I should clarify something: the types of problems I can most efficiently tackle are retrospective analysis of already-collected data.
Prospective clinical and animal studies are not out of the question, but given the investment in infrastructure and regulatory compliance they would need, these would have to be collaborations with researchers already pursuing such studies. This is on the table, but does not leverage the clinical data I already have (unless, in the case of clinical researchers, they are already at my institution or an affiliated one).
My idea at the moment is to fit a hidden Markov model and derive a state model for human aging. But this pile of clinical data I have has got to be useful for all kinds of other aging-related questions...
I have some philosophical objections to your approach. I’m not sure it’s such a good idea to focus exclusively on research questions that are explicitly aging-related, just because you’ll be limiting yourself to a subset of the promising ideas out there. Secondly, you probably shouldn’t worry about pursuing a project in which your already-collected data is useless, especially if that data or similar is also available to most other researchers in your field (if not, it would be very useful for you to try to make that data available to others who could do something with it). You’re probably more likely to make progress with interesting new data than interesting old data. Also, I’m not sure if this is your intention, but it seems to me that the goal of spending 20 years to slow or prevent aging is a recipe for wasting time. It’s such an ambitious goal that so many people are already working on, any one researcher is unlikely to put a measurable dent in it. It’s like getting a math phd and saying “Ok, now I’m going to spend the rest of my life trying to help solve the Riemann Hypothesis.” Esepcially when you’re just starting out, you may be better-served working on the most promising projects you can find in your general area of interest, even if their goals are less ambitious.
P.s. Sorry if a lot of what I’ve said is naive, I’ve never worked in academia.
Also, I’m not sure if this is your intention, but it seems to me that the goal of spending 20 years to slow or prevent aging is a recipe for wasting time. It’s such an ambitious goal that so many people are already working on, any one researcher is unlikely to put a measurable dent in it.
In the last five years the NIH (National Institutes of Health) has never spent more than 2% of its budget on aging research. To a first approximation, the availability of grant support is proportional to the number of academic researchers, or at least to the amount of academic research effort being put into a problem. This is evidence against aging already getting enough attention. Especially considering that age is a major risk factor for just about every disease. It’s as if we tried to treat AIDS by spending 2% on HIV research and 98% on all the hundreds of opportunistic infections that are the proximal causes any individual AIDS patient’s death. I would think that curing several hundred proximal problems is more ambitious than trying to understand and intervene in a few underlying causes.
I have no illusions of single-handedly curing aging in the next two decades. I will be as satisfied as any other stiff in the cryofacility if I manage remove one or more major road-blocks to a practical anti-aging intervention or at least a well-defined and valid mechanistic model of aging.
Secondly, you probably shouldn’t worry about pursuing a project in which your already-collected data is useless, especially if that data or similar is also available to most other researchers in your field (if not, it would be very useful for you to try to make that data available to others who could do something with it). You’re probably more likely to make progress with interesting new data than interesting old data.
This is ‘new’ data in the sense that it is only now becoming available for research purposes, and if I have my way, it is going to be in a very flexible and analysis-friendly format. It is the core mission of my team to make the data available to researchers (insofar as permitted by law, patients’ right to privacy, and contractual obligations to the owners of the data).
If I ran “academia”, tool and method development would take at least as much priority as traditional hypothesis-driven research. I think a major take-home message of LW is that hypotheses are a dime a dozen—what we need are practical ways to rank them and update their rankings on new data. A good tool that lets you crank through thousands of hypotheses is worth a lot more than any individual hypothesis. I have all kinds of fun ideas for tools.
But for the purposes of this post, I’m assuming that I’m stuck with the academia we have, I have access to a large anonymized clinical dataset, and I want to make the best possible use of it (I’ll address your points about aging as a choice of topic in a separate reply).
The academia we’re stuck with (at least in the biomedical field) effectively requires faculty to have a research plan describable by “Determine whether FOO is true or false” rather than “Create a FOO that does BAR”.
So the nobrainer approach would be for me to take the tool I most want to develop, slap some age-related disease onto it as a motivating use-case, and make that my grant. But, this optimizes for the wrong thing—I don’t want to find excuses for engaging in fascinating intellectual exercises. I want to find the problems with the greatest potential to advance human longevity, and then bring my assets to bear on those problems even if the work turns out to be uglier and more tedious than my ideal informatics project.
