The Nature of Evolutionary Biology

DarwinAs part of my occasional series devoted to my own technical papers (forgive the self indulgence, but I’d like that body of work to be known to, if not appreciated by, a slightly wider audience than my academic colleagues), let’s discuss the nature of evolutionary biology as a scientific discipline.

The occasion is provided by a paper I published in a collection put together by K. Kampourakis, entitled The Philosophy of Biology: A Companion for Educators. (The book, here, is pretty expensive; my chapter can be downloaded for free here.)

For some reason, the scientific status of evolutionary theory has always been questioned, and I don’t mean just by creationists. Darwin’s famous “long argument” laying out the foundations of the new field of evolutionary biology, was seen as ill-fitting with both of the major philosophical views of how science works that were being debated in late nineteenth century Victorian England. This is known as the great induction debate, and featured a who’s who of early philosophy of science, with John Stuart Mill and William Whewell (the man who coined the term “scientist” in 1834).

Darwin got in trouble with both Mill and Whewell because they both regarded Darwin’s work as an example of deductive reasoning, not of induction (whitch they both favored as a scientifically-sound means of reasoning). According to Mill and Whewell’s understanding, what Darwin had done was to arrive at a hasty generalization based on a small number of observations, proceeding then (deductively) to derive consequences from them, and finally collecting data for decades to back up his hasty conclusions.

Needless to say, Darwin was taken aback by all this, particularly by Whewell’s criticism, since he had been the latter’s student. Indeed, in apparent frustration, Darwin wrote to a friend: “How odd it is that anyone should not see that all observation must be for or against some view if it is to be of service!” — a sentiment that is ironically perfectly consonant with Whewell’s idea of inference to the best explanation.

The next big battle for the soul of evolutionary biology was the famous, decade-long, debate between two of the founding fathers of population genetics, Ronald Fisher and Sewall Wright. The history of this debate, and the role it played in population genetics, is both complex and fascinating. Fisher was convinced of the absolute preeminence of natural selection in shaping organismal evolution, so much so that he consciously modeled his famous fundamental theorem after the second principle of thermodynamics, one of the most successful laws formulated within the dominant experimental science, physics. Wright, on the other hand, was attracted by the complexity and messiness of biology, and his emphasis was always on non-linear, non-additive genetic effects (epistasis, or gene-gene interaction, and pleiotropy, the fact that the same gene can affect a number of traits). Most famously, Wright was interested in the role of genetic drift in evolution, a stochastic process of population sampling that he regarded as countering, and some times even nullifying, the role of natural selection.

Back in 2006, Jonathan Kaplan and I have suggested a way to conceptualize the balance between natural selection and drift, an approach that might be helpful as part of a general understanding of the respective roles of chance and necessity in evolution. Instead of thinking of drift as a force antagonistic to selection, we can visualize it it as a measure of the “error” surrounding the expected evolutionary change caused by selection. According to this way of thinking, if the target of selection is a particular phenotypic value of a given trait (in a certain environment, of course), then there is a probability distribution that tells us how likely the population actually is to land on that phenotypic target. The smaller the population, the larger the error around the selective target, i.e., the larger the drift. This means that the efficacy of natural selection is directly proportional to the size of the population, just like Fisher maintained. But it is also true, as Wright thought, that if the population is small enough, then the stochastic effect of the drift “error” may completely override natural selection’s push.

The latter part of the twentieth century saw the opening of yet another front in the seemingly perennial discussion about the relative role of chance events in evolutionary biology, as well as about the status of the discipline as historical and yet scientifically fully mature. The main charge was led by Stephen Gould and his associates, with a series of papers that unleashed decades of debates and new research.  The opening salvo by Niles Eldredge and Gould himself was the famous 1972 paper on “punctuated equilibria,” where the standard Darwinian view of gradual evolution was challenged and, by implication, the role of natural selection in shaping long-term evolution somewhat curtailed. The paper argued that at the least in a number of cases evolution proceeds by long periods of stasis — with no detectable phenotypic change — “punctuated” by “sudden” (geologically speaking) bursts of activity. More than four decades later, my sense is that paleontologists are by and large in agreement that Eldredge and Gould basically got it right; neontologists (i.e., largely population biologists), however, are of the opposite opinion.

