On Solving Aging
On scaling for aging
Aging is the upstream cause of nearly everything that kills us. It is also a complex learning problem, one that may yield to scale.
Felix Wong · Redwood City, 2026
Why does everyone have to die? I have been asking since I was six—the year my grandpa died—and I have yet to hear an answer that is a law rather than a habit. The most common non-response is "entropy"—a law of closed systems.
In practice, human mortality follows Gompertz's law: after adulthood, the risk of death doubles roughly every seven to eight years. That regularity is routinely mistaken for a physical constraint. It is not. It is a statistical fact about a species that evolution never optimized to live long past reproduction.
Biology has solved this problem already, repeatedly and independently. The naked mole-rat (a rodent the size of a mouse) shows no rise in mortality hazard even at twenty-five times reproductive maturity. Certain turtles and tortoises age negligibly. The ocean quahog and the Greenland shark persist for centuries with function intact. When a trait evolves independently across taxa this distant, it is not a miracle. It is an engineering solution, found more than once, by search. Decelerating aging is an engineering problem: it can be engineered.
Two further facts should frame our ambition. First, humans are almost certainly nowhere near a hard biological limit: selection pressure collapses after child-rearing, so our maintenance and repair systems were never tuned for late life. That implies a tremendous amount of low-hanging fruit. Second, biological age is not necessarily one-way. The germline is effectively immortal; the epigenetic clock resets to a ground state in the early embryo; partial reprogramming restores youthful methylation patterns and regenerative capacity in old animals without erasing cell identity. Aging is a state, and states can be moved.
The obstacle is not plausibility. The obstacle is search. Aging is multifactorial, slow to read out, and—this is the part the field rarely says out loud—we do not know where to look. Most failures in aging drug discovery have not been failures of biology. They have been failures of prior: we imposed a strong belief about mechanism onto a system whose mechanisms we cannot yet enumerate, and we were confidently wrong.
Every discovery strategy is really a choice about how strong a prior to impose. There are three regimes, and one way to view them is as a continuum indexed by the ratio of what we know to what we don't.
01 · Strong prior
Aim
Start from a mechanism and interrogate it deeply.
E.g., mTOR, cellular senescence, the DNA-damage response; rapamycin came from here. Buys mechanistic depth and precisely targeted interventions. Pays for it in scope: you can only find what you already suspected.
02 · Weak prior
Sweep
Test many interventions in parallel, under one standard.
The NIA Interventions Testing Program is the canonical instance; systematic drug repurposing is its commercial analogue. Buys freedom from tunnel vision. Pays in cost and in false positives that look expensive only later.
03 · No prior
Saturate
Let the data decide what works.
Ultra-high-content phenotypic screens across millions of perturbations in aged cells and organoids, read out by learned classifiers answering a deceptively simple question: does it look younger? Buys genuinely novel mechanisms. Pays in interpretation.
These are complementary, and any serious program should run all three. But they are not symmetric, and the ratio of focus matters. Aim does not improve because you collected more data; rather, its ceiling is the quality of a human hypothesis. In contrast, saturate does. Every additional well-designed perturbation sharpens the classifier, densifies the embedding, and improves the next round of proposals. Only the low-prior end of the spectrum has returns that compound with scale. The correct long-run strategy, then, is to shift weight rightward as fast as the data allow, and to use the leftward regimes as instruments for interpreting what the right-hand one finds.
"Scale," though, is the most abused word in this industry. Scaling the wrong data is merely noise with a larger budget. In my mind, the data that compound share four properties. They are perturbational rather than observational: this is because aging poses a causal question, and correlations drawn from cross-sectional cohorts cannot answer it. They are clean, generated with tools such as optogenetics that switch aging-associated pathways on and off with temporal precision, rather than inferred through chemical insult. They are high-content: for instance, an image of a cell carries orders of magnitude more information about its state than any single endpoint. And they are anchored, or tied back to human longitudinal reality, so that the model is learning about us and not about a well plate.
Data alone is also not a moat. A pile is not a flywheel. What compounds is a closed loop: models that propose hypotheses, a high-throughput platform that tests them against living systems, and a disciplined path by which experimental truth—including negative results—returns as training signal. The loop is the asset. Programs and partnerships are evidence that it turns.
Here, then, is my main bet: If aging is modifiable, if it is reversible, and if it is measurable as a phenotype, then it is learnable. And if it is learnable, then generating the right kinds of biological data at sufficient scale, inside a loop that feeds empirical truth back into the model, does not merely produce a longer list of compounds. It converges. The search stops being a sequence of guesses about aging and becomes a model of it: a foundation model of aging biology, whose outputs are interventions against aging itself rather than against its downstream diseases.
Aging research today sits roughly where oncology sat fifty years ago: a death sentence being slowly converted into a managed condition by systematic work. The goal is to compress morbidity—to extend the years in which people are well, not the years in which they are dying—and reaching it will demand as much from regulators, payers, and clinicians as from scientists. But the scientific question should no longer be whether modifying aging is tractable. It should be: who will build the machine that finds the answer at scale?