist...[/quote]
Glad you overcame your shyness, Jay. I could think of someone here who managed to forget that he's not a biologist with some incredible success. So this would be a bad excuse for not daring to venture on thin ice. This is no criticism, I think your way of joining this debate is just right ;-) I encourage everyone attempt the same, not only in this thread but in your life as immortalists.

[quote]At any rate, I suspect he's more in support of de Grey's view[/quote]
Well suspected ;-)

[quote]increasing the rate and responsiveness of DNA repair to damage can be implemented by identifying the upstream regulators responsible for DNA maintenance and selectively overexpressing[/quote]
and Aubrey's counter:
[quote]what a review of the literature reveals is that very little has been published. I think we all know the fate of negative results in contemporary science.[/quote]
I clearly don't have the experience to weigh these points against each other, but I would suspect that a man who single-handedly created nearly all professional anti-aging initiatives out there, has.
One could also find commercially viable pharmacological solutions, rather than overexpression. This could be a way to get some venture capital in, once we have piled up enough fundamental knowlege. But is this type of fundamental research an IBG's job?

Jay:
[quote]Note that the DNA maintenance approach is not necessarily viewed as a way to cure aging. You can't stop all DNA damage. Well, some day maybe, but not soon.[/quote]
Barring a "chronometer" style breakthrough as it could be inspired by a fly prize. This could essentially be the answer to the question "how do germ cells do it?" If we had the money to do it without impacting the mouse prize, I'd be full for a fly prize.

Jay:
[quote]I'm not familiar with Campisi[/quote]
Familiarize yourself ;-) This is an excellent talk, with a revealing grand-scheme-of-things view.

Jay:
[quote]Can we ensure that each mitochondrion will get the proper amounts of the proteins that we are moving out of the mtDNA?[/quote]
If this question means something like if 50 subunits are needed, how do we assure one mito does not get 75 subunits, while another one gets only 25, then the answer is simple. We don't. For statistical reasons, distributions close to the average are just much more likely than distributions that are far away. This is ultimately due to the same forces that drive the universe towards ever increasing entropy, but I would recommend to google a little bit for introductory thermodynamics, which can be quite revealing about this kind of phenomena.

Prometheus:
[quote]You say it's a tough project. C'mon, do you realize how silly a statement that is coming from de Grey.[/quote]
My local carpenter here has a hand-written quote pinned to the wall next to his workbench, which goes roughly
[quote]The key to success is the readiness to avoid tough problems where possible, the will to tackle them where there is no other option, and the wisdom to tell one from the other.[/quote]

Aubrey:
[quote]This is a great example of what I say about the difference between the creativity of basic scientists and the creativity of engineers. For a scientist it is just really difficult to think in terms of factoring out unknowns, i.e. finding solutions that don't depend on those unknowns, because finding things out is the whole deal. For an engineer it's central to factor unknowns out, because finding things out is just a means to an end.[/quote]
and Prometheus:
[quote]it sounds arrogant. [/quote]
Aubrey is trying to teach you, and everyone who just WANTS to live an invaluable attitude here. The lack of this attitude in the sciences is the one reason for Reason's:
[quote]Serious efforts towards radical life extension comprise such a small fraction of total efforts - this is the real problem we must address[/quote]
From the beginning, I studied science as a means to an end, which is indefinite heath. Give me a compelling reason to believe that I cannot make a difference (such as achieve this goal for me), and I drop on the beach, right here, right now. (Well, at least for a while ) From this point of view, the greatest mistake one can make is to solve problems that are not actually required for the goal.
Btw, Reason, I'm a great fan of nearly anything you post. You have a wonderful bird's eye view thingy.

One thing about arrogance. When one happens to be right, and has a compelling reason to demonstrate this to others, then one has to sound arrogant by definition. At least between each other, we must not let such obviously hardwired emotions impair our productivity towards our common end.

Prometheus:
[quote]So I ask the question: with the mitochondria of fertilized oocytes potentially immortal, and clearly capable of enormous innate self-repair (certainly enough to keep them going for countless generations) should we be not looking at how we can coax somatic cell mitochondria out of their limited lifespan?[/quote]
Sure, good thing, how do we go about it? I mean, we would need a (preferably peer-reviewed) argument that this is more efficient and/or likely to succeed than allotopic expression.
This is my general piece of advice to anyone who thinks they have a productive life-extension idea. Publish it. For example in rejuvenation research. When it can stand the scrunity of peer-review, then you will have a very good stand in discussing it publicly in places like this.

