Scientists seek objective reality, but, argues Steven Weinberg, although that is a social process it does not make the end product a social construct.

Standing in a bookshop in Harvard Square a decade ago, I noticed a book on the philosophy of science by a friend of mine. I opened it and found it interesting -- my friend was discussing questions about scientific knowledge I had not thought of asking. Yet, although I bought the book, I realised it would probably be a long time before I read it, because I was busy with my research and I knew in my heart this book was not going to help me in my work as a scientist.

This was not a great discovery. Few philosophers of science take it as part of their job description to help scientists in their research. Wittgenstein and others have explicitly disclaimed any such aim. But standing in that bookshop it occurred to me to ask why this should be? Why should the philosophy of science not be of more help to scientists?

A good part of the explanation must be that science is a moving target, that the standards for successful scientific theories shift with time. It is not just our view of the universe that shifts, but our view of what kinds of views we should have or can have. How can we expect a philosopher (or anyone else) to know enough about the universe and the human mind to anticipate these shifts? We learn about the philosophy of science by doing science, not the other way round.

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Albert Einstein's development of the special theory of relativity in 1905 is an example of this point. For some years before 1905 physicists had been worrying about why it seemed to be impossible to detect any effect on the speed of light of the earth's motion through the ether. The electron, just discovered in 1897, was then the only known elementary particle, and it was widely supposed that all matter is composed of electrons. So most physicists who worried about the ether, such as Abraham, Lorentz, and Poincare, tried to develop a theory of the electron's structure, such that the lengths of measuring rods and the rates of clocks made of electrons would change as they move through the ether in just such a way as to make it seem that the speed of light does not depend on the speed of the observer.

Einstein did not proceed along that line. Instead, he took as a fundamental hypothesis the principle of relativity, that it is not possible to detect the effects of uniform motion on the speed of light or anything else. On this foundation, he built a whole new theory of mechanics. Einstein's theory was widely accepted by the cognoscenti in theoretical physics, including Lorentz. But Lorentz, though a great admirer of Einstein, did allow himself one very mild complaint: that Einstein had assumed what Lorentz and others had been trying to understand. This was quite true. Einstein just assumed that there would be no effect of motion through the ether. What Einstein had done was to set the tone of 20th-century physics by taking a principle of symmetry, or invariance -- a principle that says that some changes in point of view cannot be detected -- as a fundamental part of scientific knowledge, a hypothesis at the very roots of science, rather than something that is unsatisfactory until it can be deduced, as Lorentz was trying to do, from a specific dynamical theory. In other words, Einstein had changed the way that we score our theories. Today, a theory based on an assumed new symmetry, if it also fitted in with experiment, would be regarded as very appetising, a very promising theory. It was not so for Lorentz.

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The fact that the standards of scientific success shift with time does not only make the philosophy of science difficult; it also raises problems for the public understanding of science. We do not have a fixed scientific method to rally round and defend. Years ago I spoke to a high-school teacher, who explained proudly that in her classes she was trying to get away from teaching just scientific facts and wanted instead to give the students an idea of what the scientific method was. I replied that I had no idea what the scientific method was, and I thought she ought to teach her students scientific facts. She thought I was just being surly. But it is true: most scientists have very little idea of what the scientific method is, just as most cyclists have little idea of how bicycles stay erect. In both cases, if they think about it too much, they are likely to fall off.

The changes in the way we judge our theories has bothered philosophers and historians of science. Kuhn's early book, The Structure of Scientific Revolutions, emphasised this process of change in our scientific standards. He went overboard in concluding there was a complete incommensurability between present and past standards, but it is correct that there is a qualitative change in the kind of scientific theory we want to develop that has taken place at various times in the history of science. But Kuhn then proceeded to the fallacy -- much clearer in what Kuhn has written recently -- that in science we are not, in fact, moving toward objective truth. This a fallacy, because it seems a simple non sequitur. I do not see why the fact we are discovering not only the laws of nature in detail, but what kinds of laws are worth discovering, should mean we are not making objective progress.

Of course, it is hard to prove we are making objective progress. David Hume showed early on the impossibility of using rational argument to justify the scientific method, since rational argument, that is, appeal to experience, is part of the scientific method. But, as Bernard Williams has recently emphasised, this kind of skepticism gets one nowhere. One can be equally sceptical about our knowledge of ordinary objects, because the methods of science are not that different, except in degree, from the methods by which we live our lives. But of course we do not worry very much about whether our knowledge of common objects such as chairs is objective or socially constructed.

