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News from ICTP 112 - Features - JD Bjorken
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.