In this post, I want to propose my own view, or rather the views I have come to accept, about the nature of science.
There are three major phases in the philosophical view of science. The first was around in the nineteenth century – science is the use of inductive logic based on data to draw conclusions about the laws of nature. Thick books described this in detail, and they are still worth reading, in particular a book by W. Stanley Jevons, The Principles of Science, published in the 1870s. But induction, as anyone who has studied Hume knows, is problematic. You simply cannot justify any inductive inference non-circularly. So along came Karl Popper, who did away with induction entirely, replacing it with falsification. Popper thought that it really didn’t matter what you did to come up with a hypothesis – you could dream it like Kekule or use numerology. So long as the hypothesis could be tested and was liable to be shown false if the data indicated it, it was scientific. Popper’s targets here were Marxist economics and Freudian psychoanalytics, both of which he thought were pseudosciences.
Critics of Popper pointed out that (1) you really can’t falsify a hypothesis on its own – if you test a claim, you also test all the assumptions, ancilliary hypotheses, experimental techniques, and so forth that are used in the test. For instance, you test the veracity of the view down a microscope and the laws of optics it requires, or the interpretation of your gel phoresis and the laws of chemistry, etc., when you try to test if a particular cell will divide or necrose in a solution, and which genes are active when that happens. Falsification is a logical truth, and a practical nightmare.
The other criticism is (2) that scientists really do have a method of discovery. Nobody goes into a gravel pit and counts stones, as Darwin once said, to do geology. You know from the past what sorts of protocols will deliver good results, and you apply them. Why? Popper has no real answer to this, and so he leaves out of the picture vast swathes of actual science. Despite his book being titled in English The Logic of Scientific Discovery, that is precisely what it is not about. Moreover, Popper leaves out of the equation one aspect of science that I think is rather crucial, and that is classification, or the organisation of knowledge into general classes or types, from which inferences can be made.
Thomas Kuhn, who is no doubt in purgatory for unleashing the term “paradigm shift” into the English language, on the other hand, denied there was one single scientific method, but rather that each “paradigm” came along with its own rules, methods, and concepts. In between paradigm shifts, science sort of plodded along, but the really great advances occurred when the whole thing underwent a revolution. He never satisfactorily explained why these revolutions constituted an advance, in my opinion.
Subsequent philosophy of science lacked this grandiose systematic account of science, but it did get a lot more realistic and faithful to scientific practice. Still, the problem of why hypotheses and theories and even, if you think they’re real, paradigms, change over time and get better remained problematic. In short, why is scientific progress not unreasonable?
The philosopher of biology David Hull, who had previously studied systematists as his research organisms, came up with a “Darwinian” solution. Hull pointed out that, like in systematics, there was a distinction between grades and clades, between timeless truths and historically mediated ideas, between, as it were, identity of definition and the identity of descent.
In Hull’s view, science was a series of traditional hypotheses generated in all kinds of ways, using local logic and method, and tested in local ways. What drove the whole process, though, was two-fold – science is a division of labor, and so it is whether the expert community accepts or rejects the hypothesis that matters; and individually and corporately, scientists are motivated by a desire, consciously or not, for what he called “conceptual inclusive credit”. The latter is like being cited, or being part of cited research groups, or being within the tradition or school of accepted research, and is deliberately analogous to Hamilton’s notion of inclusive fitness.
Consider a new scientist, freshly minted, wondering how to advance her career. What can she do? She can try to find a niche in some established research program, or she can try to strike out on her own. If she does the latter, funding, lab space, students and positions will be harder to come by, because these things come from institutions that are already committed to some prior program. If she does the former, then the chances of making a solid discovery are less, because there’s so much competition.
This is formally equivalent, said Hull, to the sorts of evolutionary “strategies” one finds in populations of organisms and genes (we should always remember Ghiselin’s comment that the only strategists in evolutionary biology are evolutionary biologists – it doesn’t matter for an evolutionary account if the players are aware of their strategies or not). And like a one locus/two allele case in genetics, there will be a distribution in the population of strategies adopted. Some will go for radical approaches, others for conservative – the mode will tend to be a little ahead of the median, because the risk will be small but the payoffs will be reasonable. It really depends on how well exploited that research problem is. But science is populational, indeed it is demic – ideas that are successful will be reproduced in the fertile minds of grad students and other scientists who can see a way to make use of it for their own inclusive credit, and the funding agencies and so forth will follow along the successful areas.
Hull’s explanation for the progress of science is that this is a “hidden hand” process – like Adam Smith’s market economy, we achieve a result that no part of the system governs, but which tends to maximise or at least increase the overall “capital” in the system; the capital here being workable ideas in science.
