How much of academia and industry is headed in the wrong direction in the matter of treating aging as a medical condition, working on projects that are unlikely to produce meaningful extension of human life span? I am largely in agreement with the author of today’s open access paper, at least to the point of saying that a large fraction of projects cannot and will not move the needle on human life span, and that likely includes near everything commonly grouped under the heading of geroscience. That means calorie restriction mimetics, autophagy upregulation, small molecules that improve mitophagy, and so forth. These largely pharmacological approaches are unified in their inability to improve on the effects of exercise, where tested in humans, with very few exceptions (e.g. rapamycin).
I concur with the author’s argument that the 1990s studies that launched the modern interest in treating aging and extending human life did not actually indicate the right way ahead. This has long been remarked upon, and coming to be taken for granted, in at least some parts of the longevity community. All of the early, low hanging fruit interventions that slowed aging in short-lived species make use of mechanisms related to the calorie restriction response, and do not meaningfully extend life in long-lived species. When it comes to surviving seasonal famine, only the short-lived species must evolve a sizable plasticity of life span. A season is a long time to a mouse, not so much to a human.
The greatest progress that has taken place towards viable treatments for aging did not build upon the early discoveries of single gene mutations that extended life in laboratory species, but happened as a result of a broadening of investment in the field into other lines of research. But in my view, unlike that of the author of the commentary, that expansion of research and development has in fact led to important approaches that seem quite likely to be useful. In particular those grouped under the Strategies for Engineered Negligible Senescence (SENS), or repair viewpoint of aging, in which one identifies specific fundamental, driving forms of cell and tissue damage and repair them. This stands in stark contrast to the geroscience viewpoint in which one adjusts metabolism to slow aging, i.e. slow the accumulation of cell and tissue damage.
Good scientists tend not to make good engineers (and possibly vice versa); the mindset needed is quite different. The scientific viewpoint is the drive for complete understanding, with only a grudging, reluctant forking of an ongoing research process into to the parallel process of using knowledge to build technology. The engineering viewpoint, on the other hand, is focused on making empirical progress in an environment of uncertainty and partial knowledge: take what is known right now and try to make something of it. It is fair to say that, from a modern materials science perspective, the ancient Romans did not know anywhere near enough about bridge building. But their engineers built great bridges because empirical discovery allows the development of a corpus of knowledge and practical expertise. That practicality can later be fleshed out by the scientists, and in fact tends to help the scientists a great deal. That is what is presently underway in the treatment of aging as a medical condition, and is largely why a growing longevity industry exists at all.
Calling the whole of the longevity industry into question because geroscience is the wrong direction is throwing the baby out with the bathwater.
Inflated expectations: the strange craze for translational research on aging
The emergence of Hevolution and the XPRIZE Healthspan is just the latest development in a remarkable phenomenon: a dramatic upsurge in activity in the private sector aimed at developing treatments for aging, fuelled by a heady optimism that the time is nigh. Other examples that involve massive funding to achieve practical outcomes in applied research on aging include the California Life Company (Calico), into which some US$2.5B has been invested; and Altos Labs, which in 2022 raised US$3B from investors.
Here we ask the question: what is the basis for this optimism? The last quarter of a century has seen a concerted effort by scientists to understand the fundamental biological mechanisms of aging, and much ground has been covered. How has this informed the recent upswell in commercial activity? We suggest that the latter is an anomaly arising in part from developments within the aging research field a decade ago that were, in some ways, counterproductive. These include the emergence of the so-called geroscience research agenda.
What seems to have happened is the following. Advances in research on the biology of aging that culminated in the 1990s yielded startling implications. It seemed possible not only to understand the fundamental mechanisms of aging, but also to slow them down. These promising prospects led to the aging field becoming bigger and better, thanks to increased funding and the influx of many good scientists. As a result, standards of research grew more rigorous, including critical reassessments of earlier findings. Such careful research over the past two decades has, regrettably, undermined a number of the reasons for earlier optimism. Disappointingly, caloric restriction in rhesus monkeys proved not to have the same remarkable effects as those seen in rodents. Growth hormone defects that extend lifespan in mice were found not to do so in humans.
With the dwindling likelihood that humans possess the plasticity in aging seen in shorter-lived animals, and the failure of existing theories of aging, how should one further pursue research? Here two possible approaches may be envisaged. On the one hand, scientists could renew their efforts to develop an effective theoretical framework with the capacity to explain diverse phenomena of aging. On the other hand, research could focus on translating existing theoretical claims and experimental observations into therapeutic trials – preclinical or clinical. The pursuit of this strategy in the early 2010s marked the emergence of the geroscience agenda.
In the past, this strategy of prioritizing translational research in the absence of a good understanding of the basic science has sometimes proved successful, aided by brute force and serendipity. There are, however, also numerous instances where such trial-and-error approaches failed, sometimes involving investment of billions of dollars. The reader may pick their own examples. Unquestionably, for translational research to yield useful, practical applications, at least some level of scientific understanding is required. At issue is judging when the time is ripe to move from basic to translational research, particularly where large investments of money and effort are involved. The oddest thing about the translational geroscience approach is its combination of pessimism about understanding aging, and optimism about translational research. Arguably, the inverse is more realistic.