Biological Essentialism and the Tidal Change of Natural Kinds
Category Archives: Natural Classification
In my last post, commentator DiscoveredJoys raised the question of abductive reasoning and how it relates to my claim that classification is basically pattern recognition. It’s a fair question. First I’ll repeat my response, and then go into it a little more.
In my view, abduction is larger in scope than pattern recognition (PR). PR provides the foundation, but abductive reasoning leaps (usually on the basis of very few observations) to a causal argument or inference, while I am merely talking about the PR itself. PR presents the explicandum for inductive, abductive and deductive explanation.
So I have a much smaller target here. However, I should have thought (and written) about abductive reasoning more. Let me now. Abduction is sometimes called “inference to the best explanation”. Recognition of species, for example, is not, I think, explanatory, but it sets up a problem for the pattern recogniser: why is that pattern there? The usual answer (leapt to immediately on the basis of prior knowledge) is that there is some reproductive power that makes progeny resemble parents. This is the abduction, not the recognition of a pattern. It is the “best explanation” based on a host of prior assumptions and knowledge claims. If we had never seen a living thing (if we were a Matrix style computer), we might not leap to the explanation, but I think we would still recognise the pattern.
Of course the economic argument would not apply, and would rely upon other criteria of salience (maybe the Matrix needs to categorise objects that have functional roles in the simulation).
First of all, what is abduction? The Stanford entry is quite complete and comprehensible (see this also), but basically it is leaping to an explanation from a single or few observations. It is called by the late Peter Lipton Inference to the Best Explanation (IBE). IBE is a principle that you should choose to explain an observation based on the best causal explanation, the most likely based on background knowledge. My commenter suggested that pattern recognition is a form of IBE. I think it is not.
For a start, to make a pattern recognition-based classification does not require positing an explanation. It requires explanation once you have one, which is to say, it sets up an explicandum. To make an IBE, one needs already to know enough to make some explanations more likely than others. Lipton (1991) calls this assessing the “loveliness” of competing hypotheses. But while pattern recognition involves prior knowledge – of the domain and its general properties, mostly what to look for – it doesn’t involve assessing the loveliness of hypotheses. Instead it involves assessing the salience of differing stimuli.
In order to make an IBE, you have to recognise things. Take for example an IBE about what made footprints in the snow. First you have to recognise the pattern of footprints. This is something you have learned to do, not least by making footprints. Second, in order to make an IBE that a deer made these particular tracks, you need to recognise the difference between bipedal and quadrupedal tracks (gotten from years of observing them), and between claws and hoofs (likewise) and so on. With all that categorical apparatus in play, you “leap” to the hypothesis that of the likely animals in the area, it was a deer, not a cat or horse.
But classification is different to that, at least initially when the domain under investigation (DUI) is unexplored. You know about the wider domains in which the DUI is situated, so you are primed to see some sorts of things. But you get an idea of what is in the DUI by looking, a lot. Experience trains you to see patterns, and then, and only then, can you make IBEs. Hence my response above.
There are those who think taxa are explanations. One author, Kirk Fitzhugh (2005, 2009) thinks species are explanations, a view I cannot make sense of. An explanation of why a species is a species is something independent of recognising the species. Others have argued that phylogenies are explanations or hypotheses, in a Popperian fashion. Again, I cannot make sense of this. In the case of phylogenies, the explanation is the theory of common descent (or, in some cases, lateral transfer and introgression through hybridisation), but the phylogenies themselves are patterns in data. If a systematist works out a phylogeny of a group, then there is an IBE of common ancestry (or perhaps a Bayesian inference, which is distinct in the eyes of IBE advocates from abductive inferences), but common ancestry is not the same thing as working out the phylogeny, again, at least initially. Then background information can come into play to revise and refine the phylogenetic systematics, for instance by using molecular clocks or distributional properties, but again, these are further inferential activities to classification.