Much in the above mentioned discussions — like any debate on the nature of science — reflects a certain philosophy of what it means to be doing experimental or historical science. It is therefore a good idea to explicitly deal with that philosophy. An excellent framework for this is provided by a paper published by Carol Cleland in 2002, on the epistemic differences between historical and experimental sciences. Cleland’s pivotal idea is that the two types of science are separated by what she calls an asymmetry of overdetermination. Building on previous work by David Lewis, she explains that “the basic idea is that localized present events overdetermine their causes and underdetermine their effects.”

She elucidates what this means by considering the example of a crime being investigated. Once committed, a crime leaves a number of historical traces, no matter how careful the perpetrator was in erasing as many of them as possible. All it takes for a criminal investigator to figure out what happened is a relatively small number of traces that clearly enough point toward a particular sequence of events. The investigator would then be using a type of induction known as inference to the best explanation (first articulated by Whewell) to pinpoint the culprit. Conversely, the simple act of not committing the crime obviously instantly erases the possibility of any historical trace to be left around. Few currently available clues overdetermine a past event, while so many futures are possible given a particular current state of things that the latter underdetermines the range of futures.

Cleland cashes in this asymmetry of overdetermination by arguing that — contrary to popular wisdom (and to the opinion of many practicing scientists) — there is nothing inherently epistemically superior about experimental over historical science. This is because of two consequences of overdetermination. On the one hand, while experimental scientists have the ability to strictly control the conditions of their experiments, it is that very strictness that limits the scope of applicability of their results: as soon as one widens the settings of a given experiment, different factors begin to interact with each other in complex ways, quickly leading to a large number of possible future outcomes; in other words, predictability is purchased at the expense of generality. On the other hand, while historical traces constantly decay through time, and may disappear forever, the historical scientist often needs only a small amount of them to arrive at a sufficiently accurate reconstruction of what happened — just like the criminal investigator in the hypothetical example of the impossibility of a perfect crime.

Cleland’s account makes sense of some surprising limitations of experimental science, as well as some spectacular successes of historical science. In the first case, it is notable, for instance, that non-equilibrium thermodynamics (for example in its applications to atmospheric physics and climate science) quickly reaches a limit in terms of predictive ability, where complex mathematical models are incapable of generating more than very approximate statistical predictions about the future behavior of complex systems, predictions often accompanied by rapidly expanding margins of error.

In the second case, however, we have for example the success of paleontologists in determining that an extraterrestrial body of massive proportions hit the Earth 65 million years ago, contributing to the extinction of countless numbers of species, chief among them the dinosaurs. The impact was suspected once geologists discovered a worldwide thin layer of iridium in rocks datable to the K/T (Cretaceous/Tertiary) boundary. This led to a search for a crater, the remnants of which were eventually identified off the Yucatan peninsula via satellite imagery. From there, geologists could calculate the size and direction of the impact, and therefore make fresh predictions concerning additional historical traces, for instance those left by the tsunamis that must have hit the western coast of Mexico as a result of the asteroid crush. Sure enough, those traces were found, leading to even more confidence in the conclusion that “the crime” had indeed taken place in the way it had been hypothesized.

Despite, or perhaps because, of all the controversies,  these are exciting times for evolutionary biology, both in terms of empirical discoveries (such as those resulting from the so-called “evo-devo” approach, or from comparative genomics) and conceptual advances (e.g., discussions of new ideas, like evolvability, emergent complexity, and others). And while it is true, as Nobel winner Jacques Monod said, that “even today a good many distinguished minds seem unable to accept or even to understand that from a source of noise natural selection could quite unaided have drawn all the music of the biosphere,” that understanding is getting richer and deeper, but it still hinges on taking seriously the dichotomy and interaction between stochasticity (“drift”) and determinism (natural selection).

