Considerations of cost versus benefit drive all human action. With this in mind, and when considering the field of aging research, I'd contend that a fair number of the better defined lines of research are not worth the time and resources likely required to reach definitive results. By better defined I mean here research that can be expressed as a concise and narrow question (e.g. "why are naked mole-rats immune to cancer?") rather than research that is as much about finding the questions in the first place (e.g. attempting to establish a coherent big picture in the progression of Alzheimer's disease), or about gathering data for later use in other people's attempts to answer questions (e.g. whole genome sequencing of various species).
The well-known difference in longevity between human genders is a good example of a constrained and defined question in aging research: why do women live longer than men? It is also, to my mind, a great example of a question with an answer that isn't worth the cost involved in obtaining it. Research to date reveals this to be an inordinately complex issue, possessing all the signs of requiring a great deal of time and money to make any headway towards definitive answers:
A sexual dimorphism in human life expectancy has existed in almost every country for as long as records have been kept. Although human life expectancy has increased each year, females still live longer, on average, than males. Undoubtedly, the reasons for the sex gap in life expectancy are multifaceted, and it has been discussed from both sociological and biological perspectives. However, even if biological factors make up only a small percentage of the determinants of the sex difference in this phenomenon, parity in average life expectancy should not be anticipated.
The examination of biological mechanisms accounting for the female-based advantage in human life expectancy has been an active area of inquiry; however, it is still difficult to prove the relative importance of any 1 factor. Nonetheless, biological differences between the sexes do exist and include differences in genetic and physiological factors such as progressive skewing of X chromosome inactivation, telomere attrition, mitochondrial inheritance, hormonal and cellular responses to stress, immune function, and metabolic substrate handling among others. These factors may account for at least a part of the female advantage in human life expectancy.
Despite noted gaps in sex equality, higher body fat percentages and lower physical activity levels globally at all ages, a sex-based gap in life expectancy exists in nearly every country for which data exist. There are several biological mechanisms that may contribute to explaining why females live longer than men on average, but the complexity of the human life experience makes research examining the contribution of any single factor for the female advantage difficult. However, this information may still prove important to the development of strategies for healthy aging in both sexes.
I should say that the last line quoted above has the sound of a quick scrabbling for relevance when the next budgetary decision comes due. Still, perhaps I'm just a cynic.
So research to date suggests that working on the gender difference in longevity with the aim of finding a definitive answer will be expensive. That is the cost side of the cost-benefit consideration. On the benefit side, we might think that the best possible benefit resulting from a definitive answer to the question "why do women life longer than men?" is something like five to seven years of life - that being the additional life expectancy enjoyed by women in wealthier regions of the world, and which might conceivably be captured by men given an exact methodology to do so. Which is not to say that this outcome could be engineered as a practical matter even if the cause of the difference was known in certainty - for example if it turns out to be, say, some many-headed web of fundamental interactions between metabolism and the genetics of being male, something that must be worked around rather than just altered.
Trying to safely alter metabolism with minimal side-effects is a complex and expensive business, a realm akin to traditional drug discovery processes, where billions can be spent with ease while only marginal benefits resulting. When it comes to slowing aging via metabolic and genetic manipulation, working through this drug discovery process, the mainstream research community believes there is little hope for significant progress towards longer human lives in the next few decades.
My point here is that a goal wherein the research community has no great hope of rapid progress, and which has every sign of being enormously expensive to pursue, and which can only at best somewhat point the way towards a possible gain of up to five years or so of healthy life in half the population is not a goal that merits a full-court press and singular attention - or at least not where better alternatives exist. Insofar as human aging goes, there is no shortage of better alternatives at this point. The aging research community should look to bolder plans, better and more beneficial ways to spend their time: work with far bigger potential gains. This is an age of revolution in the capabilities of biotechnology, a time for great leaps ahead in intervening in the aging process, not a time to be tinkering in the sandbox of fiddling questions.