While there are many differences between modern science and philosophy, there are still a number of lessons in modes of thought that scientists can take from philosophy. Scientists' ideas about the nature of science have evolved over time, leading to new ideas about falsifiability, creativity, revolutions, and the boundaries and limits of what can be accomplished by different types of science.
Platt, John R. "Strong Inference." In Science, New Series, Vol. 146, No. 3642 (Oct. 16, 1964), pp. 347-353
Raup, David C. and Thomas C. Chamberlin. "The Method of Multiple Working Hypotheses." In The Journal of Geology, Vol. 103, No. 3 (May, 1995), pp. 349-354
March 23, 2009
Professor Stephen Stearns: Okay, so today what we're going to talk about is the logic of science. And there's a reason that this lecture comes at this point in the course. Most of you are now just getting to the point where you're going to get serious about writing your papers--that's going to happen during the next couple of weeks--and in doing that, you're going to be making judgments about how good is the science that you're reading in the papers.
So I want to raise, in your minds, this issue of what constitutes science and what is not science, and what's good science and what's bad science, so that you'll yourself start to develop your own criteria. And these are issues that have occupied a lot of bright people for a number of centuries; so I'll only be touching on a few points this morning, but they're important ones.
Now science is basically culture's answer to the big problem of epistemology, which is how can we know anything at all? How do we know that there is a material reality? And this issue, as you know, goes back to Plato and Aristotle, in the Western tradition, and in each of the other major cultural traditions these issues have been debated. There's a lovely humorous story in Zuang Zi from the third century B.C. in China, about this issue. So basically if you look at what all the different parts of our culture do for our society, this is the role of science. It tries to give some kind of objective message about the nature of reality, to everybody in the culture, if they want to pay attention.
Now in talking about this, I am essentially assuming that you've got some background in these issues; and not all of you do, but there are places where you can catch up. For example, Bertrand Russell wrote a somewhat opinionated but amusing and informative history of Western philosophy, where you can sit down and in the course of about a month read through all of the major issues that have been debated.
I'm going to assume that you know that David Hume demonstrated that inference doesn't lead infallibly to truth. And that's an interesting point and it's one that I think a lot of modern philosophers probably would disagree with, to some extent. Basically what Hume was arguing about was how do we know that in fact the sun will rise in the east tomorrow morning? And the fact that it's just done so, for a long time, is no guarantee that it will do it again. We need to know something else in order to feel confident that the sun will rise in the east tomorrow morning.
And, in fact, what we've got going for us now is we've got a model of the universe in which the earth spins on its axis and planets go around the sun and stuff like that. That is a theory. It's a model of the universe, and it's been so extensively validated and connected to so many observations that it would be mad to deny its reality.
But that's quite different from just sitting there, without having that model of the universe in your head and noting that the sun comes up every morning, and just accumulating instances. And what Hume essentially pointed out was that just the accumulation of instances is not leading you infallibly to the truth; that there could be alternative explanations. So without that contest of alternative explanations having taken place, we don't really know that the sun will come up in the morning.
By the way, it is rather similar with the issue of something like is DNA the genetic code, which is a little bit closer to the subject of this course. It was not at all clear, say in 1945, in the Avery experiment, that DNA was the genetic substance. And as late as the discovery of the structure of DNA in 1953, by Watson and Crick, there were still people who felt that DNA probably wasn't the genetic code; that it was probably some protein that contained the genetic code.
And so there was a contest of alternatives, there were critical experiments that were done, and then the evidence accumulated to the point where it would become mad to deny that DNA is the genetic molecule, and that it has a particular triplet code and so forth.
So that's a way of showing how a working hypothesis survives a contest of alternatives to become something that then gets operationally accepted as truth. [laughs] And I suppose that it is conceivable that someone might now come up with an observation that would convince us that, at least in some cases, DNA wasn't the genetic code. But for all intents and purposes, this contest of alternative ideas, through experimental demonstrations, leads to something that science then accepts pretty much as truth. And what I'm telling you is that these theories about the structure of reality are basically arrived at by a contest of ideas that is being testing empirically over and over again, and you're accepting the last one that's left standing.
