Criteria for scientific choice I, II

Alvin Wein­berg wrote two pa­pers in 1963 and 1964 ti­tled Cri­te­ria for Scien­tific Choice and Cri­te­ria for sci­en­tific choice II: The two cul­tures. In them, he makes a case for bet­ter al­lo­ca­tion of the large amounts of pub­lic fund­ing go­ing into sci­ence in the USA (which was re­mark­ably new, and in large part a re­sult of WWII). Un­for­tu­nately, these pa­pers are not open ac­cess, so if it in­ter­ests you to read you can reach out to me. This was in­ter­est­ing and rele­vant to pri­ori­ti­sa­tion within sci­ence, so I’d thought to share my notes here. It isn’t pol­ished or highly de­tailed.

Wein­berg sets two cat­e­gories of crite­ria by which to as­sess what to fund within sci­ence. In­ter­nal crite­ria are gen­er­ated within the sci­en­tific field it­self and an­swer the ques­tion: How well is the sci­ence done? Ex­ter­nal crite­ria are gen­er­ated out­side the sci­en­tific field and an­swer the ques­tion: Why pur­sue this par­tic­u­lar sci­ence?

He thinks that Ex­ter­nal crite­ria are more im­por­tant, be­cause these more di­rectly map to benefits for so­ciety. He also says in the pa­per that he ex­pects gen­er­ally use­ful sci­en­tific progress to be less serendipi­tous -

The tech­nolog­i­cal use­ful­ness of the laser came af­ter, not be­fore, the prin­ci­ple of op­ti­cal am­plifi­ca­tion was dis­cov­ered. But it is my be­lief that such tech­nolog­i­cal bolts from the sci­en­tific blue are the ex­cep­tion, not the rule

Than he clas­sifies ex­ter­nal crite­ria into three parts:

  1. Tech­nolog­i­cal merit—for a given tech­nolog­i­cal goal, sup­port the nec­es­sary knowl­edge.

  2. Scien­tific merit—A field in which lack of knowl­edge is a bot­tle­neck to the un­der­stand­ing of other fields de­serves more sup­port than a field which is iso­lated from other fields. That field has the most sci­en­tific merit which con­tributes most heav­ily to and illu­mi­nates most brightly its neigh­bour­ing sci­en­tific dis­ci­plines. (Wein­berg seems to be ar­gu­ing against the claim that sci­en­tific fields should be judged in­ter­nally, by do­main ex­perts).

  3. So­cial merit—rele­vance to hu­man welfare and the val­ues of man.

The fol­low­ing is a fun part, where the au­thor as­sesses 5 sci­en­tific fields ac­cord­ing to these mer­its, so I’ll cite it all:

Hav­ing set forth these crite­ria and recog­nis­ing that judg­ments are fraught with difficulty, I pro­pose to as­sess five differ­ent sci­en­tific and tech­ni­cal fields, in the light of these. The five fields I choose are molec­u­lar biol­ogy, high-en­ergy physics, nu­clear en­ergy, manned-space ex­plo­ra­tion, and the be­havi­oural sci­ences. Two of these fields, molec­u­lar biol­ogy and high-en­ergy physics, are, by any defi­ni­tion, ba­sic sci­ences; nu­clear en­ergy is ap­plied sci­ence, the be­havi­oural sci­ences are a mix­ture of both ap­plied and ba­sic sci­ence. Manned ex­plo­ra­tion of space, though it re­quires the tools of sci­ence and is re­garded in the pop­u­lar mind as be­ing part of sci­ence, has not yet been proved to be more than quasi-sci­en­tific, at best.

The fields which I choose are in­com­men­su­rable: how can one mea­sure the merit of be­havi­oural sci­ences and nu­clear en­ergy on the same scale of val­ues? Yet the choices be­tween sci­en­tific fields will even­tu­ally have to be made whether we like it or not. Cri­te­ria for sci­en­tific choice will be most use­ful only if they can be ap­plied to seem­ingly in­com­men­su­rable situ­a­tions. The val­idity of my pro­posed crite­ria de­pends on how well they can serve in com­par­ing fields that are hard to com­pare.

