The Value of Theoretical Research

For many of us, choos­ing a ca­reer path has a dom­i­nant effect on our con­tri­bu­tion to the so­ciety. For those of us who care what hap­pens to so­ciety, this makes it one of the most im­por­tant de­ci­sions we make. Like most de­ci­sions, this one is very of­ten made by im­pulses sig­nifi­cantly be­low the level of con­scious recog­ni­tion, with con­sid­er­able in­tel­lec­tual effort spent on jus­tify­ing a con­clu­sion but very lit­tle spent on ac­tu­ally reach­ing one. In the case of smart, al­tru­is­tic ra­tio­nal­ists, this seems like the most tragic failure of ra­tio­nal­ity; so, what­ever the out­come, I ad­vo­cate much more se­ri­ous con­sid­er­a­tion by smart ra­tio­nal­ists of how our ca­reer choices af­fect so­ciety. For the most part this is a per­sonal thing, but some pub­lic dis­cus­sion may be valuable. I apol­o­gize (largely in ad­vance) for any­thing that seems con­de­scend­ing.

I pre­vi­ously planned to do re­search in pure math (and more re­cently in the­o­ret­i­cal com­puter sci­ence). I fre­quently jus­tified my po­si­tion with care­fully con­structed ar­gu­ments which I no longer be­lieve. It still may be the case that do­ing re­search is a good idea (and spend­ing the rest of my life do­ing re­search is still the eas­iest pos­si­ble ca­reer path for me), so I am in­ter­ested in ad­di­tional ar­gu­ments, or rea­sons why any­thing I am about to write is wrong. Here is a ba­sic list of my jus­tifi­ca­tions, and why I no longer be­lieve them.

Ar­gu­ment 1: Much math is prac­ti­cally im­por­tant to­day. The math I am work­ing on is not prac­ti­cally im­por­tant to­day, but maybe it will be the math that is prac­ti­cally im­por­tant to­mor­row. How can we pre­dict what will be use­ful? It seems like push­ing math gen­er­ally for­ward is the best re­sponse to this un­cer­tainty.

Re­but­tal: If we re­ally want to eval­u­ate this ar­gu­ment, it is im­por­tant to un­der­stand the con­di­tions un­der which the im­por­tant math of to­day was done. In the case of calcu­lus, differ­en­tial equa­tions, statis­tics, func­tional anal­y­sis, lin­ear alge­bra, group the­ory, and nu­mer­i­cal meth­ods, the im­por­tant re­sults for mod­ern work were in fact de­vel­oped af­ter their use­ful­ness could be ap­pre­ci­ated by an in­tel­li­gent ob­server. There is very lit­tle hon­estly com­pel­ling ev­i­dence that push­ing math for the sake of push­ing math is likely to lead to prac­ti­cally im­por­tant re­sults more effec­tively than wait­ing un­til new math is needed and then de­vel­op­ing it. Per­haps the most com­pel­ling case is num­ber the­ory and its un­ex­pected ap­pli­ca­tion to cryp­tog­ra­phy, which is still not nearly com­pel­ling enough to jus­tify work on pure math (or even provide sig­nifi­cant sup­port).

Ar­gu­ment 2: Math is prac­ti­cally im­por­tant to­day. The math I am work­ing on is in a field that is prac­ti­cally im­por­tant to­day, and not many peo­ple are qual­ified to work on it, so push­ing the state of the art here is an ex­cel­lent use of my time.

Re­but­tal: Con­sider the ac­tual marginal util­ity of ad­vances in your field of choice, hon­estly. In the over­whelming ma­jor­ity of cases, the bulk of re­search effort is di­rected grotesquely in­effi­ciently from a so­cial per­spec­tive. In par­tic­u­lar, a small num­ber of largely ar­tifi­cial ap­pli­ca­tions will typ­i­cally sup­port re­search pro­grams which con­sume an in­cred­ible amount of in­tel­li­gent math­e­mat­i­ci­ans’ time, com­pared to the time re­quired to make fun­da­men­tal progress on the ac­tual prob­lem that peo­ple care about. Here you have to make a differ­ent ar­gu­ment for ev­ery re­search pro­gram, which I would be happy to do if any­one offers a par­tic­u­lar challenge.

Ar­gu­ment 3: The­o­ret­i­cal physics re­search ad­vances the fun­da­men­tal limits of un­der­stand­ing, which has led to im­por­tant ad­vances in the past and will prob­a­bly con­tinue to lead to im­por­tant ad­vances.

Re­but­tal: What mat­ters are in­ter­ac­tions in regimes that hu­mans can en­g­ineer—im­prov­ing un­der­stand­ing in such regimes is re­spon­si­ble for ev­ery tech­nolog­i­cal de­vel­op­ment I am aware of. In par­tic­u­lar, im­prove­ments in our un­der­stand­ing of high en­ergy physics or cos­mol­ogy are un­likely to be use­ful un­til we can de­sign sys­tems which op­er­ate in those regimes. There is fun­da­men­tal physics re­search which seems likely to have a high pay­off—but if you ap­proach the­o­ret­i­cal physics with the hon­est goal of con­tribut­ing to tech­nolog­i­cal progress, you end up with a re­search pro­gram which is un­rec­og­niz­ably differ­ent from most physi­cists’.

Ar­gu­ment 4: Pure re­search is at least a lit­tle use­ful, and its what I am best pre­pared to do.

Re­but­tal: There is a short­age of in­tel­li­gent, ra­tio­nal peo­ple in pretty much ev­ery area of hu­man ac­tivity. I would go so far as to claim this is the limit­ing in­put for most fields. If you don’t be­lieve this, at least ask your­self why not. Do you have ex­pe­rience in other fields that sug­gests you are un­able to con­tribute? Do you have a causal ar­gu­ment?

Ar­gu­ment 5: So­ciety is rel­a­tively effi­cient. The marginal re­turns for work in ev­ery field are roughly com­pa­rable, so I should work wher­ever I have com­par­a­tive ad­van­tage.

Re­but­tal: Why should so­ciety be re­motely effi­cient? I be­lieved this for a long time, but even­tu­ally re­al­ized it was just a hold-over from a point in my life where I had more faith in other peo­ple. If you are typ­i­cal LW read­ers, you prob­a­bly be­lieve at least half a dozen strong coun­terex­am­ples to this claim already.

Ar­gu­ment 6: Pure re­search has fun­da­men­tal value as an in­tel­lec­tual pur­suit.

Re­but­tal: For whom? If you are con­cerned ex­clu­sively with the in­tel­lec­tual rich­ness of math­e­mat­i­ci­ans’ lives, then I can’t well dis­agree and this ar­gu­ment may be com­pletely con­vinc­ing. Other­wise, if you be­lieve that the in­creas­ing rich­ness of hu­man math­e­mat­ics is a fun­da­men­tal good which non-math­e­mat­i­ci­ans can en­joy, con­sider the in­fer­en­tial dis­tances sep­a­rat­ing mod­ern ad­vances from even the most in­tel­li­gent layper­son. If your ul­ti­mate goal is the pro­duc­tion of math­e­mat­ics, or in fact any tem­po­rally al­tru­is­tic ob­jec­tive, then con­sider al­ter­na­tives which may in­crease the fu­ture’s ca­pac­ity to do math­e­mat­ics and which may be or­ders of mag­ni­tude more effec­tive.

Ar­gu­ment 7: What else would I do to make a liv­ing? Re­search pro­vides at least some benefit to so­ciety; al­ter­na­tives seem even worse.

Re­but­tal: My past self, at least, was guilty of mo­ti­vated stop­ping. See ar­gu­ment 4.