The physicist who lives with principles of symmetry, like the principle of relativity, or with more esoteric constructs such as quarks or quantum fields or superstrings, gets nearly as familiar with them as with the chairs on which he or she sits. The physicist finds that, just as with chairs, these constructs cannot be made up as one goes along, that they seem to have an existence of their own. If you say the wrong thing about them, you will find out about it pretty soon, when experiment or mathematical demonstration proves that you have been wrong.

My experience with the principles of physics is not that different from my experience of chairs. Even with chairs one can raise the question of different levels of knowledge. We mostly know about chairs by sitting in them or by bumping into them, but there are other ways of knowing about chairs that are more refined. For instance, you can look at photographs of chairs. There are apparently primitive peoples -- though I am not sure about this -- who do not recognise photographs of objects as representing the objects. I know that my cat does not. He is incapable of associating a photograph even of something interesting, like a fish, with the actual object. We can; we are sophisticated enough to possess such a higher mode of knowing about objects like chairs as looking at pictures. From that to the methods of modern science I see no philosophically relevant discontinuity.

It does no good for scientists to pretend we have a clear a priori idea of the scientific method. But still we should try to say something about what it is we think we are doing when we make progress toward truth in the course of our scientific work. There is one philosophical principle of use here. It is, to paraphrase another author: "It don't mean a thing if it ain't got that zing." That is, there is a kind of "zing" that is quite unmistakable when real scientific progress is being made.

Here is an example close to my own work. The 1960s saw the development of a unified theory of weak nuclear forces and electromagnetism. It was not clear that this theory was mathematically consistent, although Abdus Salam and I argued it was. Then, in 1971, a previously unknown graduate student, Gerard 't Hooft at the University of Utrecht, showed that theories of this type are, in fact, mathematically consistent. Immediately, the world of theorists began to take this seriously and write many papers about it. It had not yet, however, become part of the scientific consensus. In 1973, two years after 't Hooft's first work, and six years after my own earlier work, experimental evidence began to emerge showing that the theory was valid. Even so, although the theory was now widely held to be correct, there remained some healthy scepticism, which was reinforced in 1976 when some other experiments pointed in the other direction. Finally, in 1978, experiments done at the Stanford Linear Accelerator Center decisively supported the unified theory of weak and electromagnetic forces, and from then on it has been generally taken as the basis for our understanding of these forces. The "zing" was unmistakable. From beginning to the end, the process of general acceptance had taken about 11 years, of which five were a period of intense experimental effort.

Experiment always has something to do with the fashioning of a scientific consensus, but in ways that can be quite complicated. In this case, the theorists were pretty well convinced of the general idea of this sort of theory after 't Hooft's work in 1971, before there was the slightest new experimental evidence. The rest of the physics community became convinced over a longer time, as the experimental evidence became unmistakable. But, by the end of the 1970s, there was a nearly universal consensus that this theory was right.

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This story illustrates a few points. First, the interaction between theory and experiment is complicated. It is not always the experimentalists who make discoveries that are then explained by theorists; just as often theories come first and are then confirmed by experiment. Indeed, theory and experiment often go on at the same time, strongly influencing each other.

Another point, ignored almost always by journalists and often by historians of science, is that theories usually exist on two levels. On one hand, there are general ideas that are not specific theories but frameworks for specific theories. One example is the theory of evolution by natural selection, which leaves open the question of the mechanism of heredity. In the case of the unified theory of weak and electromagnetic forces, the underlying general idea was that the apparent differences between these forces arise from a phenomenon known as "spontaneously broken symmetry", that the equations of the theory have a symmetry between these forces that is lost in the solution of these equations -- the actual particles and forces we observe. These general ideas are very hard to test because they do not lead to specific predictions. This has sadly led Karl Popper to conclude that because such general ideas cannot be falsified, they cannot be regarded as truly scientific.

Then there are the specific, concrete realisations of such ideas. These are the theories that can be tested by experiment, and can be falsified. As it happened with the unified weak and electromagnetic theory, the symmetry pattern that had been originally suggested as a specific realisation of the general idea of broken symmetry turned out to be the right one. During the period of the 1970s, theorists were mostly convinced about the general idea but not about this specific realisation of the idea. Of course, the experimentalists had to prove that some specific theory was right before any of this could become part of the scientific consensus.

