A physicist
who turns 100 this year would have been working on his doctoral thesis in 1931, the year the American
Institute of Physics was founded. The student would have been surveying physics and its allied
sciences to spot some promising area on which to stake a career. What would the 25-year-old have
seen in 1931? And how did the apparently promising areas play out over the next three-quarters of
a century? How does the 1931 landscape compare with what a physics student sees today? What important
things would the 1931 student have failed to see? What can we learn from these questions as we look
over our field today?
A quick way to compare the situations
then and now is to look at the Physical Review. The most obvious difference is size. Last
year's volumes take up about 30 times as much shelf space as did the two 1931 volumes—not to
mention that the pages have gotten bigger and the print smaller. To be sure, the 1931 student also
had to read Zeitschrift für Physik and Nature. Even so, the student could
have read every important article in the field. Today such breadth is out of the question; dozens
of subfields each publish more than the entire physics community did back then. To get an overview
of physics nowadays, you must read review journals; scan news stories in Science, Nature,
and PHYSICS TODAY; and—that old standby—talk with professors.
A physics student in 1931 could easily
spot some exciting topics. Barely five years had passed since Erwin Schrödinger, Werner
Heisenberg, and others gave quantum mechanics a solid mathematical foundation. Now they were
struggling to extend and interpret the theory. Albert Einstein and Niels Bohr, the two founding
intellects of the revolution, were arguing over the fundamental reality of quantum states. If
that argument seemed closer to philosophy than to experimental science, quantum mechanics clearly
had the potential to resolve long-standing scientific questions.
Physicists had understood
for two decades that atoms were composed of electrons and nuclei, but at that point they had gotten
stuck. Now in 1931, Paul Dirac proposed that the electron has an antiparticle, what would come to
be called the positron. This was a hint that particles come in families with positive, negative,
and perhaps neutral members. Dirac was a year short of his 30th birthday. Younger still, at 26, was
Caltech student Carl Anderson, just getting into the cosmic-ray studies that in 1932 would demonstrate
the positron's existence.
All kinds of bizarre ideas
about particles were in the air. Wolfgang Pauli, for example, was developing the neutrino hypothesis,
although he wasn't quite ready to publish it. On the experimental side in 1931, Ernest Lawrence
at the University of California, Berkeley, completed a little prototype cyclotron that accelerated
protons to 1 MeV on the way to higher energies that he hoped would break into the nucleus. He had just
turned 30; so had Robert Van de Graaff, who was developing another type of particle accelerator.
With such a rich smorgasbord
of opportunities, where was a young physicist to begin? Einstein was embarked on a search for a unified
field theory, and lesser mortals could at least try to go a step or two beyond quantum mechanics.
That was the hope, for example, of 27-year-old Robert Oppenheimer, newly appointed to the Berkeley
faculty. But such hopes were frustrated. Dirac's relativistic equations had put a capstone on
quantum theory; the edifice was complete. Einstein's unified theory turned out to be mathematically
ingenious but physically vacuous, and nobody could do better.
Within the narrower scope
of Einstein's general theory of relativity, an opportunity appeared in 1931 when an overlooked
work by the Belgian cleric Georges LeMaître appeared in English translation. Only then did
theorists read LeMaître's interpretation of the equations of general relativity and see
a connection with Edwin Hubble's recent demonstration that distant galaxies appear to recede
from us with velocities proportional to their distances. Hubble's discovery could be explained
by a continual expansion of spacetime. Einstein immediately abandoned the cosmological constant
he had introduced into the equations of general relativity to keep the universe from expanding.
The theoretical opening
was, however, illusory. Attempts to push general relativity into new areas got no further. In 1939
Oppenheimer and a graduate student, Hartland Snyder, did come up with a particularly weird consequence
of the theory—what would later be called "black holes." But at the time, the Oppenheimer–Snyder
discovery seemed little more than a mathematical curiosity that couldn't be connected to experiments
or observations.
In hindsight, it is clear
that one of the best roads forward for the physicist of 1931 was the one Lawrence was taking, along
with theorists like Heisenberg, Hideki Yukawa, and others. That road led to the discovery and understanding
of new nuclear particles. Physicists in 1931 recognized that the nucleus was a storehouse of enormous
energies, but few expected to unlock it soon, if ever. Within 15 years, however, nuclear fission
had totally changed international politics and seemed poised to revolutionize the world economy.
