Category Archives: Natural Classification

This is part of a series of first rough drafts of a book I am working on with Dr Malte Ebach of UNSW. It is not citeable nor is it necessarily clear or correct.

by | February 15, 2013

My latest paper

Science & Education, February 2013, Volume 22, Issue 2, pp 221-240

Biological Essentialism and the Tidal Change of Natural Kinds

Abstract

The vision of natural kinds that is most common in the modern philosophy of biology, particularly with respect to the question whether species and other taxa are natural kinds, is based on a revision of the notion by Mill in A System of Logic. However, there was another conception that Whewell had previously captured well, which taxonomists have always employed, of kinds as being types that need not have necessary and sufficient characters and properties, or essences. These competing views employ different approaches to scientific methodologies: Mill’s class-kinds are not formed by induction but by deduction, while Whewell’s type-kinds are inductive. More recently, phylogenetic kinds (clades, or monophyletic-kinds) are inductively projectible, and escape Mill’s strictures. Mill’s version represents a shift in the notions of kinds from the biological to the physical sciences.

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Filed under Epistemology, Metaphysics, Natural Classification, Systematics

by | February 3, 2013

The relation of classification to abductive reasoning

Deer tracks in the snow

Deer tracks in the snow.

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.

References

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.

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Filed under Epistemology, Natural Classification, Philosophy, Science, Species and systematics, Systematics

by | January 27, 2013

Pattern recognition: neither deduction nor induction

NewImage

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.

References

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.

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Filed under Epistemology, Natural Classification, Philosophy, Science, Systematics

by | December 24, 2012

Classification and the DSM

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.[1] 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. [2]

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. [3]

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. [4]

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.

3. For example, the Canadian Medical Association Journal editorial, 10 December 2012. Child psychiatrist Claudia Gold refers to DSM-V as a “care rationing document”.

4. Kupfer and Regier 2011, Regier, et al. 2009.

References

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.

 

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Filed under Epistemology, General Science, History, Natural Classification

by | December 19, 2012

Classification and the periodic table

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).

Mendeleev's first published table, 1869

Until Dmitri Mendeleev’s table was published in 1869, the best previous version was that of Julius Lothar Meyer,[1] 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.[2]

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.

1. Scerri gives notice of at least four later “precursors”, Emile Beguyer De Chancourtois, Gustavus Hinrichs, John Newlands and William Odling, who proposed some of the features later credited to Mendeleev.
2. Scerri 2012 has argued that Weisberg 2007 is wrong to think Mendeleev was producing, inadvertently or otherwise, a model. He proposes that classification is a kind of “sideways explanations”. This need not affect Weisberg’s view of the importance of models (since he allowed that Mendeleev was not actually making models, but gave a hypothetical interpretation in which he was), but it is indicative of the lack of philosophical attention generally given to what he calls mere classifications.
 

References

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.

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Filed under General Science, History, Natural Classification, Philosophy, Science

by | December 7, 2012

Evopsychopathy 2: The phylogenetic bracket

As noted, SB and EP have a very unfortunate tendency to reflect the status quo in their results and research questions. This is not unique to them. History, sociology, other fields of psychology (psychotherapy for gods’ sake!), and in my own profession, ethics, all have this “Pull of Privilege”. Somehow the results of this research generally seem to show how natural and right things are. I am always amazed that no matter how radical the ethical foundations in philosophy, ethics always seems to end up supporting the bourgeois status quo (Peter Singer, whose approach I disagree with, is an honourable exception – he’s not afraid to follow his ethical foundations wherever they lead).

This Pull is very hard to shake off. Historians of science (and more recently historians in general) have a term for it: The Whig Interpretation of History, AKA whiggism (also triumphalism, or presentism, ). It is widely, and rightly, seen as a sin of interpretation. Why? It is because if you wish to understand the subject under investigation, rather than tell a story that makes you feel warm and comfortable about you and yours, you must to the best degree possible rid yourself of your relative attachments. You can’t see animist religions in terms of Christianity, alchemical practitioners in terms of modern chemistry, or sexuality in the Azande, say, in terms of Middle American marriage practices and categories (or worse, of penguins in terms of those practices).

So defeating the Pull of Privilege is a serious concern in any discipline that studies human behaviours. How can we do it in SB4.0? As it happens, I have Thoughts.