The relations of different kinds of cognitive activities here are not simple. While it helps us to classify them as distinct activities, in practice we shift and change from one to another, or do them simultaneously. Science is not done by recipe. However, it pays to be clear about the differences between them.
Fitzhugh, Kirk. 2005. The inferential basis of species hypotheses: the solution to defining the term ‘species’. Marine Ecology 26 (3-4):155-165.
———. 2009. Species as Explanatory Hypotheses: Refinements and Implications. Acta Biotheoretica 57 (1):201-248.
Lipton, Peter. 1991. Inference to the best explanation. London: Routledge.
It occurs to me as I read Rosenberg’s Philosophy of Science (2005), that we tend in that field to classify epistemic activities into two kinds: induction (about which we have many arguments as to its warrantability) and deduction (with many arguments about its applicability). But I believe there is something else that we do to learn about what exists in the world. In my forthcoming book, The Nature of Classification, coauthored with Malte Ebach, I argue that this is classification, but typically classification is seen as either of the other two kinds of inference. I think it is a third kind.
So what happens when we classify in the absence of theory? We aren’t yet inductively constructing theory, and we aren’t able to deduce from theory (since there isn’t any yet) the classes of objects in the domain we are investigating. We argue that what is happening here is pattern recognition (Bishop 1995). We are classifier systems. It is one of the distinguishing features of neural network (NN) systems such as those between our ears that they will classify patterns. They do so in an interesting fashion. Rather than being cued by theory or explanatory goals, NNs are cued by stereotypical “training sets”. In effect, in order to see patterns, you need to have prior patterns to train your NN.
Where do these come from? I think that there are several sources. One is evolution: we are observer/classifier systems of a certain kind. This gives us a host of cue types to which we respond by training our stereotype classifier system. For example, we respond to movement of large objects, to differences in colour and shade, and so on, in our optical system. Quine (1953) referred to this as our “quality spaces” – these are fields of discriminata, to which we (in Quine’s view, behaviouralistically) react. They are adaptations to the exigencies of survival for organisms of the kind that we are. The problem is that so long as our survival and reproductive success is ensured, evolution cannot guarantee us access to the way things “really” are. At best it gives us a good balance between false positives and false negatives. It is good enough, as it were, for government work (Godfrey-Smith 1991). But is it good enough for science and metaphysics?
One of the standard accounts of the success of science is that it increasingly approaches the truth. This is called the Ultimate Argument for Scientific Realism by van Fraassen (1980) and the Miracle Argument by Putnam (1975, that unless science does converge on reality, science would be a miracle). It is quite clear that the received dispositions evolution has bequeathed our cognitive capacities is not enough. While one might reject the Plantingan argument against all naturalism based on this insufficiency of our evolved cognitive powers (Plantinga 2002), there is a problem. How do we come to identify aspects of the world reliably and properly?
Science proceeds by refining its categories of what exists in the world based on two main sources. These are evidence, and explanatory force. In the case of a domain of investigation for which there is as yet no explanation, all we have is evidence, but apart from our evolved dispositions to respond to certain stimuli, how do we identify the salient aspects of evidence? There is an almost infinite amount of possible information we might make use of, and so we must glean the right sources of information. One source is economic necessity. Over time, farmers and hunters will tend to respond to the features of the things they are engaged in acquiring and using that are more or less important for success, because those features which are not salient will impose a cost of time and effort that tends to reduce success. This is a process very like natural selection, and has been the basis for what came to be known as evolutionary epistemology, in which a parallel process to biological evolution occurs in the domain of knowledge. Cognitive traditions become better at acquiring reliable knowledge because ideas and approaches that do not aid this goal are costly and are abandoned.
However, we have a superfluity of cognitive and conceptual resources. We can retain ideas and practices that are not really relevant for social reasons, such as rituals and “explanations” that have no counterpart with the reality being dealt with. So the fact that a particular culture is successful at farming by relying upon a ritual calendar (as in pre-Indonesian Bali) doesn’t warrant belief in Hindu gods. The functional aspects of the rituals acts to transmit the information even if nobody in the culture (or in Western agribusiness) fully understands why those rituals make farming successful (Lansing 2007).