For physics, one consequence
was a spectacular change in the scale of instrumentation. Nobody looking at Anderson's little
cosmic-ray cloud chamber in 1932 could possibly have imagined today's gargantuan neutrino detectors.
Similarly, nobody looking at Lawrence's 11-inch cyclotron in 1931 could have imagined the Large
Hadron Collider with its 27-kilometer circumference, now nearing completion at CERN.
Such changes in scale brought
profound changes in physicists' careers and work styles. In 1931 only a minority of Physical
Review papers had more than one author, and usually no more than two. Today papers with hundreds
of authors are not uncommon.
The giant instruments
built in the decades after World War II created a baffling zoo of subnuclear particles. Whereas
experimenters in the 1930s strove to "split" the nucleus, nowadays Brookhaven's Relativistic
Heavy Ion Collider "melts" the proton into its constituents. The enigmas of the 1950s and 60s have
been resolved in our present understanding of quarks and allied families of particles. Every experimental
result, thus far, agrees with the predictions of the "standard model" completed in the 1970s. The
standard model of particle physics is arguably the major accomplishment of physics in the second
half of the 20th century.
That theoretical edifice
places us, in 2006, at a quite different stage from where physicists stood in 1931. Linus Pauling
was just then publishing The Nature of the Chemical Bond, using the new equations of quantum
mechanics to explain the rules for covalent chemical bonding. Others were applying the new theory
to calculate the positions and strengths of spectral lines with increasing precision. Today we
are several decades into an analogous program with the standard model.
Despite the model's unfailing
successes, basic questions remain unresolved. The very existence and number of the model's beautifully
symmetric families of hadrons and leptons pose an unmet challenge. As quantum theory underlies
the numerical regularities of atomic spectra, and as quarks underlie the great variety of hadrons
that emerge from high-energy accelerators, so the grand order of the standard model surely requires
a deeper explanation we have yet to grasp.
The standard model relies
on the old foundation of quantum theory. Another feature of the contemporary scene is the renewed
study of the now 80-year-old theory's fundamental characteristics. Lasers and other instruments
of surpassing delicacy nowadays pour out a stream of demonstrations of the validity of Heisenberg
and Bohr's interpretation of quantum mechanics. Yet those results only confirm Einstein's intuition
that quantum physics is too paradoxical ever to be reconciled with ordinary understanding. Meanwhile
physicists have also resumed the study of his general theory of relativity after a long period of
little progress. Again instrumentation has led the way, with new kinds of tests in terrestrial
laboratories, in space, and in astronomical observations. Like quantum theory, Einstein's equations
have passed all the tests so far.
The confirmations of both
theories leave us dangling. The standard model is not the long-sought unified field theory. Its
quantum basis has never been reconciled with general relativity. Some physicists hope that the
role played by quantum mechanics in the 1930s may soon be played by some form of string or brane theory
(see the essay by Jim Gates on page 54). Others suspect that string theory is more like the old aether
theory of electromagnetism. In the 1890s, leading physicists felt they were on the verge of a great
breakthrough with that theory, hoping that kinks in the aether and refinements of Maxwell's equations
would soon provide a simple, unified explanation of all phenomena.
In the first decade of the
new century, however, the mysterious quantum and the special theory of relativity showed physicists
how long and strange would be the road they had still to travel. Not until 1931 did they reach their
destination in Dirac's relativistic wave equation. In 2006, the situation of frontier theory
is arguably more chaotic. Nobody knows when, or if, a breakthrough will come.
Using quantum physics
While the search inward from the quantum
mechanics of atoms to subnuclear particles led to profound puzzles, a search outward into the world
of ordinary matter brought extraordinary practical success. Around 1931 Eugene Wigner liked
to tell his students at Princeton that if he dropped his glasses, the glass would break but the metal
frame would not, and nobody knew why. Today we can explain that, as well as the transparency
of the glass, the silvery shine of the frame, and almost anything else of practical significance.
Wigner and his students—for
example Frederick Seitz, 20 years old in 1931 but only three years from his PhD—and many other
physicists glimpsed the prospects for explanation that quantum mechanics opened up, although
they could not see how far it would lead. The most obvious path led to the study of solids, or at least
simple ones like crystals and superconducting metals. The path was not attractive to everyone.
Schmutzphysik (dirt physics), Pauli called it, not just for its concern with crystal impurities
but also for its connections with applications and hopes for monetary profit. Yet solid-state
physics gradually won respect as it worked toward explanations of long-mysterious properties
of matter.
