Evolution through natural selection is an immensely powerful theory. It is able to synthesize and found the many and various fields within the biological sciences into a coherent, explanatory network. Its explanatory success has in turn led most biologists to regard the phyletic configurations of organisms as aggregates of individual adaptations. Adaptations are gradual, heritable alterations in a phenotype that provide a reproductive benefit(s) to its possessor. That is, these gradual alterations are the result of environmental and sexual constraints and pressures on inherited gene structures.
However, the scientific standing of adaptationism has been called into question. For instance, Karl Popper, in his 1976 autobiography, claimed evolution through natural selection “is not a testable scientific theory but a metaphysical research programme.” (Though, I should note, Popper did- by and large- consider evolution through natural selection a valid scientific endeavor.) Later, Stephen Jay Gould and Richard Lewontin famously made a similar charge in The Spandrels of San Marco and the Panglossian Paradigm. It is clear, then, that if adaptationist hypotheses (and by extension, the received view of natural selection) are to remain scientifically viable, then scientists must devise some way of testing them.
One answer to this challenge is that formal optimality and game theoretic models provide an opportunity to test adaptationist hypotheses. For space constraints, though, I will concentrate on optimality models. Thus, I shall analyze the extent to which optimality models test adaptationist hypotheses in any meaningful sense. In the course of the analysis, however, attention must be paid to the charge that optimality models suffer from a certain, systemic flaw: perpetual revisability.
Formal models are an essential element in modern scientific research. They enable scientists and philosophers of science to make testable predictions within a circumscribed theoretical framework when direct observation and/or laboratory experimentation are impractical or impossible. In biology, formal optimality models are used to predict the phyletic structures of existing organisms, and thus test the many competing and at times complex, ambiguous causal explanations of a given trait’s evolutionary history. In brief, the model analyzes an adaptationist hypothesis much in the same manner an engineer would analyze a technological problem.
The hypothesis in question is broken down into four essential parts: a fitness measure, heritability assumptions, a phenotype set, and a set of state equations, or algorithms. The fitness measure is the manner by which reproductive success is weighed, such as offspring quality and production or energy efficiency in locomotion. Heritability assumptions determine to what extent traits are passed on to successors. While prima facie these assumptions are easily assumed, the probabilistic factors at play in the model are rather complex. Considerations of allelic variation, epistatical variation, and maternal and paternal dominance must be appropriately evaluated and accounted for. The phenotype set lays out the various alternate but possible design configurations within the model. The possible design schemes are layered. That is, upon the development of one design another becomes more or less probable. In other words, an organism’s future phenotypic development is constrained by his phenotypic history. Lastly, the state equations are the set of algorithms that determine how the operative factors within the model will transpire.
While the mathematical equations can be multifarious, their theoretical viability is obtained via other, more rigorous sciences. For instance, if the flight ability of an osprey’s wings is being tested in the model, the state equations will draw upon the laws of aerodynamics, biomechanics, and muscle physiology to help determine their optimality.
From the data inputs and the algorithms, the model will provide predictions that biologists may test against extant organisms or certain phenotypic configurations. Ideally, when the predictions are not confirmed by any positive instance, then the hypothesis in question is falsified. However, rarely is the testing process so simple. As critics of the received view of natural selection are apt to point out, the failure of a model to make accurate predictions is often not regarded as a failure of the hypothesis. What the critics have noticed is that a modeler may modify some aspect of the model so as to make it conform to any future observation. The concern is not so much for the integrity of the modeler; rather, the concern is that the modeler may unwittingly allow his theoretical presuppositions to cloud his scientific integrity. For instance, he may adjust the probability factors in the heritability assumption or even revise the set algorithms because his hypothesis must be correct. Moreover, it is worried that he may continuously modify his model and thus avoid falsifying his hypothesis altogether, which would not bode well for its scientific validity.
To a certain extent this worry is justified. One need only refer to Marxian historicism for a case in point (see Karl Popper’s The Poverty of Historicism). However, the concern is nevertheless much too simple. It seems to rely upon the belief that a single experiment- in our case, a singular model output- is sufficient to falsify an entire hypothesis. While it is indeed possible for such a singular falsifying instance to obtain, such crucial experiments are exceptional. Rather, scientific hypotheses themselves are rarely open to complete falsification. They often exist within a wider theoretical framework that itself has innumerable logical entailments and empirical repercussions. This insight, made both- though in different degrees- by Pierre Duhem and W.V.O. Quine, is known as the Duhem-Quine thesis. This, though, need not detract from the scientific validity of optimality models.