So when a classifier recognises patterns in economic circumstances, what counts is not the conceptual superstructure, the theories and ideologies, but the categories of what matters – in this case of water, soil, and landscapes. How might this explain the success of science?
Taxonomists are classifiers in a particular economic situation: professional science. When a taxonomist encounters organisms in the wild, they are in the same situation as when a hunter hunts in that ecology. To succeed at taxonomy, as to succeed at hunting, the agent must know the right things about the target objects. A hunter that doesn’t know what different species of bird look like and how they behave and where they live is in exactly the same economic conditions as a taxonomist who also lacks knowledge. Neither will end up with dinner on the plate (qua hunter or taxonomist). In the case of the taxonomist, the gap between failure and hunger is somewhat more distal than for the hunter (but hunters typically get most of their food from foraging rather than hunting anyway, courtesy of the non hunters, mostly women, in their village), but ultimately economic success depends directly upon correct pattern recognition.
Ernst Mayr was fond of telling the story of how when he visited Papua in the 1930s, he and the local hunters identified the same species of bird, with an exception where western ornithologists also disagreed, and he used this as justification for the reality of those (and all) species. He made the inference that science was able to discover kinds of things that were real in the world, and he may have been right (many biologists and philosophers believe species are not real), but it was not, I think, because of the pattern recognition abilities of humans per se to see species. When Ed Wilson tried the same experiment about ants, a subject he knows intimately, instead of the locals counting the same species he did (several dozens) he got something like “the black ones, the bitey ones and the red ones”. Why did Mayr’s informants know their birds while WIlson’s did not know their ants? The answer is that birds, but not ants, were of economic importance to the locals, while ants were of economic importance to Wilson and entomologists only.
By “economic” I do not mean fiscal, but the acquisition of resources, success at which gives the person investigating a living. What distinguishes scientific success is a unique socioeconomic system of professionalism, credit in society, and access to funds and resources like labs, students, and equipment. The motivations of the individuals concerned are several, often (but not always) based on personal curiosity, but curiosity is not enough if you don’t get the resources to do the work.
So we are very good at turning our perceptual pattern recognition systems to scientific work. What evolution provides, science refines. It happens that pattern recognition and the subsequent classificatory activities can deliver reliable knowledge of the world when it matters. But being as it is parasitic upon those evolved capacities, and being as scientists are social organisms, this is not without its failures. Social influences, particularly the inherited traditions of ritual and conception that history bequeaths, can skew and bias our categories about the world. This is where theory and experiment come in.
Science, by way of its historical accidents, also seeks to explain things in ways that can be tested. Here the ordinary philosophical issues come into play – we inductively generalise based on the patterns we have recognised, and form hypotheses, and from those hypotheses we derive deductive consequences, which we can test in ways that are not circular, which do not rely upon our original observations. As T. H. Huxley once said, nature whispers yes, but shouts NO! And so we can eliminate hypotheses that are not fit to the facts, more or less. This is what the evolutionary epistemologists, and philosophers like Popper, built their views upon. What evolutionary epistemology never explained, nor Popper, was how we came up with those hypotheses in the first place. Pattern recognition does.
For a half century or more we have had the view that observation is theory laden. As I have argued before (and which is part of our forthcoming book), observation need not be laden with theory of the domain under investigation. And what evolution has bequeathed need not be in the slightest theoretical, nor even reliable (as the massive literature on illusions shows us). We can naively observe things that we know little about, but we never start knowing, or at least being disposed to know, nothing.
So can we say that science is adequate to tell us the true nature of the world? Putnam’s miracle argument indicates a reason for thinking the world is knowable. If we could not know the world, there would be no reason to think that success indicated anything. And while success is not a guarantee of truth, it is as good as fallible knowers can ever achieve. In the end, I think that truth is, as the pragmatists said, what works. More than that is restricted to gods, demons and mathematicians.