The reason I’m asking for the LW community’s perspective on what’s on the critical path to human longevity is that I spent too much time around excuse-driven^H^H^H hypothesis-driven research to put too much faith in my own intuitions about what problems need to be solved.
I wasn’t arguing whether aging research should receive more attention, just that it receives enough to make a single researcher a drop in the bucket, but you might not be an average researcher. I’m interested in knowing, how likely do you think it is that the life expectancy of some people will be measurably lower if you work as a used-car salesman for the next 20 years rather than a researcher. I’m not suggesting that aging isn’t a worthwhile area of research, just that it may be counterproductive for you to be trying to make all the work you do for the next 20 years have some direct bearing on aging.
When I say a project is ambitious, I mean that it is very unlikely to return good results, but that the impact of those good results would be enormous. Developing a large number of drugs to increase the life expectancies of terminally ill cancer patients is less ambitious than trying to cure their cancer. You seem to be thinking that we have made so little progress on aging because it hasn’t received enough attention. What if it’s the other way around, and so few researchers tackle aging head-on because it’s hard to make meaningful progress on? I think that for any researcher who wants to provide mechanistic insights into aging, or figure out how the brain works, or create a machine with human-like general intelligence, there’s a lrage incentive for success, but almost inevitably such researchers need shorter term results to keep themselves going. If there simply aren’t any shorter term opportunities to make meaningful progress on, they run the risk of working on something that seems related to the problem they set out to solve, but in reality contributes only shallowly to their understanding of it. This is how you end up with so many attempts to better understand the brain through brain scans or make progress in machine intelligence by studying an absurdly specific situation. There were probably more meaningful things those researchers could have been doing that didn’t seem to fall under the heading of an extremely ambitious goal. You might be able to bypass these tendencies, but it won’t be easy; if it were easy, we would have more researchers who are making meaningful progress on aging.
Okay, neat! I have an idea, and it might be kind of farfetched, or not amenable to the types of analyses you are best at doing, but I’ll share it anyways. Here goes.
Given that there is a tradeoff between health and reproduction, I wonder if you could increase the expected lifespan of a healthy human male by having him take anti-androgens on a regular basis.
We already know that male eunuchs who are humans live longer than intact male humans. I suspect that most guys wouldn’t be willing to become eunuchs even if they valued having a long lifespan very highly, but being able to increase one’s expected lifespan by decreasing one’s testosterone levels while still remaining intact might be something that a few males would consider, if such a therapy were proven to be effective.
Anyways, after taking 10 minutes to look around on Google Scholar, I wasn’t able to find any papers suggesting that taking anti-androgens would be an effective anti-aging measure, so maybe this would be a viable project for someone to work on.
As an aside, I don’t know which mechanisms cause castrated men to live longer, but this seems relevant to the question of why/how castrated men live longer.
Great idea! Here’s how I can convert your prospective experiment into retrospective ones:
Comparing hazard functions for individuals with diagnoses of infertility versus individuals who originally enter the clinic record system due to a routine checkup.
This is interesting, but a clear confound is that people who enter for infertility are likely to be more conscientious, which correlates with lifespan.
Whether male eunuchs actually live longer is controversial to say the least. Eg, the effect is not seen in dogs. In humans there are clear confounds.
Also, t levels don’t seem to clearly correlate with decreased or increased lifespans. And as your last link points out, lower levels of t (ie hypogonadism) are correlated with increased risk of CVD mortality.
Also, t levels don’t seem to clearly correlate with decreased or increased lifespans. And as your last link points out, lower levels of t (ie hypogonadism) are correlated with increased risk of CVD mortality.
Yes, you’re right about that. The paper says that:
“Our meta-analysis shows that patients with CVD have, on average, lower testosterone level than healthy controls.”
However, the paper also says that:
“Taken together, these results suggest that low testosterone may be considered as a marker of poor general health status, negatively affecting prognosis, rather than a specific CV risk factor (11, 84–86, 95). Low testosterone level has also been associated with an increased mortality in patients affected by non-CVD...”
In fact, since there is a tradeoff between health and reproductive ability, we might expect the development of health problems in previously healthy males to cause testosterone levels to drop, as a means of offsetting some of the negative effects of said health problem. This could account for why lower levels of testosterone are correlated with increased CVD mortality.
However,
Whether male eunuchs actually live longer is controversial to say the least.
In my view there is reasonable evidence for a trade-off between health and reproduction between species, but not within species. Am I wrong on this?