Edited by John Schloendorn, 13 February 2005 - 02:50 AM.

[ag24]

Prometheus: you are again diminishing my ability to persuade myself that bothering to reply to you is a good use of my time. If you want to be constructive you might try harder to avoid the following, which are abundant in your latest posts:

- asking me and others to tell you things that you can trivially discover for yourself at PubMed, my website, or both;
- repeating over and over again reservations about SENS components or arguments for other approaches that have already been responded to without offering reasons why you think those responses are inadequate;
- accusing me or others of arrogance when we're just finding your tone counterproductive;
- using derogatory terminology like "SENS loyalists" to describe people whose goal is just the same as yours and mine - to reach escape velocity as fast as possible.

Perhaps you could try the strategy of re-reading your draft posts for such features before posting them. They're not hard to spot when you try.

[eternaltraveler]

Prometheus,

why don't you put together an alternative SENS list?

Furthermore after reading this thread I think that if both you and Aubrey were to take a step you might see your differences are not nearly as great as you make out. Many of the differences seem largely semantical (Aubrey agrees with many of the points you bring up, but simply doesn't believe they belong on the SENS list).

Are you against other parts of SENS besides WILT?

[John Schloendorn]

Recall that Aubrey maintains that the main outcome and consequently concern of chromosomal mutations is cancer. Do you agree with this position?

I have always avoided responding directly to this question, because I clearly don't know. I must admit that I am a bit curious, but I don't think it should be a high priority for me to form such an opinion. Can't that wait until we have working rejuvenation therapies? I'm saying I'm pushing for rejuvenation therapies based on cellular replacement in order to reverse the deleterious effects of any intracellular deterioration. It is the great strength of such therapies that they do not require us to resolve which kind of intracellular deterioration is responsible for which phenotypical outcome.

For example, the WILT related stem cell division problem in the GI tract and the allotopic related effect of altered regulation on mt genes in the nucleus.

I abstained from answering that question for the same reasons as above: I don't have an empirically validated, mechanistic explanation. I don't have a high priority to find one. The contemporary results are compatible with Aubrey's strategy. (Although in this particular case I have other problems with Aubreys strategy)

I was in fact surprised by your view that if a theory sounds "cool" it is convincing

Read again.

This is not a popularity contest on what may or may not impress the a public that is largely ignorant of science.

Yes, unfortunately, it is just that. We need someone's money to do the R+D we need, and one way to get it is by winning a popularity contest against the currently prevailing fatalism.

biologists will be looking for a strong scientific substrate from SENS

If we had such a substrate, then we would not need biologists to develop it. An alternative means to attract biologists is money and that comes, at least in a democracy, largely from popularity of one's goals.

What we have is a number of hypotheses that are largely founded on no direct experimental evidence whatsoever.

Sad but true. We have to be extremely open, creative and hard-working if we're to get anywhere from here.

"someone here who has forgotten he is not a biologist". If that was directed at me, as I suspect it was

Sorry that I'm not fully aware of your CV's details. I always thought you were a practising molecular Biologist. Of corse I was alluding to Aubrey, who started with a computer science background and dashed into the biology field at the moment he realized there was a chance to beat aging.

John, I think, you suspect far too much and read far too little...

I can't entirely disagree.

Edited by John Schloendorn, 14 February 2005 - 01:45 AM.

[jaydfox]

Whew! That took a while to get caught up. If for no other reason, I'd like to see this debate end soon (but on good terms, with both sides feeling edified and positive about our future direction).

I had an ordered, inter-related series of questions formed in my mind over the weekend, but I'm going to have to modify it in light of responses from de Grey, Prometheus, and John.

Okay, I'll start with John's comments, even though they were unanticipated, because they are germane to the questions I had formulated.

We also should clarify some semantics about WILT: A general anti-cancer strategy is to replace chronologically old cells with young ones. This takes two things: A way to introduce fresh cells, and a way to ablate existing cells. Literally, WILT makes only reference to the latter (small WILT). But, in our casual language, the acronym is normally used to include both (big WILT).
The introduction of fresh cells is not the real matter of debate here. I think we all agree it is necessary. The matter of debate is the utility of small WILT as a cell ablation strategy. (I.e. the issue is not even as big as it may sound to some.)

