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:
- Technological merit - for a given technological goal, support the necessary knowledge.
- 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).
- 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.