One promising route lay
through low-temperature experiments, which at that time had reached about 1 K. That was
cold enough so that, for example, Willem Keesom and his colleagues could measure shifts between
helium I and helium II as they sought an interpretation in terms of phase transitions. No less intriguing
were advances in understanding solids at room temperature. Already in 1931 Hans Bethe, a student
who turned 25 that year, found a solution of the Ising model for a one-dimensional lattice. That
solution would be a key to the more elaborate model that eventually helped explain magnetism and
other collective phenomena. It was also in 1931 that theorist Yakov Frenkel proposed excitons,
a new sort of "particle" that could exist only as a result of interactions of other particles in an
array. The notion of particle-like excitations was a clue to understanding many phenomena, including
superconductivity. A still more imposing landmark of 1931 was Heisenberg's introduction of the
concept of "holes" in a conductor's electron sea. The idea was soon applied in the comprehensive
theory of metals and semiconductors that Alan Wilson was developing with Felix Bloch.
Today the largest field
in physics, encompassing more than a fifth of all the PhDs granted in the last decade and a still higher
fraction of physicists' careers, is the study of "condensed matter." The term replaced "solid-state"
in the 1960s following successes in the study of fluids. Since then, the rubric "materials science"
has been added, pointing toward the proliferation of practical applications. In basic physics,
superfluidity research—now reaching into the nanokelvin range—keeps producing
surprises. Meanwhile, research on magnetic materials not only has been intellectually satisfying
but has brought exponential progress in data storage for computing. Computers themselves, of
course, also rely on the manipulation of holes in semiconductors. Computer calculations nowadays
increasingly illuminate fluidic and chaotic phenomena and many other things far beyond the reach
of calculation 75 years ago.
Everyone knows how applications
of solid-state physics have changed industry and daily life. The students of 1931 could not have
imagined the consequences, from iPods to "smart" missiles. But they had seen equally revolutionary
changes coming from physics even in the short time since they were children, such as the proliferation
of radios, airplanes, and electric motors. They understood that the results of their own research,
whatever those results might be, should find fabulous applications with far-reaching social
consequences.
Those two routes forward with the new
quantum mechanics—inward into nuclei and outward into solids—were more obvious than
some of the other roads that were in fact opening up in 1931. One example is the work of Ernst Ruska,
another of the students who turned 25 that year. When he focused beams of electrons to create the
first electron microscopes, few could have guessed their value for probing matter. Instrumentation
such as positron emission tomography now finds applications not only in physics but in medicine
and physiology—even in the investigation of mental states. Manipulating beams is also central
to the new nanotechnology, which arranges individual atoms into devices that the most adventurous
science-fiction writers of the 1930s never imagined.
To be sure, the best molecular-scale
devices in 2006 are rudimentary compared to the intricate machines into which living cells have
evolved over the past few billion years. But of all the ways forward that we can see today, I think
the clearest is the one leading toward the full control of such machinery. When we get there, the
old terms "medical physics" and "biophysics" will have vastly expanded meanings.
The growth of such hyphenated-physics
disciplines, only dimly perceived in the 1930s, has been one of the most important trends of the
past half-century. The rise of geophysics is particularly instructive. The large data sets necessary
for most of the progress in that field were first made available in about 1957 by the global collaboration
of the International Geophysical Year and by the advent of satellites. In 1931, for example, a large
majority of geologists believed that the theory of continental drift was ruled out by physical
limitations on the motions of rock. Today seismic tomography uses computers to study in depth the
structure of moving continental plates.
The atmospheric sciences
offer especially good examples of that sort of progress. My personal nominee for an outstanding
publication of 1931—although it was entirely ignored by other scientists at the time—is
a Physical Review paper on atmospheric spectroscopy by Edward Hulburt.1
His innovative calculation supported a hypothesis published three decades earlier: Doubling
the carbon dioxide in the atmosphere would bring a significant rise in surface temperature. In
1931, Hulburt was almost alone in finding the idea plausible. Not until the 1950s did others make
solid measurements of the absorption of infrared radiation using improved detectors. And theorists
used those measurements in computer calculations that were hard to dismiss. Only in the present
decade have we gotten data and computer models good enough to convince virtually all experts that
greenhouse warming poses a grave risk to the well-being of our civilization.