To the contrary, by modifying his model the modeler may be viewed as calibrating it and thus refining its predictions for more accurate testing. For, if within in the course of inputting the data into the model and deriving the predictions some defective bit of information was included- say, for instance, it was derived from faulty generalizations or new evidence warrants its revision- there must exist some procedure for its identification and subsequent correction. If the alterations can be made without significant theoretical modifications, then the model should in all lights be maintained. That is, if the modeler must call upon assumptions at odds with adaptationism, say assumptions of punctuated equilibrium, to conform his model to observational findings, it is then that the adaptationist program should be called into question.
Of course, noting that having to modify a model does not necessarily falsify the hypothesis and the theoretical framework upon which it rests is not to assert that a successful model prediction verifies the hypothesis. Finding positive instances of model predictions means only that it is tentatively accepted. This tentative acceptance, however, should and often does grow in theoretical strength in proportion to the amount of confirming instances: As the number of confirming instances of a hypothesis increase, so to should our acceptance of its utility. To conclude, then, optimality models provide biologists opportunities to test the scientific validity of adaptationist hypotheses; even if the modeler makes numerous modifications to the model’s data set and, perhaps, even to its set equations.
For an excellent exposition of this debate (and more that concern the philosophy of biology) see:
Sterelny, Kim & Griffiths, Paul E. Sex and Death. The University of Chicago Press. Chicago, US. (1999).
I disagree that a scientific theory can be falsified. Popper was wrong and Kuhn offers a more plausible alternative involving Paradigms. What makes a theory stand out is its ability to have less anomalies than another theory. An anomaly (such as dark matter) is indeed a falsification. But we realize that such exceptions can probably be explained away at some point. If not, we might eventually find a better alternative theory.
Aaron,
First of all, great post! I really enjoyed reading it! I found the section where you discuss the falsification of theoretical models to be practically interesting. In particular, the notion of calibration that you employ seems to allow you to sidestep the sorts of problems which plagued Constructive Empiricism- namely that van Fraassen requirement of an isomorphic match between a theory and any observation which purports to confirm it is too strict of a criterion. However, I wonder if you would say more about the distinction between calibrating a theory and simply using a new theory. I am not too familiar with the philosophy of biology, so I can’t think of an example which would be germane to your post, but I do think that I can come up with one from physics that will sufficiently illustrate my concern (I’m sure you are familiar with the example I am about to give, so I won’t spend too much time describing it…). It took Einstein about ten years to get the math right for general relativity, and when an American physicist tried to test the theory by observing stars during a solar eclipse the observations did not match what the theory had predicted. Arthur Eddington did the same sort of test after Einstein had revised the math. I am inclined to think that these two men tested different theories, despite the fact that the macro-concepts of the theories were the same. Asserting the opposite, that the American and Eddington were testing the same theory, would seem to entail that the theory has been both falsified and not falsified. So, anyway, I was wondering how many alterations to a theory can be made before it is a new theory (sort of like a scientific Ship of Theseus) and how you would avoid contradictions (if indeed you think my example actually posses a problem). By the way, I am not asking these questions because I disagree with you, rather I am quite interested in/sympathetic to this project but I am not sure how I would deal with these objections (or if I am just confusing myself).
James,
Popper’s theory may not be completely correct, but I don’t think that falsification needs to be completely done away with. Furthermore, I think that Aaron’s use of falsification is at least, prima facie, unproblematic. Additionally, I think you are wrong on Kuhn. First of all, Kuhn does not use the idea of falsification and considering you just dismissed it as incorrect, it seems strange that you would invoke it here. Secondly, your discussion of Kuhnian paradigms does not seem to be accurate either. Scientific theories which constitute normal science, for a time, may fall into a period of crisis as a result of anomalies. However, the existence of a single anomaly is not grounds for science to begin to work towards a new normal science. Furthermore, in The Structure of Scientific Revolutions Kuhn spends a great deal of time explaining that in periods of normal science scientist’s engage in puzzle solving, and it is only when those puzzles post too great of a threat to the overall picture being used that revolution occurs. Perhaps, though, your comment was too brief for me to understand what you meant to be saying, exactly. Anyway, what I really wanted to say here is that Kuhn’s account of when one ought to reject a theory is at least equally as problematic as Poppers, albeit for different reasons. I am not going to spend too much time discussing those problems, although there is one that stands out in my mind which alone is problematic enough. Kuhn says that the definitions of terms in different paradigms are completely incommensurable. So, according to Kuhn, when Newton and Einstein spoke of gravity they were talking about completely different things. While their understandings may have been vastly different, we know via ostentation that what each man was talking about was the same thing. If I drop something and it falls, irregardless of how you understand that falling, it is the same phenomena, gravity, which is being discussed. There are two different notions of gravity at play in each theory, but those notions are not completely isolated from each other, as Kuhn would have us believe. In reality our understandings of these terms is more like a continuum. (I know that gravity may have been a problematic term to use as an example, but I feel as thought it worked well enough to make my point clear).