So here's more or less what scientists think. They think there's a material reality and they think we can discover its nature. Not everybody on the planet agrees with that. We can eventually agree on what we've discovered. At the leading edge of science there's plenty of disagreement about the nature of reality; that's the whole point about the contest of alternative hypotheses. So what we call science is limited to knowledge about the part of material nature that is currently accessible by our current technology, our current techniques, our current investment, and on which we can agree; and that agreement can take some time.
And not everything in material nature is accessible. If you just go back and you look, for example, prior to the discovery of- or to the invention of sensors that could detect the orientation of magnetic fields on the floor of the ocean, we didn't have access to the evidence that demonstrated plate tectonics. Okay? So that's something that happened after about the Second World War, and that evidence was accumulated actually mostly in the '50s and '60s. Prior to high throughput DNA sequencing techniques, we did not have access to the deep structure of the Tree of Life.
So those are technological advances that then open up things that we can get answers to. Currently we do not have the technology to decide about whether or not string theory is the best way to look at the very, very fine structure of substances, and therefore whether or not time travel is possible, or there are worm holes in space time, and stuff like that; we don't have enough technology to get us to where those ideas are going. So this is something that depends on the current state of technology.
Now the part of knowledge that people can agree upon, through this debate of alternatives, is what we call science; and that means that somebody else can replicate your claim. They can't replicate your claim unless you've described it clearly. That means if you're reading a paper, for one of your papers, and somebody can't tell you clearly what they've done, they're not doing a good job. They have to be able to write clearly in order to complete this part of the logic.
One of the loveliest cases of this that I ran into was now almost 30 years ago. I was invited to Scandinavia, and there were people there in departments in Göteborg -- Gothenburg -- and in Lund and in Oslo and in Stockholm, and Uppsala, who did not have any professors who could teach them modern behavioral ecology.
But they were fascinated by it, and the professors that they had, who were experts in things like comparative morphology, were willing to let their students study this new subject, and the students taught it to themselves entirely from the scientific literature. It had been so effectively described in journals that they could pick up and read that they'd bootstrapped themselves into becoming world experts in behavioral ecology, and the Scandinavian School of Behavioral Ecology has become a dominant force in the field.
They did it without having any professors to teach them, because people could write good papers. So that is one of the reasons that I'm so enthusiastic about people learning to write effectively, because it can actually accomplish cultural transformation. I think I've already made this point well enough. Okay.
So how do we agree? Well here are some issues. I'm going to be talking a bit about the method of multiple working hypotheses, about falsifiability, about strong inference, about scientific revolutions, and about the issue of whether philosophers understand this better than scientists do. And I'd like to touch a little bit on where ideas come from; and I've already given you a couple of hints on that in terms of support for writing your papers.
By the way, if I just go through this, this is certainly not a rigorous and inclusive coverage of all of the important points in the philosophy of science. It is just hitting a few high points that I hope will stimulate you to think about these things, and perhaps you'll want to read further. So there are many different ways of doing this, but in choosing these particular things I am hitting on issues that have particularly occupied the minds of biologists. So it's not random, in that sense. Okay, so let's go back to T.C. Chamberlain.
T.C. Chamberlain was the head of the Geological Society of America, and he gave a wonderful address, which has been reprinted several times, and which is part of your reading for Section this week. And basically what Chamberlain says is that we fall in love with our own ideas, and therefore we're biased, and so when we look at a pattern of data, we will have a tendency to pick out the parts of it that support our preconceptions and to leave out the parts that don't support our preconceptions, and if you're interested in an objective view of reality, this is a bad thing to do.
So how do we protect ourselves from this? Well the best way, he thought, was to explicitly come up with a set of multiple working hypotheses, that are actually different from each other, and then weigh the evidence for and against each of them. So this is a way of protecting ourselves against our love for our own ideas.
Now sometimes, several can all be correct, and that is the case whenever hypotheses are not mutually exclusive, where they could all actually be working at the same time. Sometimes that is true and sometimes that's not true. That tends not to be true when you're talking about particular molecular structures. There is normally just one molecular structure. If your techniques are not good, there are some alternatives, but when you get them really good, usually there's just one.