Astrophysics is yet another
hyphenated field in which we can see some key developments of the 1930s only in hindsight. In 1931,
for example, Bernhard Schmidt invented an optical system for a telescope that could take high-resolution
photographs of a wide area of the sky. Fritz Zwicky was one of the few who saw an opportunity. He turned
a Schmidt telescope to a large cluster of galaxies and concluded from their relative motions, as
measured by redshift, that the cluster contained a lot of unseen mass. That made little sense to
people at the time. Today, the wide-field Sloan Digital Sky Survey is producing huge quantities
of data that not only make a convincing case for Zwicky's "dark matter"; they also give evidence
of "dark energy" that looks like a manifestation of the cosmological constant that Einstein abandoned
too hastily after Hubble's discovery.
It was also in 1931 that
the 26-year-old engineer Karl Jansky began using a crude antenna to study radio telephone interference
for Bell Labs. He would later demonstrate that some of the interference he found was radio emission
from the Milky Way galaxy. Once Jansky's bosses understood that the galactic emission would not
interfere with communications, they assigned him other work. Today astronomers use radio and
other waves outside the visible spectrum to probe objects ranging from neutron stars to the cosmic
microwave background, a remnant of the Big Bang. These are realms that scientists of the 1930s lacked
the observational data to picture in their minds, let alone study.
Another candidate for
the most overlooked paper in that period would be one published way back in 1917 but largely forgotten
in the 1930s despite its author's reputation: Einstein's prediction of stimulated emission of
photons (see the article by Daniel Kleppner in PHYSICS TODAY, February 2005, page 30). Today lasers
are used everywhere. Why did no one notice that path forward? Because it was too great a conceptual
and technical leap from Einstein's curious idea to a working device. The laser was actually approached
stepwise through the maser, which could not be built until the development of microwave techniques
for radar in the 1940s. So it's not so much an overlooked path as a technology that would appear only
after the rise of other technologies.
I believe we have come here
upon a general rule. If physicists in 1931 failed to see some potential paths, it wasn't for lack
of creative imagination. What they lacked was data and the instruments and collaborative networks
to get the data, and in some cases the computers needed to analyze them. Like many other things important
to science today—the mid-ocean rifts, Bose–Einstein condensates, the cosmic microwave
background radiation, and so forth—the laser was something that people in 1931 simply had
no way of foreseeing.
A community transformed
Physics is not just an intellectual
exercise, but also a community of people and their institutions. The first step we should look at
in the physicist's career is education. The students of 1931, transported to a physics department
of comparable size today, would find many familiar things in the setup of textbooks, courses, examinations,
seminars, and thesis mentoring. For better or worse, graduate education in the 21st century retains
most of the structures that originated in 19th-century Germany.
Beyond their education,
the students of 1931, like those of today, were thinking about jobs. Prospects looked poor as the
Great Depression deepened. Most physics students would have expected to get a job in academia,
some would have considered jobs in industry, and a few would have sought work in a government institution.
But in 1931 none of those prospective employers were hiring anyone. Fortunately for the students,
within a few years universities began to expand again, followed by industrial and government labs.
The Depression and World War II only temporarily interrupted the exponential rise in the number
of physicists, which doubled about every dozen years.2
This growth by orders of
magnitude produced a qualitative change. Many physicists in the 1930s, reading everything important
in the journals, would shift after a few years from one subfield to another. By the 1960s, it was rare
for anyone to publish in more than one specialty. Meanwhile physicists found they no longer knew
personally all the main Figures in the field. From a community as close-knit as a village, the physics
profession became a sprawling confederation of interlocking subfields, each with its own institutions
and customs, with no clear leaders of the whole.
The rise of hyphenated
physics compounded the situation by separating the physicists who went into astro- or geo- or biophysics
even farther from their colleagues. Yet far more than in the 1930s, physicists today have found
that their training can help them in very different undertakings, from Wall Street to sculpture.
Angela Merkel, Germany's chancellor, started her career as a physicist. So did Askar Akayev, who
returned to the community after he was deposed as leader of Kyrgyzstan.
Of course the exponential
rise in numbers could not continue indefinitely. In the late 1970s, the number of physicists in
the developed nations reached the limit that society was willing to support. Since then, their
numbers have oscillated around that limit, which has been rising gradually with the growth of the
economy. (Faster growth continues in some developing countries.)