Bishop, Christopher M. 1995. Neural networks for pattern recognition. Oxford, New York: Clarendon Press; Oxford University Press. [Sorry, I forgot to put this in]
Van Fraassen, Bas C. 1980. The scientific image. Oxford: Clarendon Press.
Godfrey-Smith, Peter. 1991. Signal, decision, action. Journal of Philosophy 88:709-722.
Lansing, J. Stephen. 2007. Priests and programmers: technologies of power in the engineered landscape of Bali. Princeton NJ: Princeton University Press.
Plantinga, Alvin. 2002. The Evolutionary Argument against Naturalism. In Naturalism Defeated? Essays on Plantinga’s Evolutionary Argument against Naturalism, edited by J. K. Beilby. Ithaca, NY: Cornell University Press:1-13.
Putnam, Hilary. 1975. Mind, language, and reality, His Philosophical papers v. 2. Cambridge Eng. ; New York: Cambridge University Press.
Quine, Willard Van Orman. 1953. From a logical point of view: 9 logico-philosophical essays. Cambridge MA: Harvard University Press.
Rosenberg, Alexander. 2005. Philosophy of science: a contemporary introduction. 2nd ed, Routledge contemporary introductions to philosophy. New York; London: Routledge.
More from my forthcoming book with Malte Ebach. Last post for the year, folks.
The Diagnostic and Statistical Manual of Mental Disorders
This text, known by its acronym the DSM (-I, -II-, III or -IV, and -V due in 2013), is the main standard classification of mental illness and disorders used across the world, although it is primarily the production of the American Psychiatric Association (APA). It is not the sole classification, there being also International Statistical Classification of Diseases and Related Health Problems (ICD), produced by the World Health Organization. Both systems are widely used in the context of drug prescription, medical insurance and administration, government statistics, and medical education.
The original system that the DSM-I codified was based upon psychoanalysis categories. DSM-I evolved out of the pre-war “Statistical Manual for the Use of Institutions for the Insane” after the second world war, in 1952, relying strongly upon military terminology and practice during the war, especially the Navy’s. Over the years it was revised extensively, and by DSM-III the APA abandoned the goal of earlier editors and authors to find an etiology for the diseases classified. Since very little in the way of etiologies for the diseases had been uncovered, it was seen that the role of the DSM was to provide practitioners with a way to efficiently and effectively diagnose conditions, and prescribe drug treatments and other treatments.
This meant that the DSM was not a nosology the way classifications of diseases were in medicine. Although medical science might not know what the etiologies of diseases were, the aim and project of medical research and classification was to move from phenomenology to etiology, and when a disease was finally explained in a way that might break it up into several distinct or more general conditions, medical science had little trouble doing so. Psychiatry, on the other hand seemed to move in the opposite direction. Instead of explaining and revising categories based on a knowledge of causal substrate, psychiatry revised based on “general concepts” of mental illness, some of which were in fact lay notions, and upon the availability of drugs to prescribe. What etiological research there was tended to be done by neuro-psychologists and neurologists instead.
The DSM is a case of a classification that is moving away from Theory rather than to it, largely because it is not an attempt at a natural system, but one of convention and operational use. However, the majority of those who employ it seem to think it is a natural scheme. This may retard the progress of psychiatry, as Dom Murphy thinks:
… classification can draw on causal discrimination in the absence of causal understanding. And it can use causal discrimination as a source of hypotheses. If we have good reason to believe [through this classification] that two syndromes depend on different pathologies, then we can orient research around finding out what they are. … The system of classification in the DSM is incoherent, heterogeneous, and provincial. It is incoherent in that it rests on a theory about the taxa of interest that requires symptoms to be expressions of underlying causes whilst at the same time it prohibits mention of these underlying causes in the taxonomy. It is heterogeneous in that it does not classify like with like at appropriate levels of explanation. And it is provincial in that it is cut off from much relevant inquiry. These complaints … reflect worries about the current state of biological psychiatry as a whole, since DSM-IV-TR is its flagship. 