On eunuch lifespan, you are basically relying on three studies, each of which are historical, ie the Mental Health studies in the mid 20th century and the historical Korean eunuch study. I think there are big problems in interpreting these studies. For example, it’s not like the eunuch lifespans in either sample is as long as men in wealthy countries, which makes things like infections and generally risky behavior a much stronger candidate for the mechanism, which wouldn’t generalize to lifespan today. What am I wrong about here?
Let me be clear that I want you to be right. It suggests a clear mechanism to increasing lifespan in men. I just don’t think that there’s very strong evidence for it.
I should clarify something: the types of problems I can most efficiently tackle are retrospective analysis of already-collected data.
Prospective clinical and animal studies are not out of the question, but given the investment in infrastructure and regulatory compliance they would need, these would have to be collaborations with researchers already pursuing such studies. This is on the table, but does not leverage the clinical data I already have (unless, in the case of clinical researchers, they are already at my institution or an affiliated one).
My idea at the moment is to fit a hidden Markov model and derive a state model for human aging. But this pile of clinical data I have has got to be useful for all kinds of other aging-related questions...
I have some philosophical objections to your approach. I’m not sure it’s such a good idea to focus exclusively on research questions that are explicitly aging-related, just because you’ll be limiting yourself to a subset of the promising ideas out there. Secondly, you probably shouldn’t worry about pursuing a project in which your already-collected data is useless, especially if that data or similar is also available to most other researchers in your field (if not, it would be very useful for you to try to make that data available to others who could do something with it). You’re probably more likely to make progress with interesting new data than interesting old data. Also, I’m not sure if this is your intention, but it seems to me that the goal of spending 20 years to slow or prevent aging is a recipe for wasting time. It’s such an ambitious goal that so many people are already working on, any one researcher is unlikely to put a measurable dent in it. It’s like getting a math phd and saying “Ok, now I’m going to spend the rest of my life trying to help solve the Riemann Hypothesis.” Esepcially when you’re just starting out, you may be better-served working on the most promising projects you can find in your general area of interest, even if their goals are less ambitious.
P.s. Sorry if a lot of what I’ve said is naive, I’ve never worked in academia.
In the last five years the NIH (National Institutes of Health) has never spent more than 2% of its budget on aging research. To a first approximation, the availability of grant support is proportional to the number of academic researchers, or at least to the amount of academic research effort being put into a problem. This is evidence against aging already getting enough attention. Especially considering that age is a major risk factor for just about every disease. It’s as if we tried to treat AIDS by spending 2% on HIV research and 98% on all the hundreds of opportunistic infections that are the proximal causes any individual AIDS patient’s death. I would think that curing several hundred proximal problems is more ambitious than trying to understand and intervene in a few underlying causes.
I have no illusions of single-handedly curing aging in the next two decades. I will be as satisfied as any other stiff in the cryofacility if I manage remove one or more major road-blocks to a practical anti-aging intervention or at least a well-defined and valid mechanistic model of aging.
This is ‘new’ data in the sense that it is only now becoming available for research purposes, and if I have my way, it is going to be in a very flexible and analysis-friendly format. It is the core mission of my team to make the data available to researchers (insofar as permitted by law, patients’ right to privacy, and contractual obligations to the owners of the data).
If I ran “academia”, tool and method development would take at least as much priority as traditional hypothesis-driven research. I think a major take-home message of LW is that hypotheses are a dime a dozen—what we need are practical ways to rank them and update their rankings on new data. A good tool that lets you crank through thousands of hypotheses is worth a lot more than any individual hypothesis. I have all kinds of fun ideas for tools.
But for the purposes of this post, I’m assuming that I’m stuck with the academia we have, I have access to a large anonymized clinical dataset, and I want to make the best possible use of it (I’ll address your points about aging as a choice of topic in a separate reply).
The academia we’re stuck with (at least in the biomedical field) effectively requires faculty to have a research plan describable by “Determine whether FOO is true or false” rather than “Create a FOO that does BAR”.
So the nobrainer approach would be for me to take the tool I most want to develop, slap some age-related disease onto it as a motivating use-case, and make that my grant. But, this optimizes for the wrong thing—I don’t want to find excuses for engaging in fascinating intellectual exercises. I want to find the problems with the greatest potential to advance human longevity, and then bring my assets to bear on those problems even if the work turns out to be uglier and more tedious than my ideal informatics project.
The reason I’m asking for the LW community’s perspective on what’s on the critical path to human longevity is that I spent too much time around excuse-driven^H^H^H hypothesis-driven research to put too much faith in my own intuitions about what problems need to be solved.