When I read this post I was also thinking about Amy’s distinction between “calibrating” a theory and opting for a new theory (i.e. what factors could/would/should determine the difference, if there is any meaningful difference) is useful here, and it points towards my concerns about a certain theoretical conservatism that Quine for one would smuggle in (I’m thinking in particular of the essay “Hypothesis” by Quine and Ulian).
In fairness, I think Aaron’s post presumes a rejection of the kind of “naive” falsification that is usually subject to the most criticism (paragraphs 8 and 9 imply this at the very least).
Amy, I am not sure what you are saying. I have studied Popper and Kuhn and have at least a basic understanding of the two.
I reject a simple kind of falsification. If rejecting a theory is called “falsification,” then there is such thing as falsification. If we mean something like what Popper means by falsification, then I reject it. Kuhn also rejected a simple kind of falsification but we still reject theories when better theories arrive. A theory can be viewed as better when it has less anomalies worth consideration. The details of paradigms are actually pretty irrelevant at this point.
Popper seems to take anomalies as falsifications. There is no time that a theory will be simply falsified by an anomaly that I know of. Instead, a theory is faced with a problem and scientists will call it an anomaly.
Perhaps you are right that Kuhn’s view is problematic but I disagree that it is more so than Popper’s. Popper’s view seems almost nothing like how science works. Popper rejects induction then uses induction to falsify theories. (Is it still falsified? Is falsification true in the past and so also true in the future?)
Even if I am somehow wrong about Popper and Kunh’s views, what I am saying is still relevant. There is a lot of controversy about how scientific theories get rejected and the view that a theory can be falsified either needs to be clarified or it is suspicious.
James,
First, to address Kuhn and his infamous “paradigms”. In “The Structures of Scientific Revolutions,” he seems to use the term to mean both “disciplinary matrices” and “exemplars”. The former designate the conceptual framework and theoretical tools employed by scientists to solve the relevant scientific problems, while the later refer to particular problems that scientists have solved. Kuhn’s conception of the incommensurability of any two “disciplinary matrices” is, I think, founded upon bad analysis. If taken to its logical ends, Kuhn’s program is trapped in militant relativism, which, as Amy points out, is untenable and simply does not fit the relevant historical evidence. Moreover, I think it is more accurate to describe the evolution of theoretical concepts, like “heat” or “gravity”, as being refined and built upon through successive stages of scientific inquiry, not as their empirical reference changing (this is akin to Amy’s point). The “exemplars” are unproblematic, in my view; in fact, they often are the building blocks from which future scientists begins; Newton’s famous quote, “If I have seen farther than any other man, it is because I stood on the shoulders of giants,” is here appropriate.
Second, as Mark and Amy correctly point out, I do not subscribe to nor does my essay support naïve falsificationism. Having said that, I must say falsificationism, while not sufficient, is a necessary condition for science. The sciences need a way to test competing hypotheses, and, since scientific hypotheses seek to explain empirical phenomena, we should expect them to have empirical implications that are detectable. Quite simply, falsification and confirmation are formal methods of organizing and testing the empirical implications of scientific hypotheses. In Kuhnian verbiage, they are the precise ways we detect “anomalies”. Now, how much anomalies are required to ditch one theory and adopt another (presumably we must adopt some theory and not remain theory-less) is certainly a wonderful question. But, more or less, I think there are goods ways to make such a decision.