Of the sci­en­tific fields now re­ceiv­ing pub­lic sup­port, per­haps the most suc­cess­ful is molec­u­lar biol­ogy. Hardly a month goes by with­out a stun­ning suc­cess in molec­u­lar biol­ogy be­ing re­ported in the Pro­ceed­ings of the Na­tional Academy of Sciences. The most re­cent has been the crack­ing by Nieren­berg and Ochoa of the code ac­cord­ing to which triples of bases de­ter­mine spe­cific amino acids in the liv­ing pro­teins. Here is a field which rates the high­est grades as to its ripe­ness for ex­ploita­tion and com­pe­tence of its work­ers, It is profoundly im­por­tant for large stretches of other biolog­i­cal sci­ences—ge­net­ics, cy­tol­ogy, micro­biol­ogy—and, there­fore, ac­cord­ing to my crite­rion, must be graded A + for its sci­en­tific merit. It also must be given a very high grade in so­cial merit, and prob­a­bly in tech­nolog­i­cal (that is, med­i­cal) merit—more than, say, tax­on­omy or topol­ogy. Molec­u­lar biol­ogy is the most fun­da­men­tal of all the biolog­i­cal sci­ences. With un­der­stand­ing of the man­ner of trans­mis­sion of ge­netic in­for­ma­tion ought to come the in­sights nec­es­sary for the solu­tion of such prob­lems as can­cer, birth defects, and viral dis­eases. Al­to­gether, molec­u­lar biol­ogy ought, in my opinion, to re­ceive as much pub­lic sup­port as can pos­si­bly be pumped into it; since money is not limit­ing its growth, many more post-grad­u­ate stu­dents and re­search fel­lows in molec­u­lar biol­ogy ought to be sub­sidised so that the at­tack on this fron­tier can be ex­panded as rapidly as pos­si­ble.

The sec­ond field is high-en­ergy physics. This field of en­deav­our origi­nally sought as its ma­jor task to un­der­stand the nu­clear force. In this it has been only mod­estly suc­cess­ful; in­stead, it has opened an un­dreamed-of sub­nu­clear world of strange par­ti­cles and hy­per­ons, a world in which mir­ror images are of­ten re­versed. The field has no end of in­ter­est­ing things to do, it knows how to do them, and its peo­ple are the best. Yet I would be bold enough to ar­gue that, at least by the crite­ria which I have set forth—rele­vance to the sci­ences in which it is em­bed­ded, rele­vance to hu­man af­fairs, and rele­vance to tech­nol­ogy—high-en­ergy physics rates poorly. The nu­clear forces are not be­ing worked on very di­rectly—the world of sub­nu­clear par­ti­cles seems to be re­mote from the rest of the phys­i­cal sci­ences. Aside from the brilli­ant re­s­olu­tion of the r-par­ti­cle para­dox, which led to the over­throw of the con­ser­va­tion of par­ity, and the stud­ies of mesic atoms (the lat­ter of which is not done at ul­tra-high en­ergy), I know of few dis­cov­er­ies in ul­tra­high-en­ergy physics which bear strongly on the rest of sci­ence. (This view would have to be al­tered if ma­chines such as the Ar­gonne Zero Gra­di­ent Syn­chrotron were ex­ploited as very strong, pulsed sources of neu­trons for study of neu­tron cross sec­tions.) As for its bear­ing on hu­man welfare and on tech­nol­ogy, I be­lieve it is es­sen­tially nil. Th­ese two low grades would not bother me if high-en­ergy physics were cheap. But it is ter­ribly ex­pen­sive—not so much in money as in highly qual­ified peo­ple, es­pe­cially those brilli­ant tal­ents who could con­tribute so ably to other fields which con­tribute much more to the rest of sci­ence and to hu­man­ity than does high-en­ergy physics. On the other hand, if high-en­ergy physics could be made a ve­hi­cle for in­ter­na­tional co­op­er­a­tion—if the much-dis­cussed in­ter­con­ti­nen­tal 1,000 Bey ac­cel­er­a­tor could in­deed be built as a joint en­ter­prise be­tween East and West—the ex­pense of high-en­ergy physics would be­come a virtue, and the en­ter­prise would re­ceive a higher grade in so­cial merit than I would now be will­ing to as­sign to it.

