Nobel Prize lecture: John J. Hopfield, Nobel Prize in Physics 2024

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Honored Nobel laureates, your excellencies, distinguished colleagues, dear students,
ladies and gentlemen, a warm welcome to the 2024 Nobel Lectures in Physics.
This year's Nobel Prize in Physics is about artificial neural networks and their central role
in the revolutionary development of machine learning.
Machine learning is the ability of a computer to learn from examples. Instead of following
instructions of programmed recipes, artificial neural networks are the foundational building
block of machine learning. By feeding a neural network with large amounts of data,
be it images, speech or music, it is trained to recognize patterns.
Once it has learned to find these patterns, it can generate new data that resemble the ones
in the given data set. Giving it millions of pictures of cats, it will learn what a cat looks
like and how it differs from a dog, without having to follow gradually narrowing programmed
subroutines describing the taxonomy of mammals and the meowing and purring sounds that they make.
I do not need to convince you that today this new technology has drastically changed our daily
lives. Also in research areas as diverse as particle physics, protein crystallography,
material science, astrophysics, artificial neural networks have contributed to discoveries
and inventions of great importance. But how did it all start? How are artificial neural networks
built and how do they work? As long ago as the early 1980s, this year's Nobel laureates
John Hopfield and Geoffrey Hinton made foundational discoveries and inventions
that enable machine learning with artificial neural networks.
Incurably curious about how our brain works with the billions of neurons wired together
by incountable connections, they searched for answers to the questions of how we humans learn,
how we process and categorize information and how we recognize new information by association
to the stored memories and experiences. John Hopfield made groundbreaking contributions
by describing the dynamic model of associative memory using fundamental concepts from physics,
the physics that describe collective phenomena. He used the same equations and models that
govern the physics of magnetic materials to describe the interactions in the brain.
Geoffrey Hinton applied concepts from statistical physics to develop efficient neural networks
with multiple layers. He developed learning algorithms and methods for the networks to
self-improve. It's now my pleasure and great honor to introduce our first speaker, John Hopfield.
John Hopfield was born in Chicago in 1933. He received his first degree from Whartmore College
in 1954. He earned his PhD in 1958 from Cornell University. He was appointed professor of physics
at Princeton University in 1964 and in 1980 he became professor of chemistry and biology at
California Institute of Technology. He returned then to Princeton University where he presently
is affiliated as emeritus professor in molecular biology. Please join me in welcoming John Hopfield
to the stage to tell us about the developments that led to this year's Nobel Prize for physics.
Thank you for the introduction. Thank you, thank you. Thank you for coming. There we go.
My first full-time employment was at the Bell Telephone Laboratories where the transistor
had been invented 10 years earlier. I joined its six-person theoretical physics group
in March 1958. A full half day of employment was spent on administrative detail.
I headed for my new office. Unpacking a few books and journals took an hour. A visit to
the fifth floor stockroom produced some lined tablets, pencils, and a hand crank pencil sharpener.
I returned to my office and sharpened several pencils. Now what should I do?
That stark question has plagued me many times in my research and teaching career.
Every scientist, every scholar faces this vexing issue of what to work on each day.
Most respond by working today to extend a little yesterday's line of thought or line of measurement
or plot development. Most of us spend little time thinking seriously about choosing the research
area we next pursue. You hear very few lectures on how to choose the research direction.
Yet the choice of problem is the primary determinant of what one accomplishes in science.
Two papers that I wrote more than 40 years ago form the basis of the work often referred to
as the Hopfield model. I will first describe how the subject developed, some of the choices made,
the situations encountered, ultimately defining the germ of a useful viewpoint
on which mathematics could be overlaid. For shorthand, I refer to this process as
problem choice, but it really is a description of how a useful point of view
was winnowed from an analysis of random events from my past.
When viewed with historical hindsight, the development of a problem is often presented
as a logical sequence of correct choices in a branching decision tree.
Without the benefit of hindsight, research is often pursued in random directions, taken with
no overwhelming insight. To me, growing up with a father and mother, both of whom were physicists,
physics was not defined by subject matter. The atom, the troposphere, a piece of glass,
my bicycle, a magnet, the atom, these are all incidentally the subject matter.
Physics was a point of view that the world around us, with effort, ingenuity, and adequate resources,
is understandable in a predictive and reasonably quantitative fashion.
Being a physicist is a dedication to a quest for this kind of understanding.