Amy & Mark,
Now for the difficult question: How to differentiate “calibrating” a hypothesis from the adoption or employment of a “new” theoretical hypothesis. First, I should say, I doubt if anyone will ever demarcate the necessary and sufficient conditions for such a distinction. However, an economy of thought can help researchers in maintaining hypothetical integrity. Simplicity is vital to calibrating a hypothesis. Scientists should seek to posit their hypotheses within their theoretical framework with the least of amount of variables because when observational findings do not conform to predictions, it is simply easier to see where we might have gone wrong, and, what is more, it assists scientists in keeping clear of ad hoc formulations. In addition, simplicity is a guard- though not a safeguard- against error: the more complicated our hypothesis, the more opportunity to go awry. (Ad hoc formulations, such as the many “epicycles”, “deferents”, and “crystalline spheres” posited by supporters of the Ptolemaic solar system, often are extra-theoretical.)
Now, what does “extra-theoretical” mean? If you recall, I mentioned that if biologists, in order to conform their model predictions to observable evidence, must incorporate assumptions at odds with their own theoretical position, then serious changes are in store. For instance, if adaptationists must utilize within their model data-set assumptions of biological chance (ala Stephen Jay Gould) and suppose “adaptations” to be merely spandrels (adaptive traits that have developed not through adaptationism, but rather exist because of, say, body plan constraints, etc.), then adaptationism, as a research project, begins to lose scientific utility. “Spandrels” and Gouldian evolutionary chance are extra-theoretical assumptions- to adaptationists, at least.
Finally, insofar as Einstein conceived of his theory of general relativity, prior to his and Hilbert’s rectification of the math, he expected it to explain the same phenomena as after the corrections. Therefore, in that respect, Einstein’s theory of general relativity did not change; but this leads to a problem of intention. Einstein intended his theory to explain the same phenomena before and after the corrections, but the precise empirical implications of his theory before the corrections were indeed different than after the corrections. This is similar to the pervasive use of the double negative to connote a negative affirmation: the speaker does not say what he means. Not a full answer, I know, but enough to further the discussion, I hope.
James,
Also, I should like to point out that not all anomalies are created equal. The quality of the anomalies, that is, whether they are systemic or peripheral to the theoretical core, so to speak, are relevant to questions of theory revision and maintenance.
Mark,
I completely overlooked your comment about theoretical conservatism. In an analogy I know you will find fault, my view on science (or for that matter, epistemology and logic) is similar to Edmund Burke’s view on political theory: I am very skeptical of sudden, revolutionary change. My skepticism is premised really upon reliabilists sentiments: I simply do not think turmoil in scientific methodology is a reliable way to formulate useful scientific theories.
I agree that anomalies can be more or less relevant or have various qualities. The fact that you take both confirmation and falsification into account is evidence that you share my suspicion of Popper.
I never argued that your ideas require a naive form of falsification. I was more concerned with what you had to say about Popper. Evolution can have anomalies like any other theory and in some sense can be falsified (given that an alternative theory can be better.)
Popper disliked that Marxists make some predictions but fail to reject the theory when the predictions fail. However, this is normal for scientific theories. They attempt to make predictions, but they are not easily rejected when the predictions fail. Of course Marxism might be unscientific, but I don’t think it is for reasons given by Popper. If we give Marxists the benefit of the doubt, then there should be alternate theories also making predictions, and the most useful theory might be considered the best. Such a theory is scientific insofar as it turns out to be reliable.
Ok, then, we are not too much in disagreement.
However, I am not convinced you accurately represent Popper’s view on Marxian historicism- at least, not an entirely accurate view.
He did indict Marxism for failure to drop their theory because of numerous failed predictions, but that is only half of the story. He also charged Marxism with being theoretically unfalsifiable. That Marxists perpetually revise in light of new evidence, use ambiguous language, and make vague predictions is what Popper emphasized. But since a discussion of the scientific merits of Marxism would take us too far afield, I will end here.
By the way, thank you for your contributions to the post.
Aaron,
I guess it was a bit convenient that I forgot to mention that part of Popper’s challenge to Marxism. Yes, some Marxists did keep revising “their theory” because of the failed predictions. I agree that constant arbitrary revisions is generally a bad way to do science. I don’t know enough about the history of Marxism to know how arbitrary the revisions were.
This is one way Marxists might defend themselves from Popper’s challenge:
Popper also said that when one theory/hypothesis fails, that we should invent a new one. I think Popper sees theories as pretty arbitrary, so if Marxism is the only plausible theory that we can think of (for the time being), then we might have no choice but to revise it arbitrarily.