I was just going to get to this. This is exactly the essence, as I see it, and I will try to explain why.

Nuclear DNA damage is the single most important aspect of aging that we must contend with. Dr. de Grey even admitted as much, and of course we all should be able to tell by now that this is one of the central pillars of Prometheus's message.

What we have some disagreement over is they types of DNA damage, and the timeframes in which they'll matter, and the degree to which they can be controlled.

Dr. de Grey focuses remorselessly on cancer. Cell dysfunction and senescence seem to be of little concern to him. This view, I believe, would be complete folly if we did not have a way to ablate and replace those senescent and dysfunctional cells. Under the reliability theory, senescence and dysfunciton are of primary concern, equal in weight to cancer and only orderable in concern by the relative rates of cancer and non-cancer age-related deaths. In mice, cancer wins, but in humans, cancer has until recently been the secondary concern.

Even assuming that the reliability theory is just a cute, descriptive, wrong theory, senescence and cell dysfunciton are still very important without oblation. Given the level of cellular dysfunction and senescence in aged tissues (in a "normal" lifetime), and given their exponential increase (which may or may not be mediated by a WILT-less SENS), it seems only obvious that our concern of DNA damage should extend beyond just cancer.

But, de Grey doesn't strike me as a man of folly, and I must assume that WILT was intended to provide just such oblation and replacement. In something less than a typical human lifespan, cancer would be a primary concern, assuming that modern medicine can fix or treat senescence- and dysfunction-related diseases. In something far less than a human lifespan, say 10 years, then neither senescence nor dysfunction would be of concern, as with cancer.

So I'm satisfied that, given de Grey's 10-year replacement system (using, as John points out, WILT as the ablation engine, and stem cell reseeding as the replacement engine), SENS will work as described.

In theory. But we have a practical concern here.

If it costs $1,000 to do such a reseeding (a pitifully conservative estimate, most likely), and if 1 billion people receive such a reseeding every ten years, then we're looking at $100 billion a year in reseedings, not including malpractice lawsuits—there's no way that 100 million procedures a year are going to be done without tens of thousands of malpractice suits being launched, a good percentage of which will be legitimage.

So the whole argument that it's a waste of resources to invest in DNA repair becomes plain absurd, if such research cost a one-time $10 billion and could increase the reseeding period by even 20% (saving $20 billion a year indefinitely).

Granted, exercise and diet would probably be sufficient to extend that period 20%-30%. Supplements, pharmacologicals, etc., could add another 10%-30%. But those are a constant lifestyle change, with their inherent financial costs as well, and we know how well society can keep up with those. DNA repair, genetically programmed, is a one-time procedure, replenished at reseedings if necessary. (At what point I actually accepted the absurd idea of reseedings, without which we would die from telomere depletion, I don't know. I guess I still don't accept it, but I'm going along with it until a better long-term solution to the ablation problem is laid out in detail and peer-reviewed; I'm sure even de Grey would favor a better solution, but this is what we've got for now, so we have to go with it.)

And DNA repair offers a hope much greater than diet, exercise, and pharmacologicals (which typically aim to square the curve rather than truly lengthen it (with the exception of CR), as DNA repair would): regardless of its effects on tissue damage buildup (addressed by the other 6 SENS items), decreasing relevant net DNA damage by 75% across a wide range of input damage (e.g. not just slowing the initial DNA damage rate, but slowing the doubling rate of that rate) should allow as much as a doubling or more of the reseeding period, allowing longer telomeres to safely be inserted (up to the safety limit with respect to random malignant cancers; but those will be treatable in the rare instances they occur anyway, much more cost effectively than more frequent reseedings for the broader population; hence as long a telomere chain as cost-effectively possible should be used).

Even if we researched DNA repair in mice instead of flies, I don't think anyone here seriously thinks it would take more than $10 billion to research, when de Grey's price tag for all of SENS is less than that. But if we did start with flies, and compared in vitro micro-array genetic expression screenings in mice and flies before validating fly results in mice (to ensure a higher probability of genetic relevance), then a price tag under $100 million seems reasonable, and less than 1% of the money it could save (and thus the greater availability it can provide) once the treatments are brought to market.

But I digress. I actually had a rational point to make, so I will get back to it in my next post.