Of course, neither of my parents ever spoke of what defines physics. It was only much later
that I thought about how my upbringing had defined a useful world view.
I grew up taking things apart, seeing how they work, repairing bicycles, exploring chemistry,
building flyable model airplanes, crystal sets, and simple radios,
playing with batteries, and learning to think with my hands and manipulate real objects.
Each thing I understood, why my bicycle brakes got hot when they were used, how a consistent story
could be incorporated as a small part of a much grander understanding in a complicated system,
heedless of the financial consequences of being a physicist, I only briefly considered an
alternative career. My high school chemistry teacher had been superb, while my physics teacher
lacked an understanding even of the rudiments of electricity and magnetism.
Thus influenced, when listing potential majors on college applications, I wrote
Physics or Chemistry. At Swarthmore College, I was assigned Professor William Elmore as my advisor.
We met in his office to discuss my future. He located the student card describing my high
school record, and thus the field of study I was interested in, took out a pen and crossed
out two words, remarking, I don't believe we need to consider chemistry. And that is the way my
education went. An arbitrary act by Bill Elmore had much to do with my being here today. I began
looking at graduate schools in physics with an eye to what I might specialize in. My upbringing
had particularly focused my interest on the physics of the daily world and its technologies.
I went to graduate school at Cornell because in 1954, Cornell had a segment of the physics
department interested in a field called solid state physics. In the middle of my second year
at Cornell, I approached theoretical physicist Albert W. Overhauser to ask if he would supervise
my thesis and help me find a thesis problem. Through courses and doing problem sets,
I was rapidly acquiring the tools of theoretical physics, but I had no idea
of how to find an appropriate research problem.
Happily, Overhauser had a list of interesting puzzles. They were often in the form of a
paradox. Elementary theoretical analysis of a particular phenomenon in solid state physics
is resolved to be. Root A over here is what experiments get, and they're totally different.
In most paradoxes in this list, Overhauser himself had no idea of what was producing the
conflict between a common sense theoretical view and the experimental facts. I picked a problem
having to do with the radiative lifetime of an exciton in a crystal. Overhauser was enormously
supportive as a listener and a critic when I went to see him, but finding direction and resolving
technical theoretical issues were entirely my problem. The great gift he gave me was the
ownership of an interesting question and total responsibility for research and progress.
I've done my best to repay my mentors, my mentor Bill, my mentor Overhauser,
through similarly nurturing another generation of independent students,
a couple of which are actually here today.
PhD in hand, I took a position in the theory group at Bill Laboratories.
Conyers Herring was head of the group and saw me struggling to identify my next problem to work on.
He suggested visiting with experimentalists to get my own sense of where interesting puzzles
lay. This was the framework within which I met chemist David Thomas, and we formed a working
theory experiment alliance. It was to provide me with unanticipated problems and paradoxes for 10
years and provide AT&T with a major knowledge base in compound semiconductors. It garnered
David and me a joint Oliver E. Buckley Solid State Physics Prize from the American Physical Society
in 1969. At the time, no one would have guessed that the combination of light
and compound semiconductors would have a major technological role in the future.
By 1968, I had run out of problems in condensed matter physics, to which my particular talents
seemed useful. I went to the Cavendish Laboratory of Cambridge University in the UK
on a Guggenheim Fellowship for half a year, hoping to find new interesting avenues,
but found little for me. Returning from Cambridge to Princeton University and my consultancy in the
semiconductor group at Bell Labs, I ran into Robert G. Shulman, a chemist who was doing
the first high-resolution nuclear magnetic experiments on hemoglobin.
Bob told me about the cooperative oxygen binding at the four iron atoms in the center of the
widely separated heme groups of the protein. An incredible panoply of physics techniques
was being used to study the molecule. NMR, EPR, optical spectroscopy, neutron scattering,
mass power spectroscopy, all the clever experimental techniques in solid state physics
seemed relevant to understanding hemoglobin. Hemoglobin provided me a simple entrée from
condensed matter physics to biological matter physics. In both fields, the goal was to understand
how structure and low-lying excitations were related to measurable and relevant properties.
It seemed that my background in condensed matter physics might find good use in biology.
When Linus Pauling, a double Nobelist in chemistry and in peace, was asked about choosing
problems to work on, he remarked, I ask myself whether the problem I am considering is one to
which I am likely to make a contribution. I would clearly need to emulate Pauling.