Now the reasons why I like this view is that it allows for flexibility in method, process and conception, and is a purely descriptive account of scientific progress. Hull doesn’t try to teach the birds to fly. He is a da Vinci noting how they actually do. But there’s a nasty catch in this “conceptual selection” view of science. Sometimes, it fails.
Anyone who has studied game theory knows of the Tragedy of the Commons – if a common field will support a little more than one sheep for each farmer, someone will eventually graze two sheep, forcing everyone else to do the same thing, and destroy the commons through overgrazing. Markets can, through selection, overgraze their resources. Science can do the same thing. In an evolutionary process, once you have reached a particular peak in the fitness landscape, if selection is strong you cannot move to another higher peak. If you stay there and grow the “population” of grazers, in this case scientists, eventually you are either going to distribute too little resources to too many folk, for resources aren’t infinite, and reach a carrying capacity, or you are going to select for more voracious grazers, I mean grant getters, which will reduce the chances of further advancement by new scientists. But science progresses along from peak to peak, so perhaps this is not the whole story.
For selection to work, there needs to be a fitness landscape, where each possible combination of genes or ideas has a fitness value. The fitness of ideas in science is largely empirical – if it matches the data, or can be used to generate more data that is consonant with the idea, then it is a fit idea. Of course, ideas in science, like genes in biology, are in a constant state of flux, and while you may get some sort of core genome over time, new combinations are constantly being tried out. If there were a determinate scientific method, eventually this would be exhausted, and so the discipline or research program would dry up. But if methods as well as hypotheses are in flux too, then there is always something new to try. That which generates promising avenues of research is more likely to be followed up because it is a better bet for generating the credit on which scientific careers rely. I make passing mention of the excellent work of Sergey Gavrilets on evolution in adaptive landscapes – according to him, there are almost always “nearly neutral networks” by which high fitness genotypes can drift from one place to another. If this is the case, then science might also be able to wander about from “peak to peak” because they aren’t peaks but ridges. What that does to science as a progressive enterprise, I leave you to consider.
Hull’s view of science is, it seems, sociological, but unlike most sociological accounts of science, it explains the successes of science, sort of. We need to add that science’s “adaptive radiation” was the focus on experiment and observation, and on publicising these reports, as well as using exact measurement, mathematical models, and so on. These happened, at some point in the 17th and 18th centuries, to be socially adaptive ways of gathering knowledge. But will they remain so? Is science still adaptive in the modern world?
I want to now talk about two case studies, as it were. The first is systematics. The second is antievolutionism. You can generalise each to areas that are of interest to you. For instance, the methodology wars in systematics have their close analogues in almost every active discipline, and there are antiscience movements in everything from medicine to ecology.
Systematics used to be a fairly stodgy affair, done often in museums by leading figures, based on what seemed to them to be the appropriate similarities, but it was often the case that a group described by one researcher, which would be left relatively untouched by other researchers until the authority retired or died, was redescribed by a subsequent worker in a different manner.
In the 1930s, impressed by the new developments in formal logic, a philosopher named J. H. Woodger wrote up a new way to conceive of evolving groups in terms of their initiating taxon and successor taxa. One of the things about logic was that it did not happily accept complement sets or overlapping sets – if something fell into two sets, then the sets were misdescribed, and if it was what was left over after some positive set was removed, it was not considered special.
This influenced an East German entomologist who was trying to take the German heritage on evolutionary classifications and put it in clear, logical terms. His name was Willi Hennig, and the kind of systematics he employed came to be known as phylogenetic systematics, or snearingly by its opponents (mostly Ernst Mayr) as “cladistics”. It is by this insult that, like the term Christian, we now know its philosophy and adherents.
The motivation for cladistics was both clarity of reference – taxonomic names had to apply to clades without ambiguity – and a desire to recover the past evolution of a group. The “official” evolutionary view at the time Hennig published, the so-called New Systematics, came to be known as “evolutionary systematics”, and it used both genealogy, which was mostly worked out by impressionistic groupings, and ecological niche or grade. So birds weren’t just evolved from dinosaurs (something I don’t know if they agreed with Huxley on), they also were defined by filling the “flight grade”.
Cladistics took a lot of the subjectivity of classification out of the equation. There were developed all kinds of more or less mechanical algorithms for grouping species, and personal judgement or authority ceased to be an issue. But there was still a choice of which data to put into a cladistic analysis, and before cladistics made it to the English speaking world in 1966, two American researchers, Sokal and Sneath, produced a new kind of “theory-free” classification, relying on the “operationalist” philosophy of physicist turned philosopher Percy Bridgman. This relied on that new technology, computers, to cluster characters of any sort, without any attempt to sort or exclude them, in a metric space, and to call the results Operational Taxonomic Units, or OTUs. The problem with OTUs was that as the variables changed, an organism could find itself in several OTUs simultaneously. It clearly didn’t work as a way of finding “natural” groups.
