ICTP Dirac Medallist J.D. Bjorken contends that the way science is done depends crucially upon the presence of quality data, and especially upon the rate at which it is acquired.

Data Matters

For most of my career I have chosen to stay close to data. The 1960s was a golden age for particle physics thanks to remarkable advances in accelerator physics-progress matched by the increased power and sophistication of particle detectors. When I began my career, for example, it was unthinkable that the strong force would be so quickly understood. The weak force looked to be as big a problem. Now we are in remarkably good shape in understanding both.
What matters most for progress is a steady advance in technology. Next is steady progress in experimental techniques, along with the opportunity to carry out the experiments themselves. Theory is at the bottom of the list.
Of course, technology, experiment and theory are all essential components for the advancement of scientific knowledge and strong feedback loops among the three are vital.
What's also important is how fast things happen. When data is coming in quickly, with more in the pipeline (on a time scale of a few years at most), researchers can take a detached and objective 'scientific' viewpoint. "If such and such is measured, then I am right. But if it comes out differently, then so-and-so is right." Either way we will soon know much more.
On the other hand, if data is not going to arrive for a long time, then people tend to develop more rigid viewpoints and to be more dismissive of alternative points of view. I first saw this in the cosmic-ray community in the 1960s, where progress moved slowly before the proton-decay experiments spurred a technological revolution in the field. Before that revolution, individual events became institutionalised and created communities with fixed opinions that simply would not have taken hold if the field had been more dynamic.
Today the pace of progress in elementary particle physics has slowed. Experiments have become big, expensive and time consuming. In addition, the standard model works too well and does not provide researchers with an abundance of unanswered opportunities that are within the range of experimental investigation.
This has led to more hardened institutionalised opinions than would be the case were the field more dynamic experimentally. I think weak-scale supersymmetry is much less of a sure bet than is generally assumed. Emphasis on supersymmetry has had the effect of overfocussing the search for dark matter onto WIMPs (weakly-interacting massive particles) at the expense of other alternatives, especially axions.

James D. Bjorken

Similarly, ideas that are 'string-inspired' more readily receive certification-and funding-than those that are not. Real long-shots like large extra dimensions and/or weak-scale strong gravity get more serious attention than they probably deserve.
My current interests focus on gravity and cosmology. I am a newcomer to the field. Thus far I perceive the gravitation-theory community to be fragmented into relatively isolated subcommunities, again attributable to the lack of data. But this is not universally so. For example, there are links with observational cosmology and the study of black holes as well as experimental investigations into gravitational radiation and Lorentz noncovariance. I do not have much experience with these subcommunities, but would venture the guess that they are more eclectic and inclusive than those communities dealing with the more formal or experimentally remote subfields.
Then there is the string community, which to a large extent goes its own way. It remains almost completely detached from data and dismissive of alternative approaches to the problems it proposes to address.
I frankly do not like this situation at all. The string theory community seems driven by a conviction that their basic ideology is correct, a conviction largely based on aesthetic grounds. I am very skeptical of any such ideological position, primarily because it is likely wrong. Humility should be the order of the day. Given the speculative nature of the subject, doubt and cross-fertilisation among different approaches should drive the research effort.
I find it paradoxical that ideas which are about to be tested experimentally are treated with a sense of skepticism and doubt, while much more speculative ideas-for example, string theory-are held with a greater sense of certainty. There is, however, an easy explanation for this paradox and that explanation can be conveyed in one word: fear.
In vibrant fields of observational science, practitioners cannot be too dogmatic or doctrinaire for the simple reason that their ideas will soon be put to the test. Unless there is an unusually high level of certitude, it is not a good idea to be dogmatic. There is too much to lose, whether it is just feeling bad about being wrong, being embarrassed, or even having more trouble getting a job.
It makes a big difference behaviourally when science is strongly data-driven, with the 'fear factor' front and centre. And this difference feeds back into improved sociology throughout the entire scientific community. On the other hand, when there is no fear factor, there is no penalty for dogmatism. And so dogmatism often emerges.
I do not mean to imply that science which is not data-driven is not good science. That would leave out all of mathematics. And aesthetic judgments do matter. But I do think that when practising such science one should exhibit at least as much skepticism and doubt as certainty, and as much tolerance for other points of view as is the case in a strongly data-driven environment.

James D. Bjorken
Stanford Linear Accelerator Center
ICTP Dirac Medallist 2004

BIG STEPS AND SMALL
While scientists continue to pay a great deal of attention to such big questions as the origin of time, the boundaries of space, and the nature of the 'ultimate' theory, it is not clear that these questions are ready for serious science. As I observe in the main article, I consider it very probable that all ideologies presently addressing such questions are wrong. History is my guide in making this assessment. The great thinkers of the past, including Johannes Kepler, Isaac Newton and Albert Einstein, had plenty of ideas of what the big picture should look like. But in the light of present data, the facts simply do not fit their ideas. I think a necessary condition for presuming that the present situation is different is that there exists concrete evidence for convergence toward simplicity. Yet, neither observational cosmology, nor 'string phenomenology', nor phenomenological supersymmetry, at the electroweak scale as well as at the grand-unification scale, points the way toward a simpler big picture. There remains a clutter of poorly understood numbers no matter where one looks. Understanding the big picture, if attainable at all, is very far away.

STRING THEORY: TAKE 2
String theory deserves to be around for a long time. Putting ideological and social issues aside, string theory is a superb technology. The string theory toolkit has already supplied many new concepts and insights into particle theory and cosmology. Very probably some, if not many, of those elements will find their way into future theories. Nevertheless, I think it is a mistake to assume string theory contains the whole story. Classical textbook gravity, effective field theory, thermogravity, holography, loop gravity, and emergent gravity all deserve serious attention.

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