With the approval of the DSM-V in 2012, critics noted in review that it was an amalgam of convenience and in some cases putative special interests. 
Apart from a connection with the available treatments, not all of which are clinically or epidemiologically tested, there is a minimal change of emphasis upon etiology in refining the categories of the manual. Nevertheless, the mere having of a systematic classification generates substantial research programs, and the results of neurobiological research has input much of what etiology there is in psychiatry. 
1. This is based upon the comprehensive research and discussion in Murphy 2006. Although Murphy’s theoretical discussion of classification in chapters 9 and 10 is consonant with ours, we arrived at similar ideas independently and in distinct domains.
2. 2006: 323.
4. Kupfer and Regier 2011, Regier, et al. 2009.
Kupfer, David J., and Darrel A. Regier. 2011. Neuroscience, Clinical Evidence, and the Future of Psychiatric Classification in DSM-5. American Journal of Psychiatry 168 (7):672-674.
Murphy, Dominic. 2006. Psychiatry in the scientific image. Cambridge, MA; London: MIT Press.
Regier, Darrel A., William E. Narrow, Emily A. Kuhl, and David J. Kupfer. 2009. The Conceptual Development of DSM-V. Am J Psychiatry 166 (6):645-650.
Thanks to Dom for providing me with a copy of his wonderful book.
It might be thought that classification in the special and historical sciences is occasionally atheoretical, but that in the general sciences, physics and chemistry, it is derived from Theory. But in fact one of the most exemplary cases of empirical classification that led to Theory is in these sciences: the periodic table.
According to a study by Eric Scerri (2007), the standard textbook story of the periodic table is wrong, unsurprisingly since most such textbook narratives are. The idea of a table of elements did not derive from Dalton’s revival of atomism, but from increasingly refined laboratory techniques for ascertaining the atomic weight of elements. The notion of atoms, of course, did derive from Dalton but these developments did not seemingly rely much upon it. Because samples of element include what we now understand are isotopes, atomic weights are not perfectly correlated with atomic numbers. Consequently while it was apparent from the experimental data as the atomic weights of elements were refined that there was some sort of pattern, e.g., by Stanislao Cannizarro and Alfred Naquet who both arranged these weights in a table, early attempts tended instead to rely on a kind of platonist numerology, Johann Döbereiner’s “theory of triads” in which patterns of elemental properties fell into threefold relations. These were not unlike the affinities of systematics, and indeed the term “affinity” was used by chemists. However, there were too many exceptions for triads to be the basis for a table of elements (although something like it later returned briefly).
Until Dmitri Mendeleev’s table was published in 1869, the best previous version was that of Julius Lothar Meyer, who, like Mendeleev had arranged elements in a series based on their atomic weights. What Mendeleev did that was better than Lothar Meyer and other precursors was to employ his vaster knowledge of the empirical properties of chemical elements, and to make an arrangement based on weights and properties, in a kind of family resemblance (Scerri 2007: 125, 150). He refined it over many years, again based on the experimental results. The term “experimental” here is a little bit misleading, in our terms, because while there was intervention to refine and purify the samples used, this was not intervention to experimentally modify the samples along some independent variable to test a hypothesis. In our terms, it was simple empirical research.
Mendeleev even expressly noted that he was taking a Lockean or even operationalist approach:
. . . by investigating and describing what is visible and open to direct observation by the organs of the senses, we may hope to arrive, first at hypotheses, and afterwards at theories, of what has now to be taken as the basis of our investigations. (quoted in Kultgen 1958: 180)
Subsequent to the adoption of the table by chemists, there arose a program to improve and explain the “periodic law”. As Scerri says, once scientists have a classification, they seek an underlying cause of the regularities (as Darwin did).