I had become interested in the unexpectedly small number of mistakes
made in choosing the correct amino acid when the next amino acid is inserted in a protein
during protein synthesis within a cell. How might I make my physics background more likely to see
a solution to this problem? Free energy is the key. High-energy molecules like glucose or ATP
are expensive for a cell to make, and a biochemical process using unexpectedly large
numbers of high-energy molecules in a simple process must be paying dearly for that cost
or purpose. Suppose that the purpose was to proofread, to remove biosynthesis errors.
Perhaps experimental biochemists had not noticed because they did not know how to look.
I was successful in that problem. I found a plausible scheme for proofreading in protein
synthesis based on known biochemical detail and described critical experiments to test the theory.
I gave a talk at Harvard Medical School in 1976, ending with a brief account of proofreading
and my prediction about non-stoichiometry in protein synthesis.
The first question after my talk was Robert C. Thompson. He asked,
would you like to hear the results of such an experimental measurement?
And went on to describe his experiments, not yet published, in measuring the stoichiometry ratios
when a system was being pushed to proofread and when it was not. He described
experimental facts which just overwhelmingly pushed the idea
proofreading works that way. It was one of the biggest and most delightful
prizes of my brief career in chemistry.
Now, let's see if I can get this right. Yes. This 1974 paper was important in my approach
to biological problems, for it led me to think about the function of the structure of a reaction
network rather than just what is the function of the biological molecule.
Six years later, I was generalizing this view and thinking about networks of neurons
rather than the properties of single nerve cells.
This, writing this paper, doing this research also led me to think more about problem identification
and biophysical research. The unexpected success of this paper was due
to its formulation of a new biological problem and had nothing to do with my knowledge of
biochemistry or biophysics. Chance had favored the unprepared but the inquiring mind.
I spent the winter of 1977 at the Bohr Institute in Copenhagen as part of its sporadic but historical
outreach toward biology. My task was to run a broad modern biology for physicists seminar series.
In 1932, Niels Bohr had opened the International Congress on Light Therapy with a lecture entitled
Light and Life. Bohr asked whether a deep explanation of life itself
and the philosophical ambiguities of how to interpret quantum mechanics were intrinsically
intertwined. However, in 1977, my distinguished experts in biology emphasized what they understood.
They certainly did not describe biological science as being in the help, being in need of help from
physicists. I returned to Princeton without a new problem for myself. I was now looking for
a big problem whose resolution and understanding will be of significance far beyond its normal
disciplinary boundaries and will reorganize the fields from which they came. Bold, prone to failure.
My Princeton University office telephone rang shortly before my morning class.
Expecting a call about important things, tennis, I answered only to find Francis O. Schmidt on the
line. He said he ran the neuroscience research program at MIT, would be transiting Princeton
next Wednesday, and would greatly appreciate a half hour, no more of my time. I had never heard
either of Schmidt or the NRP needed to head off. That's what I'm supposed to avoid. Yes,
or needed to head off for lecture, thought, what's 30 minutes, and agreed to meet.
The following week, Francis O. Schmidt descended on me. He described his neuroscience research
program, which chiefly held small meetings in Boston, attended by 20 regular members
and 20 visitors. I told him I knew nothing of neuroscience. He said, that doesn't matter,
just speak on what interests you. So I talked about my theory of kinetic proofreading
and the general issue of accuracy and biosynthesis. The audience, neurologists, immunologists,
electrophysiologists, neuroanatomists, understood little of what I said.
It didn't matter. Frank wanted to add a physicist member to the group,
hoping to bring someone with diverse science experience to interact with his subject,
and perhaps help him become more integrated at a more predictive science. I was captivated by
the talks at the meeting. How mind emerges from brain is to me the deepest question
posed by our humanity. He was being pursued in narrow slices as little problems by the
NRP club of scientists with diverse talents and a great enthusiasm. But it appeared to
me that this group of scientists would never possibly be able to address the big problem,
because the solution can be expressed only as an appropriate mathematical language and structure.
None then involved with the NRP moved easily in this sphere. So I joined the group,
hoping to define, construct, or discover something I could usefully do in this field.
My basic education in neurobiology came from attending the semi-annual NRP meetings,
sitting next to world experts in their field, who would patiently explain to me
what this figure was really trying to talk about. I tasked myself with finding an integrated
physics view of trying somehow to rise above the disjoint details of lectures,
neuroanatomy, electrophysiology, learning in the rat and Alzheimer's disease,
and find some kind of integrated structure to theory.