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Categories: Philosophy of Science

56 replies

  1. Coel,

    ” ‘Scientific’ reasoning is an aspiration to high-quality reasoning; bad science is when we (as humans) fall short”

    I guess what I mean is the term scientific is used in all kinds of situations to mean high quality reasoning but in some of those, and probably a lot if not most cases, the claim isn’t actually backed up. For example I don’t know the number of times I’ve seen “scientifically proven” or “based on scientific evidence” when it was anything but that.

    “But, my point is that there is no style of valid, high-quality reasoning that science will refuse to make use of because it is “not science”; science is pragmatic and will use anything useful that it can get its hands on.”

    I agree science will accept a method or practice once it is considered to be helpful, and that’s what happened once deduction became accepted, and today we can assume that we have a lot of scientists, and maybe a majority, who also are not on board what a new line of promising thought.

    “Thus I agree with Couvent that science will always use experimental methods where it can because they are so useful — but where it can’t, such as historical sciences, it can still make progress by other methods.”

    I’m not sure if you mean experimental is better than historical, it seem wrong to me, I really don’t know much on the subject but my first impression is that it makes more sense to ground experimental science in historical science than vice versa.

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  2. Marc, not to mention medicine & social sciences, with loose p-values and other control, where ‘scientifically proven’ is subject to overthrow.

    Brodix: Panspermia ultimately just punts backward the abiogenesis issue.

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  3. Socratic,

    That wasn’t the issue. It was originally about the mechanism of punctuated equilibrium.

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  4. Couvent,

    “I studied physics, but I’m not a fundamentalist”

    That was a (poor) joke on my part.

    “I don’t like the (in my view false) dichotomy between historical and experimental sciences because the historical sciences make use of experimental science too if they can.”

    As with most things, it’s a continuum. But paleontology and astronomy are pretty much entirely historical, fundamental physics pretty much entirely experimental, and ecology and evobio somewhere in the middle.

    “Fine with me, but then one should use the same yardstick to judge the success of the historical sciences. So yes, I’m deeply sorry, but I think the example is silly”

    Again I wonder why people can’t shift to more productive and less off-putting language. It isn’t “silly,” though you may think it inappropriate, or inadequate. And at any rate, the yardstick used by Cleland’s *is* the same: predictability.

    “*If* historical scientist were able to make such a step, *then* they would certainly make it.”

    Not necessarily. I explained the debates in ecology and evobio: field biologists often reject, or at the least are very careful about the results of controlled experiments because it isn’t clear how much the artificial conditions vitiate them. That’s a good reason to reject the sweeping claim that experiments are always better than observation, which is what Cleland is after.

    Liked by 2 people

  5. Hi Marc,

    I’m not sure if you mean experimental is better than historical, it seem wrong to me, I really don’t know much on the subject but my first impression is that it makes more sense to ground experimental science in historical science than vice versa.

    It’s not really sensible to ask whether experimental or historical science is “better”. If you can do experiments then great, it’s an extra tool, in addition to all the other tools; if you can’t do experiments then ok, you use the tools you do have. Nor, from a Quinean-web perspective, does it make sense to ask which is more foundational.

    Massimo is right that in complex scenarios such as ecology, relevant experiments may be too hard to do and that experiments that can be done may be too contrived to be that useful. (You can bet that *if* ecologists had the capability to duplicate an ecosystem 1000 times, tweak any variables, and then fast-forward a million years, then they’d be doing such experiments all the time; the fact that they can’t is a practical limitation, whereas you can do the equivalent in, say, solid-state physics.)

    But, such distinctions: inductive vs deductive, experimental vs historical, etc, just seem weird to me — you just use everything you can within practical limitations. Can you do science just fine without experiments? Yes. Would you use relevant and appropriate experiments if you could? Yes, of course.