Cladistics, on the other hand, seemed to offer promise in this regard, and it has taken over the systematics world. Moreover, clades appear to be inductively generalisable – if you know a taxon in a clade has a property, then you can infer that other members of the clade to, so long as the clade is discovered by using other characters than the one you are studying. Another way to put this is that evolution changes things conservatively.
Here is a case in which the birds are following the ornithologists’ lead. Philosophers have offered up general ideas to biology that have informed and guided scientific methodology. Even today there are ongoing debates over whether parsimony or (Bayesian) likelihood is the best way to generate a cladogram for maximum naturalness, although these debates seem to have passed out of the philosophical domain into the straight scientific realm, possibly because of the heavy mathematical load they take. However, one text, by the Bayesian philosopher of science Elliot Sober, Reconstructing the Past is still very influential in this respect.
My second case study has to do with the conservation of the birds and their social ecology; think of it as conservation philosophy.
Challenges to evolution as a way of explaining the world date back almost to the moment Darwin published the Origin of Species in 1859. Theologians often had a go at it for being atheistic or amoral. But it took American religionists to try to argue, first in the 1920s, that in fact evolution wasn’t science, but religion. After the “Monkey trial” in Dayton Ohio, this view submerged, but rose again in the 1960s. A trial held in 1981 in Arkansas included a philosopher of biology named Michael Ruse, a Popperian, who testified that there was a scientific method of falsification, and that creationism wasn’t science because it was not falsifiable. Ruse’s testimony was cited by the judge as a tipping point against those who wanted to teach creationism in science classes in schools.
After this, creationists changed their tack, and rebadged the ideas as “intelligent design”, and claimed that it really, really was science and so should be taught alongside evolution. The catchcry was “teach the controversy”, although the controversy was of their own making and clearly what they wanted was to water down and cast doubt on evolution. Of course, ID never offered any actual science, apart from one book by a biochemist named Michael Behe, and it was pretty loaded with rhetorical devices and logical fallacies. It has been torn apart by many people on philosophical grounds as well as scientific. At a trial in 2005 in Dover PA, the teaching of ID was struck down after testimony from many people, including two philosophers, led the judge (a Bush appointee, no less!) to declare ID was “breathtaking inanity”. This time the philosophical arguments were rather more nuanced, and Steve Fuller, a sociologist of science, argued for the defence that ID was a nascent science. But he also said that astrology might be science too. The most recent incarnation of this undead argument is “critical analysis” of evolution in the classrooms. Watch for it to become the next legal or political challenge in the US. These things affect Australia, and other nations like the Canada, UK, Holland, Denmark and Finland, where IDevotees, as I call them, are funded and guided by American ID interests.
Philosophers from the 1960s to today have argued against antievolutionism on the grounds of the difference between science and nonscience. It is getting less easy to do so on simple grounds, so it is important that we can identify good science even if we can’t define it. Perhaps science is a family of related methods, as Hull’s idea suggests – and those approaches that deviate too far from the best current science, even if they were once within the realm of science in Newton’s or Galileo’s day, can be seen as outgroups. It may be that there really are nascent sciences that can’t be either excluded or included. Only time will tell. But that doesn’t make science a social construct, or more accurately, science is not just a social construct. It is at least that, but so much more.
So the relation between philosophy and science is rather like siblings, to change the metaphor. We have the same parents, and we fight a bit. But we stick up for each other when the family is threatened, and the one spends its time studying what the other one does. Or back to the ornithology metaphor – philosophy of science studies, tests, and occasionally tries to cull science, but our major aim is to conserve it as best we can.
See The Routledge Encyclopedia of Philosophy entry on philosophy of science on line or the entries at the Stanford Encyclopedia of Philosophy:
Books and papers:
Gavrilets, Sergey (2004), Fitness landscapes and the origin of species, Monographs in population biology; v. 41. Princeton, N.J.; Oxford, England: Princeton University Press.
Hull, David L. (1988), Science as a process: an evolutionary account of the social and conceptual development of science. Chicago: University of Chicago Press.
??? (1988), “A mechanism and its metaphysics: An evolutionary account of the social and conceptual development of science”, Biology and Philosophy 3:123-155.
Rosenberg, Alexander (1985), The structure of biological science. Cambridge, UK; New York: Cambridge University Press.
??? (2005), Philosophy of science: a contemporary introduction. 2nd ed, Routledge contemporary introductions to philosophy. New York ; London: Routledge.
Sober, Elliott (1984), The nature of selection: evolutionary theory in philosophical focus. Cambridge, Mass.: MIT Press.
??? (1988), Reconstructing the past: parsimony, evolution, and inference. Cambridge, Mass.: MIT Press.
??? (2000), Philosophy of biology. 2nd ed, Dimensions of philosophy series. Boulder, Colo.: Westview Press.