From the book "The road to Reality" by Roger Penrose:
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[...] String theory is also a subject that is studied by a good many physicists, but does that make it physics? This raises the issue of fashion in fundamenta physical research. Let me begin by quoting a survey carried out by Carlo Rovelli, and reported in his address to the International Congress on General Relativity and Gravitation, held in Pune, India, in December 1997. Rovelli is one of the originators of the loop-variable approach to quantum gravity, and he claimed no professionalism in the conducting of his survey. Yet the results he found certainly reflect what my own (unsubstantiated) expectations would have been. He made a count of articles on the subject of quantum gravity published over the previous year, as recorded in the Los Angeles Archives. The rough average of papers per month, in the various approaches to the subject, came out as follows:
String theory: 69
Loop quantum gravity: 25
QFT in curved spaces: 8
Lattice approaches: 7
Euclidean quantum gravity: 3
Non-commutative geometry: 3
Quantum cosmology: 1
Twistors: 1
Others: 6
It will be noted that there were more articles in the area of string theory than in all the other areas put together. It seems to be a general view that if such a survey were repeated today, the preponderance of string theory papers would be even greater. If we were to think of scientific research as being driven by the principles of democratic government, then we would see that owing to an absolute majority being with the string theorists, all decisions as to what research should be done would be dictated by them! Fortunately, the criteria of science are not those of democratic government. It is right and proper that minority activities should not suffer merely by virtue of the fact that they are in the minority. Mathematical coherence and agreement with observation are far more important. But can we ignore the whims of fashion altogether? Certainly we cannot. In addition to many less believable ideas, very fashionable in their day (such as the 11-dimensional supergravity notion of seven extra dimensions constituting a ‘squashed 7-sphere’), I can recall many fashions of the past that seemed—and still seem—to me to contain very significant truths (such as Regge trajectorie and Geoffrey Chew’s analytic S matrix), but which have now been out of fashion for decades. To some extent, the popularity of a theory provides a measure of its scientific plausibility—but only to some extent. It is also true that, as with business concerns, it is the large ones that have a natural tendency to get larger at the expense of the smaller ones. It is not hard to see why that should be the case also with scientific fashions, particularly in the modern world of jet travel and the internet, where new scientific ideas spread rapidly across the globe, being propagated by word of mouth at scientific conferences or almost instantaneously transmitted by e-mail and on the internet in (frequently unrefereed) scientific articles. The often frantic competitiveness that this ease of communication engenders leads to ‘bandwagon’ effects, where researchers fear to be left behind if they do not join in. Fashion need not be so much of an issue with those theoretical ideas that continually come under experimental scrutiny. But with ideas that are as far from the possibility of experimental conWrmation or refutation as are those in quantum gravity, we must be especially cautious in taking the popularity of an approach as any real indication of its validity. [...] There is a related issue which makes it difficult for researchers, particularly young ones, to break away from the fashionable lines of research even if they wanted to. This is the sheer quantity of disparate and difficult mathematical ideas that they are confronted with in modern mathematical physics. It is hard enough to single out one small part of one particular line of work and to try to master it. To be able to make an authoritative
comparative study of the overall merits of several different lines at once would certainly be beyond the capabilities of most young researchers. If they are to make a choice, they must rely on the preferences of those who
are already established researchers, and this can only add to the propagation of already fashionable lines of work, at the expense of those that are less well known. Although my remarks above have been aimed at the kind of theoretical research that is unconstrained by experimental results, the element of fashion is not unimportant in relation to experiment also, but for a somewhat different reason. This springs largely from the enormous expense that is usually involved in the setting up of experiments at the frontiers of fundamental physics. Since most experiments are indeed so expensive, they normally require government support, or the support of large commercial concerns, and there will be the need for numerous committees to decide whether to go ahead with an experiment, or whether this or that type of experiment would make a better use of limited funds. It is natural that the scientifically knowledgeable members of these committees should be those who have establised themselves for their part in developing ideas that have successfully led to the current perspectives. Thus, they would tend only to favour experiments that directly address questions that seem natural from these particular perspectives. There is therefore a significant tendency for theory to get somewhat ‘locked’ into particular directions. It could well be very hard to make any major change in direction for this kind of reason. One might have thought that there is no real danger here, because if the direction is wrong then the experiment would disprove it, so that some new direction would be forced upon us. This is the traditional picture of how science progresses. Indeed, the well-known philosopher of science Karl Popper provided a reasonable-looking criterion14 for the scientific admissability of a proposed theory, namely that it be observationally refutable. But I fear that this is too stringent a criterion, and definitely too idealistic a view of science in this modern world of ‘big science’. Let me take the example of supersymmetry in modern particle physics. It is a theoretical idea with a certain mathematical elegance and which makes the theoretician’s life easier in the construction of renormalizable QFTs. Most importantly, it is a central ingredient of string theory Its status among theoreticians these days is so strong that it is almost considered to be part of today’s ‘standard’ particle-physics model. Yet, it has no (serious) experimental support, as things stand. The theory predicts ‘superpartners’ for all the observed fundamental particles of Nature, but none of these has so far been observed. The reason that they have not, according to supersymmetry theorists, is that a symmetrybreaking mechanism (of unknown nature) causes the superpartners to be so massive that the energies needed to create them are still beyond the scope of present-day accelerators. With increased energy capabilities, the superpartners might be found, and a new landmark in physical theory would be thereby achieved, with important implications for the future. But suppose that still no superpartners are actually found. Would this disprove the supersymmetry idea? Not at all. It could (and probably would) be argued that there had simply been too much optimism about the smallness of the degree of the symmetry breaking, and even higher energies would be needed to find the missing superpartners. We see that it is not so easy to dislodge a popular theoretical idea through the traditional scientific method of crucial experimentation, even if that idea happened actually to be wrong. The huge expense of high-energy experiments, also, makes it considerably harder to test a theory than it might have been otherwise. There are many other theoretical proposals, in particle physics, where predicted particles have mass–energies that are far too high for any serious possibility of refutation. Various specific versions of GUT or string theory make many such ‘predictions’ that are quite safe from refutation for this kind of reason. Does the ‘un-Popperian’ character of such models make them unacceptable as scientific theories? I think that such a stringent Popperian judgement would be deWnitely too harsh. For an intriguing example, recall Dirac’s argument that the mere existence of a single magnetic monople somewhere in the cosmos could provide an explanation for the fact that each particle in the universe has an electric charge that is an integral multiple of some fixed value (as is indeed observed). The theory which asserts that such a monopole exists somewhere is distinctly un-Popperian. That theory could be established by the discovery of such a particle, but it appears not to be refutable, as Popper’s criterion would require; for, if the theory is wrong, no matter how long experimenters search in vain, their inability to finnd a monopole would not disprove the theory! Yet the theory is certainly a scientific one, well worthy of serious consideration. We see how strongly matters of scientific fashion can influence the directions of theortical scientific research, despite the traditional protestations from scientists of the objectivity of their subject. Nevertheless, I should make it absolutely clear that the apparent lack of objectivity is not the fault of Nature herself. There is an objective physical world out there, and physicists correctly regard it as their job to find out its nature and to understand its behaviour. The apparent subjectivity that we see in the strong influences of fashion, referred to above, are simply features of our gropings for this understanding, where social pressures, funding pressures, and (understandable) human weaknesses and limitations play important parts in the somewhat chaotic and often mutually inconsistent pictures that we are presently confronted with.
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ROGER PENROSE: "The road to Reality".
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