Third is nu­clear en­ergy. This be­ing largely an ap­plied effort, it is very rele­vant to hu­man welfare. We now re­al­ise that in the resi­d­ual ura­nium and tho­rium o6 the earth’s crust, mankind has an un­limited store of en­ergy—enough to last for mil­lions of years; and that with an effort of only one-tenth of our manned-space effort we could, within ten or fif­teen years, de­velop the re­ac­tors which would tap this re­source. Only rarely do we see ways of per­ma­nently satis­fy­ing one of man’s ma­jor needs—in this case en­ergy. In high-con­ver­sion ra­tio nu­clear re­ac­tors we have such means, and we are close to their achieve­ment. More­over, we be­gin to see ways of ap­ply­ing very large re­ac­tors of this type to re­al­ise an­other great end, the eco­nomic de­sal­i­na­tion of the ocean. Thus, the time is very ripe for ex­ploita­tion. Nu­clear en­ergy rates so highly in the cat­e­gories of tech­ni­cal and so­cial merit and timeli­ness that I be­lieve it de­serves strong sup­port, even if it gets very low marks in the other two cat­e­gories—its per­son­nel and its re­la­tion­ship to the rest of sci­ence. Suffice it to say that in my opinion the sci­en­tific work­ers in the field of nu­clear en­ergy are good and that nu­clear en­ergy in its ba­sic as­pects has vast ram­ifi­ca­tions in other sci­en­tific fields.

Next on the list are the be­havi­oural sci­ences—psy­chol­ogy, so­ciol­ogy, an­thro­pol­ogy, eco­nomics. The work­ers are of high qual­ity; the sci­ences are sig­nifi­cantly re­lated to each other, they are deeply ger­mane to ev­ery as­pect .of hu­man ex­is­tence. In these re­spects the sci­ences de­serve strong pub­lic sup­port. On the other hand, it is not clear to me that the be­havi­oural sci­en­tists, on the whole, see clearly how to at­tack the im­por­tant prob­lems of their sci­ences. For­tu­nately, the to­tal sum in­volved in be­havi­oural sci­ence re­search is now rel­a­tively tiny—as it well must be when what are lack­ing are deeply fruit­ful, and gen­er­ally ac­cepted, points of de­par­ture.

Fi­nally, I come to manned-space ex­plo­ra­tion. The per­son­nel in the pro­gramme are com­pe­tent and ded­i­cated. With re­spect to ripe­ness for ex­ploita­tion, the situ­a­tion seems to me some­what un­clear. Our’ hard­ware’ is in good shape, and we can ex­pect it to get bet­ter—big­ger and more re­li­able boost­ers, bet­ter com­mu­ni­ca­tion sys­tems, etc. What is not clear is the hu­man be­ing’s tol­er­ance of the space en­vi­ron­ment. I do not be­lieve that ei­ther the haz­ards of ra­di­a­tion or of weightless­ness are suffi­ciently ex­plored yet pos­i­tively to guaran­tee suc­cess in our fu­ture manned-space ven­tures. The main ob­jec­tion to spend­ing so much man­power, not to say money, on manned-space ex­plo­ra­tion is its re­mote­ness from hu­man af­fairs, not to say the rest of sci­ence. In this re­spect space (the ex­plo­ra­tion of very large dis­tances) and high-en­ergy physics (the ex­plo­ra­tion of very small dis­tances) are similar, though high-en­ergy physics has the ad­van­tage of greater sci­en­tific val­idity. There are some who ar­gue that the great ad­ven­ture of man into space is not to be judged as sci­ence, but rather as a quasi-sci­en­tific en­ter­prise, jus­tified on the same grounds as those on which we jus­tify other non-sci­en­tific na­tional efforts. The weak­ness of this ar­gu­ment is that space re­quires many, many sci­en­tists and en­g­ineers, and these are badly needed for such mat­ters as clar­ify­ing our civilian defence pos­ture or, for that mat­ter, work­ing out the tech­ni­cal de­tails of arms con­trol and for­eign aid. If space is ruled to be non-sci­en­tific, then it must be bal­anced against other non­scien­tific ex­pen­di­tures like high­ways, schools or civil defence. If we do space-re­search be­cause of pres­tige, then we should ask whether we get more pres­tige from a man on the moon than from suc­cess­ful con­trol of the wa­ter­log­ging prob­lem in Pak­istan’s In­dus Valley Basin. If we do space-re­search be­cause of its mil­i­tary im­pli­ca­tions, we ought to say so—and per­haps the mil­i­tary jus­tifi­ca­tion, at least for de­vel­op­ing big boost­ers, is plau­si­ble, as the Soviet ex­pe­rience with rock­ets makes clear.

