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.
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.