But often there are several different selection pressures that will result in the same outcome. And you've seen that with sexual selection. Okay? So a female could be choosing a male for good genes, or because he's got lots of resources, or because he'll have sexy sons, and in fact those could all be true at the same time.
Now one way to get to objectivity--given that, in fact, the observer, the human, always has kind of a selfish bias towards their own idea--one way to achieve objectivity is to try to demonstrate systematically that a hypothesis is wrong. And if you try to refute it, rather than to confirm it, and you can't refute it, it just is stubborn, it will not go away, then maybe it's right. [laughs] Okay?
So this is the idea behind Popper's falsifiability criterion. Karl Popper, a very influential philosopher of science, member of the Vienna School; that was the school of people that also had Wittgenstein and Carnap and a number of others in it, and these were people who were engaged in very strong debate about how to make sense of the discovery of reality in the post-quantum mechanics world. And there had been a great deal of uncertainty in the basis of our knowledge, that entered in, in the early twentieth century, with the discovery of quantum mechanics and of the theory of relativity.
To put you back into that, for two or three-hundred years, people had thought that Newton had actually figured it all out, and then from about 1880 up to about 1910 the Michelson-Morley experiment and things like that had demonstrated that speed of light was a constant in the universe, and the only way that that could really be understood was through Einstein's special Theory of Relativity.
And that and the subsequent discovery of quantum mechanics, which came out of the photoelectric effect and other things, made people realize that it was possible for science to go cruising along for a couple of centuries, thinking that it was right, and then to discover that it was wrong. And that suggested, well that could happen again, and it could happen in places where we don't expect it. So what are we going to make of all this?
Well one of the responses is Popper's falsifiability criterion. So what Popper says is that we can never actually prove that an empirical statement is true, for there are always alternatives that are possible. So these alternatives we might not know about, but that would be a failure of our imagination, it would not be a failure of logic.
However, we can demonstrate that things are false. So Popper claims this is what distinguishes science from math. Okay? You can prove a theorem in math; you cannot prove an observation in science. So proof means true at all times, in all places.
I think that you're currently scratching your heads and wondering, well in what sense is it not true that gravity is present throughout the universe, or that DNA is the genetic code, or any of these other big things that we know in science. Well I would say that the thing that distinguishes science from math, in statements like that, is that math is 100% certain, and science is trying to get to the limit of that 100% certainty; so some of it's up there at 99.99, I would say, or even closer. But with math it's simply logically true, and with science it's a matter of empirical demonstration.
So because of that, Popper suggested that the difference between science and non-science is falsifiability. If in principle you can demonstrate that something is false, if a certain observation that one could imagine could demonstrate it, then you're dealing with science, and if you cannot imagine ever making an observation that would demonstrate that something is false, then you're dealing with non-science. Okay? So that's how Popper distinguished science from religion.
Now I think that there's something to this. Basically what I take away from this personally--excuse me, I want this last statement down here--is that we trust ideas that have taken the strongest hits we can throw at them and they're still standing. Okay? So that's, to me, the best criterion for trying to see whether people are doing natural science. They're not trying to confirm the ideas, they're trying to be critical; they're throwing everything they can at them, and by George you can't knock them down.
Now one person who more or less implemented this was a chemist named Platt, and you're going to read his paper for Section this week as well. So Platt was one of the physicists who had come into biology, a physical chemist who had come into biology, and he asked himself, "Why is it that some fields make progress faster than others?" And he said, "Oh, it's-- actually we know. They have a good method. It's called strong inference."
So devise alternative hypotheses--that's Chamberlain. Devise crucial experiments to exclude hypotheses--that's Popper. Do the experiments so well that nobody can argue with you, and then recycle the procedure. So he said people who are making progress do that, and people who aren't making progress don't do that.
And so in comments on this, that had been quoted in the letters, Leo Szilard, who is one of the founders of molecular genetics, molecular biology, said the problems of how you induce enzymes, or how you synthesize proteins, or how you form antibodies, are actually something you can do with experiments, that you can finish fairly quickly, and it will only take a few experiments to do it.