Behavior is quite labile, evolutionarily, and so there has been debate over whether it can be treated as a homology (Brigandt and Griffiths 2007; Hall 2012; Love 2007). However, classes of behaviors can easily been seen to be homologous. For example, most passerine birds have courtship displays which, while individually unique, fall into a shared class of behaviors, and moreover, these dances are very similar within groups such as riflebirds or lyrebirds (Andrew 1961). It is hard to reject the idea that these are homologies, with species-relative instantiations. The entire field of ethology is founded upon investigating both the commonalities and unique differences of behaviors in many groups of organisms.

There is, in palaeontology, a technique known as phylogenetic bracketing (Witmer 1995). If you need to reconstruct something that doesn’t fossilise in a fossil taxon (say, T. rex), you can place it in a phylogenetic tree and see what its surrounding surviving relatives have in the tissues and structures that don’t fossilise. By projection you can presume this is true of the extinct organism. Likewise, if you find a behaviour in known taxa, you can inductively project (Goodman 1954) from the known to the unknown if they are within the same clade. Of course, this only works if the clade happens to be relatively unspecialised, and the greater the evolutionary distance, the less specific you can get (remember: specific and all other words based on the Latin spec- root, are modifications of species). So you may know that all falconiformes have a recurved claw, but you may not be able to confidently predict whether an unobserved species of falconiforme is a hunter or scavenger. You’ll know, though, that it eats meat.

The application of phylogenetic bracketing here should be relatively obvious. If we wish to reduce the Pull, we need to set an objective behavioural baseline for all humans and not just the WEIRDos. We cannot do this from within the milieu of a culture by an act of will or imagination. But we can bracket humans among the Hominoidea, the African Great Ape clade.

For instance, suppose that one knew nothing else about the human species than that it was squarely nested within the Hominoidea . What would we know about that species? The inferential return on that phylogenetic investment is extensive and indefinite. We would know the species had a particular skeletal structure, with, among other things, four limbs ending in five-digit manus, or hands, and that it had a certain visual system, aural system, and so forth, and interacted with the world at a certain macroscale, in what von Uexküll called its Umwelt (1957), or sensed environment. It would have the primate Umwelt, and so interact with commonsense objects (Griffiths and Wilkins 2012). For our purposes here, however, what we would mostly know is that it was a social species with social dominance hierarchies.

Now it is very hard to find animal species that are not in some sense social. At the least they must interact during mating. But sociality comes in degrees ranging from a brief or even displaced social interaction at mating through to care of neonates and, as in chimp, gorilla, and even orang social behaviors, lifelong interaction with conspecifics of all ages. The one thing that marks all primate species, and thus all hominoids, is that they form dominance hierarchies based upon pairwise interactions, with sanctions of both a positive (reward collaborators) and negative (punish defectors) nature. As has been observed in many primate species (chimps, bonobos, various baboons and monkey species), alliances are formed and social deviants are punished (Cronin and Field 2007; de Waal 1982, 1989). We are socially normative apes. Moral strictures and social conformity is what apes do. Achieving high social dominance results in improved health and better mating opportunities (Burnham 2007; Creel 2001). Hence, such behaviors must be expected to play a crucial role in any social institution that may evolve generally in human, which is to say, one particular ape species’, social structures.

But it will not do to take what is observed among bonobos or gorillas and simply apply them directly to our human species. We know that the human species must typically have some social dominance behaviours or dispositions (why I keep referring to dispositions will become clear in a later post on selectionist explanations); we know roughly how they will be formed (through pairwise dominance displays and competitions, mate choice, etc.) and we have some reason to think they will be primarily male biased as all but bonobo dominance hierarchies are (but note: one species defeated the generalisation based on phylogenetic bracketing. This is not an infallible inference methodology, it is, as we philosophers say, defeasible).

Of course, there are differences between hominoid apes and humans in social dominance behavior, as there are between the non-human apes species. Common chimps tend to have a single alpha male, and the hierarchy is always determined by male status and females derive their status from their mates. Status is determined by aggressive competition and mating occurs in proportion to achieved male status. Bonobos, on the other hand have a hierarchy driven by female choice. This reflects their degree of sexual dimorphism: chimp males are on average around 125% the weight of females, while bonobo males are only slightly larger if at all than the females. Gorilla males are up to three times the weight of the females. As a result a single alpha male guards a harem of females against “bachelor” males. The hierarchy is both within the family, and between males in a territory. Humans, like bonobos, have very slight dimorphism: males weigh around 108% of female weight on average. The degree of polygyny (number of female mates per successfully mating male) roughly correlates with size dimorphism. Social hierarchies vary according to species-typical mating strategy.