Because fewer students
means fewer professors, the end of exponential growth left us with a different career distribution.
The gap has been partly filled by government and government-contract laboratories, which were
of little importance in 1931, when they employed only 5% of all American Physical Society members,
mainly in the National Bureau of Standards (now NIST). Today they employ about a quarter of APS members.
A related change is the
strong connection that now exists between physics and the military establishment. That connection
has contributed to a mistrust of physics among the public at large. Such mistrust is not new. In 1931,
some linked science to the novel horrors of World War I, while others linked it to technologies that
brought economic dislocation and ideas that challenged religious faith. Indeed the founders
of the American Institute of Physics, while they acted primarily to deal with the Depression's
disruption of journal publishing, also asked the new institution to work on improving the public
image of physics. Today such work is needed as much as ever.
Public mistrust of physics,
now as then, is mostly outweighed by an awareness of its benefits. A student of 1931, transported
to a modern laboratory, would probably stare most of all at computers. The computerization of many
aspects of the developed economies has been as astounding as electrification was in the decades
preceding 1931. The 1920s had seen a corresponding increase in jobs for physicists in industry,
and the years since the 1980s have seen an even greater rise. Whereas in 1931 about 12% of APS members
worked in industry, today 24% do. For all AIP member societies taken together, the fraction is 27%.2,3
The next 75 years
Can we learn anything about the future
by comparing the situation in 1931 with the situation today? Most striking is how different the
two are. Some of the trends that have brought that change can be extrapolated forward. In the next
75 years, we can hardly fail to continue to expand the uses of physics and the associated job opportunities.
We can also expect continuing improvements in collaborative organization, aided by advances
in communication. And we can look for a continuing increase in diversity as women and currently
underrepresented minorities join the enterprise in larger numbers. But scientists can't expect
the transformative orders-of-magnitude growth seen in the past 75 years. We cannot, after all,
account for more than 100% of gross world product! Growth will probably track the changes of national
economies. And what will those be?
Historians will tell you
that the one thing you can learn from history is that it's unpredictable. You can't project every
linear trend forward. Societies are prone to spurts of exponential growth and, more often than
we like to think, collapse. We do have reason to worry about that. Plausible calculations show that
humans have already exceeded the planet's carrying capacity, and we are living off resources that
cannot be quickly renewed. In 75 years, for example, there is little chance that we will be consuming
as much petroleum as we are now, or even as much water. And it is likely that climate changes will be
causing grave harm.
It is scarcely possible
that the world in 2081 will have 10 billion people each consuming the way the average American—or
even the average Russian—does now. Global per capita consumption of physical and biological
resources is almost certain to remain well below the current developed-world level. Does that
mean that our economies and standards of living must crash? Not necessarily. Against the declining
curve of resources, we can match an exponentially rising curve of capabilities. Moore's law of
doubling every couple of years is valid not only for processing speed but also for memory capacity,
the synthesis of DNA molecules, and more. It predicts a rise so fast that some people think that within
a few decades we will have soared to an "omega point" of effective intelligence beyond which our
present limited vision cannot see. We are in a race to improve our capabilities faster than we degrade
our resources. For winning such a race, nothing is more essential than physics.
Physics is not now at the
culmination of a surge of fundamental discovery comparable to the development of quantum mechanics,
which students of 1931 rightly foresaw could lead to amazing advances in many areas. Nevertheless,
now as then, there are at least two obvious paths forward. On the one hand, we are challenged by deep
unknowns in the fundamental nature of matter. On the other hand, we can go much farther in straightforward
understanding and manipulation of the immediate material world. On the first path, we can hope
for strange insights into both fundamental particles and cosmology, with unforeseeable uses.
On the other, we can hardly fail to find more wonders in the physics of condensed matter, and beyond
in the realms of nanophysics and biophysics.
What about advances that
we can't predict? In the past we have seen many unanticipated discoveries. And most of them—from
lasers to dark matter, from medical physics to climate change—depended on new instrumentation
(including computers) and extensive observational programs. Today's student should pay special
attention to new developments in instrumentation and collaborative organization. We could try
to predict what new instruments and programs may come along in the next couple of decades. Beyond
that we can only be confident that they will keep coming, each building on what came before. There
is every reason to look forward to as many surprising discoveries and extraordinary applications
in the next 75 years as we have seen in the past 75.
This article is adapted
from a talk given at AIP's 75th-anniversary celebration in May 2006.
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