So actually if intelligent people were just dealing with this issue, we would get there pretty quickly. And a young ambitious scientist says, "It's essentially the old question: how small and elegant an experiment can you perform?" And a descriptive scientist, an electromicroscopist, who is a not a person who is normally engaged in these testing of alternatives says, "Gentlemen, this is off the track. This is philosophy of science, this isn't what we really do." And Szilard says, "I'm not quarreling with third-rate scientists. Okay? I'm quarreling with first-rate scientists." And then this guy writes in, a little bit afterwards, and says, "So, should I commit suicide?" So you see people get kind of stirred up about this stuff; and there are some remarkably arrogant people out there. [laughs]
So where does this work and where does it not work? And by the way, one of the best demonstrations of this method that I've ever seen was when Tom Pollard gave his lecture in that half-credit course for freshmen, and Tom came in and described how he had figured out how cells move, how actin fibers are used in the motion of cells, and it was just a tour de force of strong inference, it worked like a charm. Okay? And it was all about cell structure.
So where does it work best? Well what's the single mechanism; what's the structure? That is where strong inference really works well. It doesn't really work so well where there are several different correct answers, where you've got multiple causation going on. That's often much more often the case in ecology and evolution than it is in molecular and cell biology, and it's certainly much more often the case in the social sciences than it is in the natural sciences. But it's a good philosophy. Okay? It's a good starting point. It's good to realize that that's a good standard to set, and to see how far you can push the process towards it.
So, for example, the genes in an environment interact to cause phenotypes. So it's not just genes, it's not just environment that are causing heart disease. And you can use experiments and hypotheses to get at these interactions; and that's clearly an important point that we would like to know about. But when you look at all the causes of heart disease, there are at least five or six, and they're interacting with each other, and when a person dies of a heart attack, it is often difficult to say it was only for this reason that they died of a heart attack.
Now strong inference actually won't work at all in a field like astronomy, geology, paleontology or systematics. And that's because we can't do experiments. Nevertheless, we can do observations that are so precise that they become convincing. So there is a rigor in descriptive science that is not captured by this paradigm of strong inference. Okay?
For example, probably the most extreme example I know of is this. Quantum chromodynamics makes a prediction for the fine structure constant, to so many decimal places that it predicts it to within half of the diameter of a piece of tissue paper, compared with the distance between Washington DC and San Francisco.
Now if a theory is able to make a prediction quantitatively, which is that precise, you're not going to ask some kind of high-faluting experimental verification of it. You're just going to measure the fine structure constant and if it measures down to that many decimal places, you're going to scratch your head and say, "Well, you know, I think maybe the theory has got something to it. It's capturing something important about the nature of reality."
Things like continental drift and the Big Bang are accepted without experimental confirmation. By the way, thank God we're not doing experiments on the Big Bang. That would be a little bit exciting [laughs] if we were doing that one. But you might want to think that if strong inference is the paradigm of good science, then why is it that we are now so happy with the notion that continental drift is going on and that the Big Bang occurred?
And I think that what you'll find is that there is a theory about how it works, and the theory makes a long series of predictions, and many, many of these predictions have now been confirmed by observation; not by experiment but just by observation. And if you line up other alternative theories, for say the location of the continents on the planet, or say the residual cosmic radiation, or something like that for the Big Bang, you'll find that the alternatives don't do so well.
Okay, now there is another possibility for what goes on in science, and that is this romantic paradigm of revolutionary science. And if you would like to read a piece of glorious philosophical rhetoric, read Thomas Kuhn's 1962 book, The Structure of Scientific Revolutions.
Kuhn was a guy who had been a physicist and then he went into the history of science. He was a Junior Fellow at Harvard. He decided to make the Copernican to Galilean- the Copernican revolution; so overthrowing the Ptolemaic structure of the universe and moving to a model of the universe in which the sun was at the center and the earth went around the sun, and then eventually to the Galilean and subsequent model of the universe in which the earth is a small planet circling an obscure star, on the fringe of a thoroughly normal galaxy, which is one of billions of galaxies.
So that kind of change in world view he described as a scientific revolution. And he described it as a paradigm shift, a shift in the whole way that we look at the world. And there have been some others. Okay? So Newton to Einstein, plate tectonics.
And the idea here is that the paradigm shift is so profound that people are not able to communicate across the divide, so that once you have seen, for example, that the continents are in motion, you can actually no longer have an intelligent conversation with your geological colleague who doesn't realize that yet, because it's such a deep change in the way that you look at the world. That one actually--I watched some of these people communicate across that divide; so that wasn't really that kind of paradigm shift.