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  6. I’ve now read the Pence (2010) paper on the extent to which Darwin was influenced by and deliberately following the methodology of Whewell and John Herschel in writing the OofS. Pence largely disagrees with Ruse (1975, 2000) that Massimo cites, but he does argue that Darwin was consciously following Herschel’s methodology.

    The summary quote is:

    “It is, however, impossible to argue that Herschel’s thought on methodology did not influence Darwin. We have seen Darwin’s argument [in OofS] unfold in precisely the way that we would expect given a desire to hold oneself to Herschel’s methodological canons. Darwin begins by proposing a speculative hypothesis, grounded on an extensive analogical basis. He then sequentially follows Herschel’s steps for the verification of that hypothesis, first demonstrating its adequacy and then its ability to account for a wide variety of phenomena which it was not originally proposed to explain.”

    Hmm, possibly. But, on the other hand, that methodology is surely pretty obvious. So Herschel states the obvious, and then Darwin does the obvious. Or am I misjudging; was that way of setting out at argument a lot less obvious in the 19th century?

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  7. Even historically sciences can make predictions about things they haven’t dug up yet or found yet. E.g., what they will find in cores from the KT meteor.

    I also don’t see difficulty predicting weather as a failure. They understand why it’s a difficult (‘chaos’) and will likely turn out to be all too good at predicting climate (i.e., averaging over longer time scales). And weather has improved and is saving lives. Things are a lot better than when ‘tomorrow will be the same as today’ was a better prediction than the weather report [a]. This is partially theory input to faster computers and partially instrumentation (follow the Hurricane, see how strong it is from above) and fly a plane threw it!

    [a] In Champagne-Urbana the prediction tomorrow will be the same as Iowa today’ may have been a little better ::|:

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  8. Coel,

    “So Herschel states the obvious, and then Darwin does the obvious. Or am I misjudging; was that way of setting out at argument a lot less obvious in the 19th century?”

    Which goes to the fact that the past(cause) is over determined and the future(effect) is underdetermined. Hind sight is 20/20, foresight is not.

    We don’t know what we don’t know, until we know it, then it seems obvious.

    One can only wonder what in hundred years will seem obvious, but remains a mystery today.

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  9. We are born knowing it all and spend our lives learning otherwise.

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  10. I suppose from a neat, objective, scientistic world view, where controlled experiments are the ideal, understanding the top down, teleological, theistic world, that would be a natural consequence of the inherently political reality in which humanity evolved and which understanding the intentions of other entities was paramount, it might be difficult to appreciate the context in which Darwin was coming from.

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  11. Way back in 1974 R C Lewontin wrote “The analysis of variance and the analysis of causes”. Worth reading.

    Also another conflict was associated with the rediscovery of Mendel around 1900 –
    http://www.nature.com/news/teach-students-the-biology-of-their-time-1.19936

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  12. Michael,

    That paper by Lewontin, which I read a few years later when in undergraduate school, is what guided most of my career as a biologist. And I had the honor of telling that to Lewontin when I was in graduate school and he was visiting the University of Connecticut.

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  13. Given your post, I imagined that you were well aware of it. I think I first ran across it when I was teaching statistics for biology undergrads.

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  14. The nice thing about experiments is that you don’t actually have to understand how your intervention works. That is, you know cause and effect but not necessarily mechanism.

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  15. (Brodix)The opposite position would be that experimental science is a subset of historical science. Given that it has to exist in and support a larger body of evidence.

    Continuing the crime-investigation metaphor, the nerds in the forensic lab complement the cops knocking on doors.

    (Massimo) But let’s remember that by far the majority of the biomass on the planet is made of bacteria, among the simplest organisms there are.

    We are, in a way, footnotes to bacteria.

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  16. wtc,

    Also bacteria keep it simple and consequently are much less prone to punctuate.

    Other than reaching the edge of the petri dish, but those don’t generally occur outside the lab.

    Hard enough keeping them off satellites.

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  17. Continuing the crime-investigation metaphor, the nerds in the forensic lab complement the cops knocking on doors

    Forensic ‘science’ is not very scientific. They don’t often use validate their methods, use controls or do finger prints or bullet matching blind. Quite a few people are unjustly in jail as a result.