[eternaltraveler]

It is hard to argue with DNA damage being a central pillar of aging. I don’t think anyone is. What this debate appears to be about are methods of dealing with it. Prometheus wants to deal with this directly. Over expression of DNA repair enzymes, perhaps introducing new repair enzymes and such.

Aubrey desires to just skip over this dilemma. If a cell has lots of damage, get rid of it, and replace it with a brand shinny new cell.

Both strategies will undoubtedly be employed in the future. However our primary concern is what will get us the most bang from our buck now.

(Jay D. Fox)

If it costs $1,000 to do such a reseeding (a pitifully conservative estimate, most likely), and if 1 billion people receive such a reseeding every ten years, then we're looking at $100 billion a year in reseedings, not including malpractice lawsuits—there's no way that 100 million procedures a year are going to be done without tens of thousands of malpractice suits being launched, a good percentage of which will be legitimage.

Your points, Jay, are well taken, and it is a correct analysis. However, I cannot agree with your conclusions. Your conclusions, if I am not mistaken, imply that since it will cost more later, we should invest more now to save these future costs. This argument is seemingly difficult to argue with. The problem is we have very limited resources now. The extra hundred million in research you speak of does not at all relate to the extra 100 billion it will cost in the future.

The research you speak of would naturally get done just a few years into it as cost benefit analyses are completed (Hey, we can save money if we repair the DNA better). Right now though, people just need to believe it’s possible at all, and they need to see some kind of results.

(Prometheus)

Secondly: in looking at why aging occurs from an evolutionary perspective I was forced to look at the mechanism of evolution itself, which is mutation. Mutation is the key to evolution, as without a steady trickle of mutation a life-form will become unable to adapt to changing circumstances to its environment and could be threatened by extinction. So I noted that a certain degree of mutation would have to be favored by evolution to keep a genome sufficiently flexible. But mutation is another word for DNA damage. I wondered, could it be possible that genomic systems have evolved to take advantage of the inherent mechanisms of DNA damage and actually allow mutation to be induced? Do genomes surf on a wave of mutation? Of course they do - because they must. But is it in a sea of potential DNA damage? I recalled that when we want to create mutations in the lab we expose organisms to UV light or chemical mutagens that will damage DNA.

From an evolutionary perspective I certainly agree that aging and death is advantageous. I remember thinking the same thing myself years and years ago when I first saw the redwoods. They used to be very common trees, but because of their extreme lifespan the speed of their evolution would be quite slow. Now they exist in two pockets, one in Northern California, and one in the Sierra Nevada’s further south. (This is just pure conjecture on my part I should point out).

The problem is that it would have never been evolutionarily advantageous to evolve these super DNA repair enzymes we would need. Over expression of existing enzymes probably won’t do all that much. It would be like oiling your car every 1000 miles instead of every 3000. It certainly would help some, but nothing fantastic.

That brings us to having to engineer entirely new gene repair enzymes from scratch. That seems hard.

And there definitely are life forms on earth that live longer than us; trees, turtles, etc. But even though they might live even many times longer I would wager that our cells experience quite a bit more metabolism than they do in our time than they in theirs (so we’re unlikely to find these super DNA repair enzymes we need).

Do you think over expression of existing enzymes would help that much, or do you know of other naturally occurring enzymes or repair mechanisms that we could import into human beings?

[jaydfox]

The research you speak of would naturally get done just a few years into it as cost benefit analyses are completed (Hey, we can save money if we repair the DNA better). Right now though, people just need to believe it’s possible at all, and they need to see some kind of results.

Right. For submitting SENS to the general public, DNA repair may not be a necessary component to convince them that curing aging is possible. In that sense, smaller is better, to drive the point home that it's not terribly complicated.

But, we have a duty as well to the scientific community, and to policy makers.

I'm not suggesting that we divert $100 million in funds from WILT or lysosomic ensyme research into DNA repair. Frankly, as you admit, we don't even have $100 million to divert. But DNA repair needs to be mentioned on its own, and pursued if and when possible.

It's not enough for someone to come forward and present a "cool" plan to cure aging that captures public imagination. Eventually, funds will materialize, public support will be backing us. And at that point, I believe we will need a comprehensive plan to make SENS available as soon and as cost-effectively as possible. Hence, I believe DNA repair is as important, if not scientifically, then at least pragmatically, as any of the other 7 pillars of SENS.