If that really is true, then the old generation has to die out before the insights of the new generation can be accepted. And if you are a young revolutionary, and you're getting a lot of resistance from the older generation, this might be some kind of solace, that actually you're younger than they are and you're just going to outlive them. Okay?
Well I think that this is an interesting set of issues, because somebody like Charles Darwin really was a revolutionary. There's been nobody who has more profoundly changed the way that we think about the human condition and what a human being is and so forth than Darwin.
But Darwin didn't want to be a revolutionary. He wanted to be a normal member of the British upper middle-class, who wasn't upsetting anybody. [laughs] And he was conservative. He wanted to be acceptable to the establishment, and so he went through rather elaborate maneuvers, to try to make himself digestible.
Steve Gould was not really a revolutionary but he wanted to appear to be one. If you go back and you look at what Steve's written about his encounter with Kuhn, in 1965, when he was a graduate student at Columbia, you can see that he was seduced by this idea that revolutionary science is great science, and that's what he wanted to become.
So he had important ideas; there's no question that Steve Gould had important ideas, but he wanted to sell them as a paradigm shift that would change profoundly the way that everybody looked at the world, and he actually overshot his mark and he created exaggerated expectations. So there was a bit of a backlash against him because he was making claims that couldn't really be supported. And that is, I think, kind of unfortunate because he had some important ideas; just oversold them.
So is it worth worrying about being a revolutionary scientist? Well I think we all have to be a bit modest about whether we can tell whether we're currently making a contribution that's going to make any difference at all. And the only thing that decides is history, and history chews this stuff over long after we are dead. So it's really only history that can identify a major scientific advance. It's very difficult, right in the middle of the generation that's experiencing it, even though it might have gotten a Nobel Prize, to be sure that it's really that fundamental, because it just takes perspective and time.
So if you're on the scene and you're enmeshed in the process, your own estimate of the contribution is kind of unreliable; and, to go back to Chamberlain, we're all in love with our own ideas, and so we all have a tendency to think that what we're doing is the greatest thing ever. And that's simply just not necessarily true, and it's kind of hard to tell until history takes its course.
So the best way to cause a change is to take the current state of affairs and push it as far as it will go. So taking the current state of science, what Kuhn might call boring, normal science, and pushing its limits and discovering where they break down is probably the most effective way, in the long-term, to really cause major scientific advance.
So, for example, the Michelson-Morley experiments, where they were simply measuring the speed of light in the direction of the earth's movement around the sun and in the other direction, and they discovered that it was the same in both directions, even though they knew that the earth was moving around the sun at hundreds of thousands of miles per hour, is a very good example of this. That caused a crisis.
And there haven't been very many experiments in the history of biology that have had that kind of impact, but there have been a few. The Avery experiments in 1945 identifying DNA as the genetic substance in bacteria are a good example of that. There have been some others.
So if you make a premature attempt at revolution and you overshoot the mark, then the attempt tends to collapse under its own weight. There's a whole cottage industry of criticisms of Kuhn. You can find conferences that have gone out and found maybe seventy or eighty different senses in which Kuhn used the word paradigm in that paper. So I would say that whether it's worth worrying about revolutionary science at all, or whether it's worth trying to be a revolutionary scientist, is an issue which is open to pretty serious discussion.
Now what about post-modernism? Post-modernism is variously defined, and some of it I think is quite interesting and worth reading. When people say Post-Modern, they usually think of the French School of Literary Criticism and Philosophy; they think of Jacques Derrida, they think of Lacan, they think of Foucault. And there are insights that those guys have had, some of which I think should be part of the intellectual equipment of any well-educated person.
And particularly among that crew I particularly admire Foucault because Foucault, for example, discusses things like is the definition of madness a function of the current power structure of society? I think that's an interesting question and I think that there's some historical evidence that it is, to a certain degree. So I think there are important issues there, and most of that I think has to do much more with literary criticism in the social sciences than it does with the natural sciences.