I can’t edit my post, but I realized that I should say something about why I don’t think actual science is completely against arbitrary revision, even though it is embarrassing when it happens. What I said about Marxism does happen in science as well. I suppose Popper might think it proves that we use bad science, but I am not convinced.
I think my example of dark matter would belong here. Dark matter is a giant question mark and it is empirically unjustified. It is an arbitrary revision given to a theory that we are confident to be true. We also lack any alternative theory that would seem to explain the anomalies better. On the plus side, dark matter itself could be associated with some risky predictions.
There was a philosopher other than Popper who mentioned that “good science” (reliable science?) requires risky predictions, but I don’t remember his name.
This is an extremely general point, but it might be helpful to point out the problems in assuming a seamless transition (and reacting negatively if there is a conflict) in simply grafting the methodological views of the natural (or “successful”) sciences onto the social/human (or “dubious” to use Foucault’s term) sciences.
Mark,
There are differences between the two fields, but if one commits to the positivistic methodological program, then hypothesis testing and theory formation between the spheres should be similar.
James,
I am confused. You say dark matter is an empirically unjustified postulation, and further that it is an arbitrary revision. Yet, in the next breath you say we lack a hypothesis that can better explain the phenomena. The question must be asked, how can dark matter be “arbitrary” if it is our best option?
Doesn’t arbitrary mean- in this context, at least- the construction of an explanative hypothesis which is premised upon no good reason? I mean, given event E we may formulate either explanation A, B, C, all which cohere with our current theoretical framwork. Now, while A, B, and C explain E equally well, they are all of them mutually incompatible with any one of the other. So it seems whatever choice we make (A, B, or C), we do so rather arbitrarily. However, if we say, A explains E better than B and/or C, then can we really say we have chosen A arbitrarily? I am inclined to say no.
Now, again, you say dark matter is empirically unjustified, that it is an arbitrary revision, and even that it is “embarrassing when it happens,” yet that you don’t think it proves that this is a mark of “bad science”. This should strike anyone as odd. Empirically unjustified postulations are not signs of “bad science”? (I so happen to believe dark matter is empirically justified, not to mention mathematically justified.)
There is a story about Pierre-Simon Laplace, late 18th and early 19th century French mathematician and physicist, who met with Napoleon Bonaparte to discuss Laplace’s work. Napoleon was amused that Laplace failed to mention or postulate God existence in his theories. When asked why this was so, Laplace answered, “Well, I had no need for that hypothesis.” Napleon promptly returned, “Ah! But the hypothesis explains so much.”
“explanatory” hypothesis not “explanative”
Dark Matter is in no way a reliable science. It has not been empirically confirmed. If good science means “reliable” then it’s not good. However, Dark Matter is considered to be scientific because we have no choice but to postulate something like dark matter. In other words, some scientific theories are more reliable than others. That doesn’t mean that the less reliable theories are not scientific at all.
I think you found that I contradicted myself because I said that it was empirically unjustified, but somehow still justified. That is right, something can be empirically unjustified, but justified in other ways. Logical coherence, Occam’s razor, and so forth. The more we require non-empirical justifications, the less a theory will be scientific in the sense of being reliable, but it is still science.
Perhaps the problem you see in what I said is resolved simply by admitting that science tends not to live up to an ideal of reliability. Nothing is perfectly reliable and some theories are more reliable than others.
Right now quantum mechanics seems incompatible with general relativity, and we want to unify the two views. The fact that they are incompatible seems to suggest that they are both false. This is a huge anomaly staring us in the face. Still, they are not falsified or rejected.
I suppose Popper would want to say that Dark Matter is “bad science” and should be done away with. Why? According to him, the anomalies that require us to postulate dark matter “falsified” our astronomical theories. This is worse than saying it is merely unreliable (or less reliable than an ideal.) We might as well just throw out our current astronomical theories if that is right. Of course, we have good reason to suspect that our current theories are right (reliable to some extent), so we don’t want to admit they have been falsified as Popper might argue. Something like dark matter could explain the anomaly just as well as the theory’s falsity.
The Darwinian theory has no more to do with philosophy than has any other hypothesis of natural science.
–ludwig wittgenstein
Ludwig Wittgenstein is simply wrong.
- Aaron Kenna