I wasn’t arguing whether aging research should receive more attention, just that it receives enough to make a single researcher a drop in the bucket, but you might not be an average researcher. I’m interested in knowing, how likely do you think it is that the life expectancy of some people will be measurably lower if you work as a used-car salesman for the next 20 years rather than a researcher. I’m not suggesting that aging isn’t a worthwhile area of research, just that it may be counterproductive for you to be trying to make all the work you do for the next 20 years have some direct bearing on aging.
When I say a project is ambitious, I mean that it is very unlikely to return good results, but that the impact of those good results would be enormous. Developing a large number of drugs to increase the life expectancies of terminally ill cancer patients is less ambitious than trying to cure their cancer. You seem to be thinking that we have made so little progress on aging because it hasn’t received enough attention. What if it’s the other way around, and so few researchers tackle aging head-on because it’s hard to make meaningful progress on? I think that for any researcher who wants to provide mechanistic insights into aging, or figure out how the brain works, or create a machine with human-like general intelligence, there’s a lrage incentive for success, but almost inevitably such researchers need shorter term results to keep themselves going. If there simply aren’t any shorter term opportunities to make meaningful progress on, they run the risk of working on something that seems related to the problem they set out to solve, but in reality contributes only shallowly to their understanding of it. This is how you end up with so many attempts to better understand the brain through brain scans or make progress in machine intelligence by studying an absurdly specific situation. There were probably more meaningful things those researchers could have been doing that didn’t seem to fall under the heading of an extremely ambitious goal. You might be able to bypass these tendencies, but it won’t be easy; if it were easy, we would have more researchers who are making meaningful progress on aging.
Okay, neat! I have an idea, and it might be kind of farfetched, or not amenable to the types of analyses you are best at doing, but I’ll share it anyways. Here goes.
Given that there is a tradeoff between health and reproduction, I wonder if you could increase the expected lifespan of a healthy human male by having him take anti-androgens on a regular basis.
We already know that male eunuchs who are humans live longer than intact male humans. I suspect that most guys wouldn’t be willing to become eunuchs even if they valued having a long lifespan very highly, but being able to increase one’s expected lifespan by decreasing one’s testosterone levels while still remaining intact might be something that a few males would consider, if such a therapy were proven to be effective.
Anyways, after taking 10 minutes to look around on Google Scholar, I wasn’t able to find any papers suggesting that taking anti-androgens would be an effective anti-aging measure, so maybe this would be a viable project for someone to work on.
As an aside, I don’t know which mechanisms cause castrated men to live longer, but this seems relevant to the question of why/how castrated men live longer.
Great idea! Here’s how I can convert your prospective experiment into retrospective ones:
Comparing hazard functions for individuals with diagnoses of infertility versus individuals who originally enter the clinic record system due to a routine checkup.
This is interesting, but a clear confound is that people who enter for infertility are likely to be more conscientious, which correlates with lifespan.
Whether male eunuchs actually live longer is controversial to say the least. Eg, the effect is not seen in dogs. In humans there are clear confounds.
Also, t levels don’t seem to clearly correlate with decreased or increased lifespans. And as your last link points out, lower levels of t (ie hypogonadism) are correlated with increased risk of CVD mortality.
Yes, you’re right about that. The paper says that:
However, the paper also says that:
In fact, since there is a tradeoff between health and reproductive ability, we might expect the development of health problems in previously healthy males to cause testosterone levels to drop, as a means of offsetting some of the negative effects of said health problem. This could account for why lower levels of testosterone are correlated with increased CVD mortality.
However,
is a statement which I emphatically disagree with.
In my view there is reasonable evidence for a trade-off between health and reproduction between species, but not within species. Am I wrong on this?
On eunuch lifespan, you are basically relying on three studies, each of which are historical, ie the Mental Health studies in the mid 20th century and the historical Korean eunuch study. I think there are big problems in interpreting these studies. For example, it’s not like the eunuch lifespans in either sample is as long as men in wealthy countries, which makes things like infections and generally risky behavior a much stronger candidate for the mechanism, which wouldn’t generalize to lifespan today. What am I wrong about here?
Again, why don’t we see the effect in dogs? http://www.straightdope.com/columns/read/3068/does-castration-longer-life
Let me be clear that I want you to be right. It suggests a clear mechanism to increasing lifespan in men. I just don’t think that there’s very strong evidence for it.