- A colleague of mine likes to point out that a Fields Medal (the highest honor in mathematics) indicates two things about the recipient: that he was capable of accomplishing something important, and that he didn't. Though harsh, the remark hints at a truth.
- Think of a "discovery" as an act that moves the arrival of information from a later point in time to an earlier time. The discovery's value does not equal the value of the information discovered but rather the value of having the information available earlier than it otherwise would have been. A scientist or a mathematician may show great skill by being the first to find a solution that has eluded many others; yet if the problem would soon have been solved anyway, then the work probably has not much benefited the world. There are cases in which having a solution even slightly sooner is immensely valuable, but this is more plausible when the solution is immediately put to use, either by being deployed for some practical end or serving as the foundation to further theoretical work. And in the latter case [...] there is great value in obtaining the solution slightly sooner only if the further work it enables is itself both important and urgent.
The question, then, is [...] whether it was important that the medalist enabled the publication of the result to occur at an earlier date. The value of this temporal transport should be compared to the value that a world-class mathematical mind could have generated by working on something else. At least in some cases, the Fields Medal might indicate a life spent solving the wrong problem - perhaps a problem whose allure consisted primarily in being famously difficult to solve.
Similar barbs could be directed at other fields, such as academic philosophy. Philosophy covers some problems that are relevant to existential risk mitigation - we encountered several in this book. Yet there are also subfields within philosophy that have no apparent link to existential risk or indeed any practical concern. As with pure mathematics, some of the problems that philosophy studies might be regarded as intrinsically important, in the sense that humans have reason to care about them independently of any practical application. The fundamental nature of reality, for instance, might be worth knowing about, for its own sake. The world would arguably be less glorious if nobody studied metaphysics, cosmology, or string theory. However, the dawning prospect of an intelligence explosion shines a new light on this ancient quest for wisdom.
The outlook now suggests that philosophic progress can be maximized via an indirect path rather than by immediate philosophizing. One of the many tasks on which superintelligence (or even just moderately enhanced human intelligence) would outperform the current cast of thinkers is in answering fundamental questions in science and philosophy. This reflection suggests a strategy of deferred gratification. We could postpone work on some of the eternal questions for a little while, delegating that task to our hopefully more competent successors - in order to focus our own attention on a more pressing challenge: increasing the chance that we will actually have competent successors. This would be high-impact philosophy and high-impact mathematics.
- I am not suggesting that nobody should work on pure mathematics or philosophy. I am also not suggesting that these endeavors are especially wasteful compared to all the other dissipations of academia or society at large. It is probably very good that some people can devote themselves to the life of the mind and follow their intellectual curiosity wherever it leads, independent of any thought of utility or impact. The suggestion is that at the margin, some of the best minds might, upon realizing that their cognitive performance may become obsolete in the forseeable future, want to shift their attention to those theoretical problems for which it makes a difference whether we get the solution a little sooner.
- (a) the two works and their timings were independent (almost true),
(b) there is no extra value in having the two different proofs of the result compared to having just one (plain false),
(c) without the two works, it would have taken another ten years for the scientific community to come up with a proof of Parisi's conjecture (pure speculation on my part).
Such superadditivity of values is not unusual. A hot dog on its own may be worthless to me, and the same may go for a bun, but together they constitute a highly delicious and valuable meal. But the Linusson-Wästlund and the Nair-Prabhakar-Sharma papers, exhibiting the same superadditivity, still does not fit the hot-dog-and-bun pattern, because unlike the hot dog and the bun, each of the papers contains, on its own, the whole thing we value (the early arrival of the proof of Parisi's conjecture). Strange.