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  18. Arthur,

    There seem to be similar issues in other fields as well, apparently. Notably medical research.

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  19. One of the great miscarriages of justice in Australia, the Lindy Chamberlain case, featured some very confident statements from the forensic scientists which turned out to be nonsense. In particular there was a blood stain which they identified as infant blood. It turned out to be a particular kind of car paint. I think that even I could tell car paint from blood.

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  20. There have been a couple of recent theories in (or about) biology which have raised the question for me of, how do you demonstrate something is true.

    The first, featured prominently in New Scientist*, that the gene regulatory network acts as a kind of neural network, storing generic phenotypes and retrieving them later in evolutionary history when they are again useful.

    Well, I’ll eat my hat if that is true, but then again I am no scientist.

    The other seems to demand to be taken more seriously, the idea that the rise of life is a response to the second law of thermodynamics. I admit to be on shaky grounds when it comes to thermodynamics but they way they talk of 2LT as being some kind of prime directive for matter which systems have to find a strategy to achieve doesn’t jell with my understanding of it. I understand it as a statistical fact about dynamic systems – they will move to states with more possible microstates, precisely because there are more possible microstates – so it is just the more likely state.

    Now obviously if I am right about that then physicists and biologists know this too 🙂 so I am clearly missing something.

    So, from the standpoint of increasing my own understanding of these theories in particular but also of understanding the way scientists demonstrate that something is true, I am interested in how they go about moving from interesting speculation to something which could reasonably be called a scientific fact.

    * I was going to say that the fact that it was featured prominently in the New Scientist was a clue that it was a no-goer, but I get told off for being snide.

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  21. Hi Robin,

    I understand it as a statistical fact about dynamic systems – they will move to states with more possible microstates, precisely because there are more possible microstates – so it is just the more likely state.

    Correct.

    Now obviously if I am right about that then physicists and biologists know this too:) so I am clearly missing something.

    It’s hard to say without reading the article in question, but the missing factor could be the “journalistic” tendency of New Scientist. This is, afterall, the magazine that specialises in lurid “Darwin was wrong” headlines.

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  22. Hi Coel,

    Thanks for the confirmation.

    I read the first theory in the NS but the other was some other magazine, I will find and link. But, yes, it doesn’t help to be always reading these things through the filter of simplifying and sensationalising journalism.

    The NS ‘Darwin was Wrong’ front page was a low point.

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  23. Forensic science (like all science) is a work in progress, and it is to be hoped that the mistakes of the past will be ameliorated, and in many cases, corrected in time to reverse faulty convictions (e.g. through DNA evidence). There is, however, the risk that its “scientific” status will count as absolute truth in an adversarial justice system that is often little more than a glorified trial by combat or ordeal.

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  24. Even in DNA they misuse it in testimony. They claim 5 Billion to one odds against a false-match. And while that is likely true for spastically odds of an accidental miss-match, it does not include ‘systematic’ errors like contamination.

    While it may be unlikely that Detective van Adder (sp?) fiddled with OJ’s DNA, the odds against it are not 5B to 1.

    And they call the Jury stupid for not understanding DNA. The jury may not have understood DNA, but they understood cops.

    Bill Maher I think got it right. “The cops were so incompetent they couldn’t frame a quilty man.”

    If you want I’ll tell you about Steven Lucas, convicted of murdering his mother based on incorrect testimony about conservation of angular momentum. He still in jail twenty some years later.

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  25. Even scientists jump to conclusions?
    Well, I’ll be.

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  26. admit to be on shaky grounds when it comes to thermodynamics but they way they talk of 2LT as being some kind of prime directive for matter which systems have to find a strategy to achieve doesn’t jell with my understanding of it.

    Sounds like new age horse pucky to me. Earth is not in thermo equilibrium. Life depends on NOT being in thermo equilibrium.

    I hope it’s not a physicist or biologist proposing the above.

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