In part two, Cri­te­ria for sci­en­tific choice II: The two cul­tures, Wein­berg dis­cusses the choices that we have be­tween gov­ern­men­tal fund­ing of sci­ence or fund­ing of other goods.

For ap­plied sci­ence, he ar­gues that we should eval­u­ate each re­search pro­ject on its own sake, com­pared with other means of get­ting the same re­sult. In­ter­est­ingly, he chooses to use an ex­am­ple of pop­u­la­tion con­trol in In­dia (re­minder that this is the 1960s):

For ex­am­ple, sup­pose we wish to con­trol the growth of pop­u­la­tion in In­dia and sup­pose we have at our dis­posal $200M per year for this pur­pose. We could de­vote most of this sum to in­ves­ti­gat­ing fer­til­ity, to de­vel­op­ing bet­ter con­tra­cep­tive tech­niques, or to study­ing rele­vant so­cial struc­tures in some In­dian village. Or, al­ter­na­tively, we could use the money to buy and dis­tribute ex­ist­ing con­tra­cep­tive equip­ment, such as Griffen­berg rings, per­haps us­ing some of the money as in­cen­tive pay­ment to in­duce women to ac­cept the tech­nique. Which way we spend our money is a mat­ter of tac­tics; ev­i­dently no gen­eral propo­si­tion can tell us how much of our effort ought to be spent on re­search rather than on prac­tice in try­ing to achieve effec­tive birth con­trol in In­dia. The sci­en­tific work that goes to­ward solv­ing this prob­lem ought to com­pete for money with al­ter­na­tive, non-sci­en­tific means of con­trol­ling the growth of pop­u­la­tion in In­dia rather than with the study of, say, the ge­netic code.

He then ar­gues that we should only fund ba­sic sci­ence in the gen­eral “sci­ence bud­get”. That’s be­cause ap­plied sci­ence should be analysed against other al­ter­na­tives for the same goal, and to have both sci­en­tists and non-sci­en­tists should par­ti­ci­pate in the de­ci­sion mak­ing of fund­ing for ap­plied sci­ence.

In “Pas­teur’s Quad­rant”, a (per­sua­sive, in my opinion) ar­gu­ment is made for the de­cou­pling of how deep a study goes and it’s goal—so that re­search could si­mul­ta­neously have el­e­ments of both ba­sic and ap­plied sci­ence. Wein­berg ad­dresses the point that the sep­a­ra­tion be­tween ba­sic and ap­plied sci­ence is vague, like two ex­tremes of a con­tinuum, but doesn’t seem to con­ceive of it as two or­thog­o­nal prop­er­ties. This has some im­pact on the con­clu­sion above, which I’d amend to be that there should be al­lo­cated fund­ing for knowl­edge-driven sci­ence, and that should per­haps in­clude par­tial sup­port for ap­plied sci­ence which has good sci­en­tific merit by it­self.

He then com­pares pure ba­sic sci­ence to art, and in the end ar­gues that un­til we will solve so­cietal is­sues and be able to have or­di­nary cit­i­zens par­ti­ci­pate in the sci­en­tific pro­cess, we should pre­fer to fund ba­sic sci­ence purely by its down­stream im­pact on tech and so­ciety.

About the im­pacts of ba­sic sci­ence on so­ciety, he ar­gues that ba­sic sci­ence should be funded as a fixed per­centage of the funds go­ing into pos­si­ble down­stream ap­plied sci­ence dis­ci­plines. So that, for ex­am­ple, Biol­ogy fund­ing should be pro­por­tional to Agri­cul­ture and Medicine fund­ing.