Which comes first, the strategy or the dimorphism? That is in many ways a silly question; strategies are constantly evolving, largely, I think, in response to ecological conditions, but also there is a large degree of contingency here – what one species might develop will depend on accidental factors that are largely unpredictable relative to another. Dimorphism is both a result of the evolution of mating strategies, and also a cause of it. These things evolve together. Nevertheless, when you find a fossil ape that has massive dimorphism like the gorilla, you can bet it was a harem-style (almost herd-style) social animal.

So what would we predict about humans, if we had just arrived from Mars and been given only a copy of Walker’s Primates of the World without the section on humans? We would first of all predict that they would form dominance hierarchies, and that high status individuals would reward those that conformed to the group norms so formed, and punish those who defected from them. We would predict a slight male dominance over females. We would expect that the progeny of high status individuals will preferentially rise to higher status than those born of low status parents (primate societies are not meritocracies, Silk 2009). We would expect that male dominance relies upon height and musculature – the bigger males tend to gain higher status even if there is no violence in the dominance behaviours of the species. There are more things we might say, but you see how this applies.

But what would we not be able to predict? Well we would not be able to predict when cultural influences modulate, moderate or even override these social dominance dispositions. We could not have predicted Elizabeth I or Benazir Bhutto (or maybe we could – both were acting as if they were sons of powerful males). We could not predict the rise of liberal democratic ideals, although once it is in play we might predict its eventual corruption and decline as plutocracy and nepotism reasserts itself. We could not predict American supermarkets, although once they are observed we can see some of the foraging dispositions (of males and females) of our predecessors being exploited.

All this does is set up the baseline of expectations. It is not, I think, even remotely possible to give a complete account of societal structures in terms of our shared ape heritage, although that heritage can be ignored at our peril.

I should note that the sort of explanations I am giving (sketching roughly) here are not the outcome of evolutionary psychology per se. Instead, it is the outcome of a number of disparate and only vaguely connected lines of research. Such research covers comparative cognitive psychology (e.g., Suddendorf 2008, a critique of Wynne and Bolhuis 2008), race psychology (Sidanius and Pratto 1999, Sidanius et al. 2000), the effect of status on primate testosterone levels (Anestis 2010, Eisenegger et al. 2011, Gray 2011), the neurology of social behaviour (Harmon-Jones and Winkielman 2007), and so on. Each of these either relies upon something like phylogenetic bracketing (as in comparative psychology) or is consonant with it (as in social dominance psychology).

There are limitations to this method. An inference to homologous traits or behaviours is going to work just to the extent that the species does not have what cladists call an autapomorphy for that trait, which is to say a trait that is unique or in a unique state for that species not shared with other species. For example, the speech centres of the human brain have homologs in other primates, but not as speech centres. Complex grammatical speech is our autapomorphy (and perhaps was also shared by extinct species like H. heidelbergensis, H. neanderthalensis and H. erectus, but we are the sole possessors of it now). So we could not predict symbolic language from a knowledge of other primates.

But the real problem with sociobiological projections is what I call the problem of analogy. Previous SBers would look at eland stamping in a place to attract mates and infer that humans would have “stamping grounds”; that chickens maintained social dominance by the use of violent pecking, and assert that humans had “pecking orders”, and so on. Even ants and bees were used to generate analogies of this kind. But we aren’t ants, bees, elands or chickens.

To infer that we have trait X because all in our clade does is a licensable inference, but much of what we are looking at is not a homology at all (although every trait rests upon underlying homologous structures and systems). Instead they are themselves analogous traits (like shopping, or “rape”*) that may in fact have no homologous dispositions underlying them. Since we want to know what humans should have without ascertainment bias, we must treat these inferences as highly questionable. First you catch your homology. Some real science has to be done.

Moreover, any trait that has been the subject of a selective sweep is, by definition, no longer a homolog in terms of its function. So if something did occur in the X million years since we separated from taxon Y, it is not a homology with Y’s function, even if it is a structural or physiological homolog. So, for example, the role of testosterone among humans may not be (but it actually is according to the research) the same as the role it plays in other primates. You have to check.

So the target of explanation is crucial. I’ll return to this in the next post.