But the people who got into this decided that they might want to turn this armament of literary ideas onto natural science. And they picked up on Kuhn, because if you could show that science consists of a series of revolutionary paradigm shifts, that would mean that science is more socially constructed than empirically verified. Okay? So it's like one paradigm is one period of mass hysteria, and then the next paradigm is another period of mass hysteria; and there isn't anything going on here, other than that people are tending to agree with each other on the nature of reality, but then they're changing their minds. Okay?
Well most of science actually doesn't proceed according to Kuhn's model of revolutionary science. It's going by the accretion of well-tested hypotheses. They're mostly much smaller than a paradigm. It's walking with small steps. So it's not built up the way that say Kuhn's Copernican Revolution would make it look like. And science does succeed in describing nature in ways that don't change as science advances.
So you can ask yourself questions like this. In what sense was Newton still right after Einstein? Well he was right enough to get people onto the moon. You didn't need the correct, the Einsteinian corrections to get man to the moon. I think that at that scale you're off by a matter of meters or seconds, rather than by kilometers; things like that.
In what way is Darwin still right after the rediscovery of Mendel's laws of transmission genetics? Well we're all in a big frenzy of honoring Darwin's 200th Anniversary this year; and he was obviously clearly right on some very important points, and wrong on some others, and science manages to distinguish that stuff.
So the point is that when the natural science community gets down to the task, and it focuses long and hard on an important point, it can actually tell you pretty well what the nature of reality is; and it's not that we're dealing with successions of mass hysteria on something like that.
Now that said, one of--there are moderate post-modernists who will say, "Yes, but the social and political context does bias the kinds of questions that are tested." And I think there's some truth to that. And I think there's some truth to the idea that if science was dominated by women, that they would be testing a different set of questions than if it were dominated by men. And I think that if it were dominated by Marxists, that they would be testing different sets of questions than if it were dominated by Capitalists.
But I think that the objective weighing of alternatives is going to cause all of those different traditions to arrive at the same point eventually. Because Mother Nature doesn't care whether you're a man or a woman, or a Marxist or a Capitalist; Mother Nature just is, and she's going to give you answers.
Now science consists of shared knowledge--that's what we can agree on--and that doesn't mean that science is a social construct. Science is accumulated by humans having social interactions, but that doesn't mean that it's arbitrary. So it's making progress, and it's expanding the part of reality we can agree on, and eventually reality has been checked by so many methods that we converge; any independent intellectual tradition would converge on reality as it actually is.
And that doesn't matter whether you would start this process coming out of a Buddhist tradition or a Christian tradition or whatever; you would eventually end up with quantum chromodynamics in physics, and you would eventually end up with cell biology and evolution in biology.
I think that there's a lot of fun that the philosophers of science have in arguing about what scientists actually do and what's the best way to do it. But I think the thing that the scientist needs to take away from it is just agreeing that we can all be critical about the hypotheses we pose, and that the tests that they have, have to withstand, and the ones that we can agree on they have withstood.
If we can agree that we're going to be critical of each other, and we will do so in a civilized way, and we will insist that we will only accept constructive criticism, and we will agree that we will only try to give constructive criticism, because we want to have this play of alternatives, and we know that's the only way we can get to an accurate description of reality, then we can do good science. And I don't think that we have to get much fancier than that agreement, in philosophical terms.
Now if we want to be philosophers of science, we can go and get as fancy as we want; that's another issue, that's another field. But what the working scientist at least needs to do is to realize that something like this is going on.
Okay. I'll now give you Western philosophy in about two minutes. Okay, so philosophy starts out as being essentially what we would now call education in general, learning in general. And then parts of it become mature, and they have then significant elements that are no longer subject to debate. So they split off.
The first thing that goes off is math, then physics. So Math gets split off by, arguably oh second century BC, I would say. Physics gets split off by roughly the time of Galileo, between Galileo and Newton. And of course Astronomy quickly follows. And then with Lavoisier and so forth, the end of the eighteenth century, Chemistry splits off. Then Geology becomes a special subject, pretty much in the nineteenth century, and so does Biology.
So what is then left in this field of knowledge that we call philosophy, that used to be everything? Okay? Well it consists largely of a set of very interesting issues, about which we remain uncertain.