Your points, Jay, are well taken, and it is a correct analysis. However, I cannot agree with your conclusions. Your conclusions, if I am not mistaken, imply that since it will cost more later, we should invest more now to save these future costs. This argument is seemingly difficult to argue with. The problem is we have very limited resources now. The extra hundred million in research you speak of does not at all relate to the extra 100 billion it will cost in the future.

Spending $100 million to save $100 billion is exactly the kind of argument we're trying to use to get support for SENS in the first place: Spend $10 billion now, or trillions of dollars annually in retirement benefits and trillions more annually in health benefits to the elderly, in the decades ahead.

But let's face it, once SENS is in place, even if it is cheaper than paying for our current health system, it's still going to be expensive. We've just replaced "trillions" with "hundreds of billions". There's still going to be a crisis of management, especially if we all have to be reseeded every 10 years. Every effort up front to extend that time to 20 years or 40 years or 80 years is an effort that will pay off. Especially because, at 10 years, we will probably each need one to five reseedings before technology obviates the need for reseedings (nanotech, etc.). With an initial reseeding time of 25 years, we may only need one reseeding, if any, after the first operation. If we can get 40 years between reseedings, many people may only have to have one treatment before advanced nanotech comes up with a more "permanent" solution.

But again, I digress.

[jaydfox]

...I must assume that WILT was intended to provide just such oblation and replacement.

Please accept my apologies for offering all our cells as gifts to some deity:

3 entries found for oblation.
ob·la·tion ( P ) Pronunciation Key (-blshn, -bl-)
n.
1. The act of offering something, such as worship or thanks, to a deity.
2. Oblation
a. The act of offering the bread and wine of the Eucharist.
b. Something offered, especially the bread and wine of the Eucharist.
3. A charitable offering or gift.


5 entries found for ablation.
ab·la·tion ( P ) Pronunciation Key (-blshn)
n.
1. Surgical excision or amputation of a body part or tissue.
2. The erosive processes by which a glacier is reduced.
3. Aerospace. The dissipation of heat generated by atmospheric friction, especially in the atmospheric reentry of a spacecraft or missile, by means of a melting heat shield.

etc.


Ummm, my bad.

[eternaltraveler]

Spending $100 million to save $100 billion is exactly the kind of argument we're trying to use to get support for SENS in the first place: Spend $10 billion now, or trillions of dollars annually in retirement benefits and trillions more annually in health benefits to the elderly, in the decades ahead.

Another point I'd like to bring up in this regard.

I believe it is unlikely people will have to be reseeded every 10 years more than once or twice. We're going to be able to engineer the living crap out of these stem cells in vitro. This will be in an era where massive anti aging funding exists. I don't see why we won't be able to make cancer just as improbable through other means as through eliminating the telomerase (and similar) pathways. Either through suicide genes planted in the new stem cells making them vulnerable to very light chemo, or other novel approaches.

Aubrey mentioned that cancers do a very good job at pumping out chemicals that might undermine the whole suicide gene idea, however I still believe that there's no reason that we can't alter their genes so that they pump in these chemicals just as fast.

This seems like a good idea anyway so that you can easily get rid of the old stem cells for the latest "upgrade".

I will admit that I do find the idea of being “addicted” to stem cell reseeding with deadly withdraw a big downside of WILT. It would be a much easier sell to me and the public in general if it could be reworked so you wouldn't automatically die if you were stranded on a desert island for 11 years, or the government was taken over by the Christian right for 11 years who think using stem cells make Jesus cry (thus killing all "immortals" in the country).

Heck, even if stem cell therapies were unavailable for 2 years that would kill a lot of immortals who needed their scheduled stem cell therapies in those two years.

[jaydfox]

The problem is we have very limited resources now. The extra hundred million in research you speak of does not at all relate to the extra 100 billion it will cost in the future.

I was thinking about this last night. Dr. de Grey's hope is that once robust rejuvenation has been accomplished, MASSIVE funding will become available. In my mind, if the U.S. can come up with $300 billion to let a hundred thousand civilians die, nearly 15,000 Americans die or be wounded, and turn a secular dictatorship into a religious democracy friendly to a nuclear-capable fundamentalist theocracy, then surely we can come up with a few tens of billions of dollars a year for any aspects of SENS that are necessary.

We can lay the groundwork fairly cheaply with a Fly Prize. When the funds become available, and they will, we can have the problem solved in no time. Cost should not be the concern. Efficacy should be. Practicality should be.