This series:

Cheesy footnote

* Rape is a social and legal term that is often illicitly projected, whiggishly, from humans to other animals like ducks and beetles. Similar objections should be used for terms like “homosexual”, “thief” and so on. Sometimes these terms are harmless, but very often they are not, and mislead us into anthropomorphisms. Caveat lector!

References

Anestis, Stephanie F. 2010. Hormones and social behavior in primates. Evolutionary Anthropology: Issues, News, and Reviews 19 (2):66-78.

Brigandt, Ingo, and Paul Griffiths. 2007. The importance of homology for biology and philosophy. Biology and Philosophy 22 (5):633-641.

Burnham, Terence C. 2007. High-testosterone men reject low ultimatum game offers. Proceedings of the Royal Society B: Biological Sciences 274 (1623):2327-2330.

Butterfield, Herbert. 1931. The Whig interpretation of history. London: G. Bell.

Creel, S. 2001. Social dominance and stress hormones. Trends in Ecology and Evolution 16 (9):491-497.

Cronin, Adam L., and Jeremy Field. 2007. Social aggression in an age-dependent dominance hierarchy. Behaviour 144 (7):753-765.

de Waal, Frans. 1982. Chimpanzee politics: power and sex among apes. London: Cape.
———. 1989. Peacemaking among primates. Cambridge, Mass.: Harvard University Press.

Eisenegger, Christoph, Johannes Haushofer, and Ernst Fehr. 2011. The role of testosterone in social interaction. Trends in Cognitive Sciences 15 (6):263-271.

Gray, Peter B. 2011. The descent of a man’s testosterone. Proceedings of the National Academy of Sciences 108 (39):16141-16142.

Goodman, Nelson. 1954. Fact, fiction and forecast. London: University of London, The Athlone Press.

Hall, A. Rupert. 1983. On whiggism. History of science; an annual review of literature, research and teaching 21 (51):45-59.

Hall, Brian K. 2012. Homology, homoplasy, novelty, and behavior. Dev Psychobiol. Early online. DOI: 10.1002/dev.21039

Harmon-Jones, Eddie, and Piotr Winkielman, eds. 2007. Social neuroscience: Integrating biological and psychological explanations of social behavior. New York: The Guilford Press.

Love, Alan. 2007. Functional homology and homology of function: biological concepts and philosophical consequences. Biology and Philosophy 22 (5):691-708.

Nowak, Ronald M. 1999. Walker’s primates of the world. Baltimore, MD: Johns Hopkins University Press.

Sidanius, Jim, and Felicia Pratto. 1999. Social dominance: an intergroup theory of social hierarchy and oppression. Cambridge, UK; New York: Cambridge University Press.

Sidanius, James, S. Levin, J. Liu, and Felicia Pratto. 2000. Social dominance orientation, anti-egalitarianism and the political psychology of gender: an extension and cross-cultural replication. European Journal of Social Psychology 30 (1):41-67.

Silk, Joan B. 2009. Nepotistic cooperation in non-human primate groups. Phil. Trans. R. Soc. B 364:3243–3254.

Suddendorf, Thomas. 2008. Explaining human cognitive autapomorphies. Behavioral and Brain Sciences 31 (02):147-148.

Uexküll, Jakob von. 1957. A Stroll through the Worlds of Animals and Men: A Picture Book of Invisible Worlds. In Instinctive Behavior: The Development of a Modern Concept, edited by C. H. Schiller. New York: International Universities Press:5-80.

Wilkins, John S., and Paul E. Griffiths. 2012. Evolutionary debunking arguments in three domains: Fact, value, and religion. In A New Science of Religion, edited by J. Maclaurin and G. Dawes. Chicago: University of Chicago Press.

Witmer, Lawrence M. 1995. The extant phylogenetic bracket and the importance of reconstructing soft tissues in fossils. In Functional morphology in vertebrate paleontology, edited by J. Thomason. Cambridge UK; New York: University of Cambridge Press:19-33.

Wynne, Clive D. L., and Johan J. Bolhuis. 2008. Minding the gap: Why there is still no theory in comparative psychology. Behavioral and Brain Sciences 31 (02):152-153.

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Filed under Epistemology, Evolution, Logic and philosophy, Natural Classification, Social dominance, Species and systematics, Systematics

by | November 26, 2012

The classification of clouds

[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)).

Bibliography

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.

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Filed under History, Natural Classification, Science, Species and systematics, Systematics