So given that, should scientists, who largely agree on how to proceed, accept dicta that are handed down by philosophers who often don't agree on what they're taking about? Well I would say that scientists shouldn't accept simple recipes from philosophers, especially if they haven't done science themselves, but they should listen to reason from those who have the perspective of standing outside the endeavor. So one should not dismiss the philosophers out of hand. They're often very bright people who are making good points, but they may not have the practical experience to understand exactly what difference their points make.
Now the final thing that I'd like to mention is a little bit about creativity. So where do ideas come from? And after all I've been talking about science as a play of alternatives, and we have alternative models, alternative hypotheses that we want to generate, and that if we can get them playing off of each other, then we can use that as a tool to try to perceive reality.
Well the best study of where these ideas come from, that I'm aware of, is called The Psychology of invention in the Mathematical Field, by Jacques Hadamard. And Hadamard was a student of Henri Poincaré, a great French mathematician and physicist, and Hadamard's own personal research agenda was number theory; he wanted to understand the distribution of the prime numbers on the real line.
But he was also fascinated by where do people get these great ideas? After all, he had hung around Poincaré, he knew him, and he had more or less grown up at the time that Einstein was having his ideas. And so he went and he talked to Poincaré and he talked to Einstein, and then he wrote down what he discovered, from his interviews. So it's more or less a history by interview.
So Poincaré described a case of stepping onto the bus in Paris, and he said, "You know, I had just submerged myself in this problem." It had to do with an issue, an abstruse mathematical issue, having to do with quadratic forms. So Poincaré just sinks as deeply as he can into this, and he gets totally frustrated, and he just can't go anywhere with it and he puts it aside. And about two months later he is stepping onto the bus in Paris when suddenly the idea for the solution appears to him, full-formed in his head, and he says, "You know, when I sat down and I started just making a few notes, I knew that when I got home I would be able to write the whole thing out."
It's almost like Coleridge writing Kubla Khan. So if that darn neighboring minister hadn't come to Coleridge's door, we would have another ten pages of poetry like Kubla Khan, because Coleridge got interrupted in the middle. Poincaré was pretty sure he could get the whole thing out, and he did. He went out and he went home and he wrote down the paper on quadratic forms. And similarly Kekulé had this dream of a snake biting its tail. And Einstein described similar things, coming up with special relativity.
And so the sequence basically is there has to be a period of hard work, and you have to push yourself right to the limit, trying to figure out the solution to some puzzle. Then you go to sleep, and maybe the next morning, or maybe two months later, something will occur to you. Your brain is processing overnight. It is making connections. It's trying out all sorts of things, and all of the clutter and bustle of every day is getting in the way.
And believe me, now that we have iPhones, and we have Twittering, there is a lot of clutter and bustle that gets in the way during the day; and some of you are probably surfing the web while I am saying this. So this point, that if you can simply put all that stuff aside and really concentrate hard, and then let your subconscious do the job, you will be surprised at what you come up with. We are all probably more creative than we give ourselves credit for.
So these things don't happen to anybody. They only happen to those who have prepared themselves by working hard. So the overview of this is basically that creative new ideas, about how the world works, can come from anywhere. So this contest of alterative hypotheses in science, those new ideas can come from anywhere, but they most often emerge from the minds of people who have worked very hard to understand something. So that's the raw material.
And, by the way, this raw material usually emerges in the minds of young people. It doesn't so frequently emerge in the minds of the old guys with white beards. Okay? It's something that emerges in the minds of young peoples. And particularly in math and in physics, those people are often between the ages of 20 and 30. It appears that in biology often they're between the ages of 30 and 40, just because it's a different kind of subject and it takes more background preparation. So those ideas are then subjected to rigorous tests, and the ones that remain standing become what we call science.
So the importance of new scientific ideas--gosh, I went through and I managed to change everything, but I didn't manage to change this one thing. And I have one or two minutes, so I think I can change it; I'm going to just pull up that last line. What's important and what's not important? Well something is important if it changes a big chunk of our view of the world, and it's not so important if it changes only a very small chunk. So the bigger the change to the way that people think about the nature of reality, the more important the idea.
Next time I'm going to talk about ecology; we'll start into that. The rest of the course is ecology and behavior. And anybody who would like lunch today, that's possible.
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