Following on from the adoption of atomic theory and the discovery of electrons by Thompson in 1897, and the nuclear structure of the atom proposed by Rutherford, Bohr’s introduction of the quantum to the structure of the atom led to an explanation of valency, which was originally discovered by Edward Frankland and Friedrich Kerkule in the 1860s. Eventually, Rutherford and Antonius van den Broek proposed around 1911 that each atom had an integer number that gave it its weight. About the same time, the discovery of isotopes by Frederick Soddy explained why atomic weights varied: different samples had varying admixtures of the isotopes, whose weights varied.
In short, the periodic table is a mixed case of empirical research guiding theory development. It is not a simple example, because there was prior Theory, and also because much of atomic theory derived from other sources and cases, especially in the study of radioactivity, but nevertheless classification plays a key role in this most central of physical scientific domains.
Kultgen, J. H. 1958. Philosophic Conceptions in Mendeleev’s Principles of Chemistry. Philosophy of Science 25 (3):177-183.
Scerri, Eric R. 2007. The Periodic Table: Its Story and Its Significance. New York: Oxford University Press.
Scerri, Eric R. 2012. A critique of Weisberg’s view on the periodic table and some speculations on the nature of classifications. Foundations of Chemistry.
Weisberg, Michael. 2007. Who is a Modeler? British Journal for the History of Philosophy 58:207–233.
[A segment of my new book, coauthored with Malte Ebach]
The classification of clouds
Clouds were regarded as so subjective, fleeting and resistant to classification that they were a byword for the failure of empirical classification, until Luke Howard in 1802 proposed the foundation for our present system of cloud classification (in competition, although he did not know it, with others in Europe, and on the heels of Hooke and later meteorological language proposals including one by Lamarck the same year.
Howard’s proposal, like Lamarck’s, was driven solely by empirical observations. No experiment was possible with clouds (although there were some schemes for building cloud producing machines early on), and there was no real theory as such, just a desire to, as Lamarck said, note that “clouds have certain general forms which are not at all dependent upon chance but on a state of affairs which it would be useful to recognise and determine” (Hamblyn 2001: 103. This section is taken mostly from Hamblyn’s excellent book). In short, this is an example of a classification scheme without much if anything in the way of Theory.
Howard proposed seven classes (genera) of clouds – three “simple modifications”, cirrus, cumulus, and stratus, two “intermediate modifications”, cirro-cumulus, and cirro-stratus, and two “compound modifications”, cumulo-stratus and cumulo-cirro-stratus, or nimbus. His criteria used apparent density, elevation, height, and whether it produced rain. Particular types of clouds were called, following the logical and Linnaean examples, “species”. He also devised our present system of signs for these cloud types, and proposed a correlation with certain types of rain and clouds. Now meteorologists could communicate and seek explanations and presently the International Cloud Atlas is the global standard for identifying clouds (World Meteorological Organization 1975).
This is a classic example of an empirical passive classification. Although the hydrological cycle was of ancient vintage, the direct Theory of clouds, such as it was, had to await the hypothesis of the thermal theory of cyclones and cloud formation (Kutzbach 1979). Similar passive classifications were done for wind, resulting in the Beaufort Scale.
Howard’s scheme outcompeted Lamarck’s largely because of its technical terminology and signs. Lamarck’s was too French and odd even for them. It gained great acceptance. Johann Wolfgang von Goethe, had written a poem in Howard’s honor, as well as contribute “Towards a Study of Weather” in which he briefly discusses Howard’s categories of clouds and a basic law of weather (Goethe 1825 (1970)).
Goethe, Johann Wolfgang.von. 1825 (1970). Versuch einer Witterungslehre. In Die Schriften zur Naturwissenschaft, edited by D. Kuhn and W. von Engelhardt. Weimer: Hermann Böhlaus Nachfolger:244-268.
Hamblyn, Richard. 2001. The invention of clouds: how an amateur meteorologist forged the language of the skies. London: Picador.
Kutzbach, Gisela. 1979. The thermal theory of cyclones: a history of meteorological thought in the nineteenth century. Boston: American Meteorological Society.
World Meteorological Organization. 1975. International Cloud Atlas. Secretariat of the World Meteorological Organization:155 pp.