Also, when I say the physics community became universally convinced of something, I am speaking loosely -- this is never entirely true. If you had a lawsuit that hinged on the validity of the unified weak and electromagnetic theory, you could probably find an expert witness who is a PhD physicist with a good academic position who would testify that he or she did not believe in the theory. There are always some people on the fringes of science who do not believe the consensus. This makes it harder for an outsider to be sure that the consensus has occurred, but it does not change the fact of the consensus.

Within the area of physics and in this century, whenever this consensus has been achieved, it has never been simply wrong. To be sure, sometimes the truth turns out more complicated than what had been thought. For example, before 1956 there had been a consensus that there is an exact symmetry between right and left, and then we learnt that the symmetry is not exact, it is only a good approximation in certain contexts. But the 40 years of earlier physics research that had relied on this symmetry to understand nuclear and atomic problems was not wrong; there are just small corrections that physicists had not known about. None of the consensus when reached in the physics community has ever been simply a mistake, in the way that in earlier centuries you might say, for example, that the theory of caloric or phlogiston was a mistake.

Now, all of this is, of course, a social phenomenon. The reaching of consensus takes place in a worldwide society of physicists. This fact has led to a second fallacy -- that, because the process is a social one, the end product is a mere social construct.

A physicist-turned-author, Andrew Pickering, wrote a book about the conceptual development of the quark, called Constructing Quarks. The book perceptively showed the interesting social process by which the existence of quarks gradually became the consensus among physicists and changed the direction of experimental research. The book's conclusion as I understood it was that whatever physicists may say about it, quarks are a social construct, as the rules of contract bridge are social constructs. Again, I think this is a simple non sequitur. The analogy I drew in my book Dreams of a Final Theory was to a party of mountain climbers who argue about the path to some peak. Their arguments are conditioned by the social structure of the expedition, but when they find the right path they know it because then they get to the peak. No one would write a book about mountaineering called Constructing Everest.

The social milieu of physics research has much less to do with the direction of this research than is supposed by the social constructivists. This milieu is far less oppressive and hegemonic than many suppose. Often the great breakthroughs are made by youngsters like 't Hooft, of whom no one had ever heard before, while the famous greybeards who have senior positions in the great universities may get left behind. Physicists did not pay much attention to the current work of Heisenberg after 1950 or of Einstein or De Broglie after 1930, and they were not convinced by the views about quantum field theory expressed late in life by Heisenberg or Dirac. Heisenberg and De Broglie rather discreditably tried to force their views on the physics communities in Germany and France. Einstein and Dirac, gentler souls, simply went their own ways. But even Heisenberg and De Broglie were not able to damage German or French physics for very long. The exact sciences show a remarkable measure of resilience and resistance to any kind of hegemonic influence, perhaps more than you would find in any other human enterprise.

The working philosophy of most scientists is that there is an objective reality and that, despite many social influences, the dominant influence in the history of science is the pull of that objective reality. It may seem that, in asserting the objective validity of what we are doing, scientists are simply trying to protect their own status. It is not easy to answer that criticism. I could say: "I am not a crook", but such arguments only go so far. Perhaps the best answer is "tu quoque". Much of the comment on science by the social constructivists and others seems motivated by the desire to enhance the status of the commentator -- to be seen not as hangers-on or adjuncts to science but as independent investigators, and perhaps as a superior investigators, by reason of their greater detachment. This is especially true of those who follow the "Strong Program" in the sociology of science, which my friend Sidney Coleman calls the "Strong Pogrom".

This motivation was close to the surface in a recent article in Isis by Paul Forman. He described historians of science as preoccupied with their independence from the sciences. He called for a greater degree of independence because this was important to their work as historians. So far, so good, but he also wanted historians to exercise an independent judgement not just as to how progress is made, which certainly is in their province, but also on whether progress is made. He gave no arguments that such judgements would have any kind of intellectual validity, except that this was the sort of thing that historians have to do as part of being historians. We scientists need make no apologies. We believe in an objective truth that can be known, and at the same time, we are always willing to reconsider, as we may be forced to, what we have previously accepted. This would not be a bad model for intellectual life of all sorts.

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Nobel Prize winner Steven Weinberg is professor of physics and astronomy, University of Texas at Austin. This is an edited version of a talk given at a symposium on What Do the Natural Sciences Know and How Do They Know It? at a conference of the National Association of Scholars in Cambridge, Massachusetts.