In 1979, Caltech appointed me to a professorship jointly between chemistry and biology,
and I left Princeton. The quantum computing facility at Caltech was a splendid environment
for trying out models. It supported multi-user real-time computing, video displays,
direct keyboard input. All things you say are trivial, but in 1979 they were a marvelous thing
to discover. My insight was that basic machine or brain operation followed, computed by following a
machine trajectory in state space from the beginning, where you put the program and data,
start it, and then every tick of the clock, the state of the system moved.
Ultimately, the state stopped changing. When the state stopped changing,
the computation must be done. You'd read out some of the registers,
and the computation had actually been done by following a dynamical trajectory from start
to end. That trajectory needs stability against perturbations to reach a correct answer,
in spite of noise and system imperfections. This picture of batch-mode digital computation is
a schematic to try to get the impression of, here's what Hopfield views as computation.
I turned finally to a more specifically chosen question, just a general one,
and trying to focus on something which an animal needs, or animals are known to have.
This turned into something which became fundamentally related to behaviors
a psychologist might call associative memory, or an engineer might call content-addressable memory,
or another psychologist would describe this as declarative memory, something you can describe.
These names share a common feature. They share a common basic paradigm that can be described
as computing by a dynamical system which follows a trajectory which is stable,
and those small perturbations away from that trajectory are squeezed back onto it,
and that's the way you go from start to finish in a noisy system. That's what
content-addressable memory does in a very different regime.
But all these, a whole bunch of things associated with, associated, I can't get by without using
a term. I'm exercising, of course, associative memory as I speak.
But all these things require what is, a mathematician would describe as convergent flows.
Once I grasped that point, I had heard enough about the mathematics of spin systems as they
are related to magnetism and complex phenomena in magnetic materials. I'd been at Bell Labs
enough to be around when people were seriously talking about these subjects, and so I knew
something about the connection between spin systems and trajectories. I only had to say,
let's make the biological system look like a spin system, and then they should have the
same kind of mathematics. Associative memory is reciprocal. Seeing someone reminds you of
remembering their name, and hearing their name reminds you of what they look like.
That fact can be expressed in a network structure by making connections that are reciprocal.
The mathematics of such networks was closely related to the mathematics of spin systems as
seen in solids, and to things having to do with their phase transitions in magnetism.
Suddenly there was a connection between neurobiology on the one hand,
and the solid state physics I sort of knew on the other.
One way to achieve a convergent flow is for a state to be associated with an energy,
and have the allowed transitions, state to state to state,
to take, allow such transitions to take place only if the energy was decreasing. Like a ball
rolling downhill on a rough terrain, if you want to understand the trajectory of the ball,
you could follow the terrain and the ball in detail, or you can understand there's an energy,
if the whole thing is going downhill, and you go from near the top of the hill to near the bottom
of the hill. An energy function is what you really need to understand convergent flows
in a wide range of systems. With that connection made, three months later I was writing a paper.
Everything really came together when I see these two parts of science
are really being described for the same set of mathematics.
Then now the problem became writing a paper. I had three target reader audiences
for such research. Physicists, computer scientists, and neurobiologists.
Disparate set of people, but being a member of the National Academy of Science,
I could publish a paper in PNAS, Proceedings of the National Academy, without review.
But for PNAS, there was an absolute five paper limit on article length, including references,
and there were these three different audiences to address and much to say.
I had to write science in the style that Hemingway wrote non-fiction. In hindsight,
the omission of the almost obvious increased the impact of the paper. The unstated became an
invitation for others to add to the subject, and thus encouraged an expanding community
of contributors to work on such network models. This 1982 paper is the first publication in which
I use the word neuron. It was to provide an entryway to working in neuroscience for many
physicists and computer scientists. Further work connected these networks to many significant
applications far beyond associative memory, including the emergent field of artificial
neural networks. It also brought many statistical physicists into the field.
They created a foundation for subsequent development of the Boltzmann machine.
Continuous associative memory networks also served as inspiration for continuous recurrent
networks frequently used in many contemporary AI systems and in complicated computational
neuroscience. One issue with what is now called the Hopfield model network of associative memory
is that it has a small information storage capacity. Biological networks can store many
more memories than the number of sensory neurons and can dynamically adapt these memories if the
environment changes. I was jolted into thinking about this problem in 2015 when I was a visiting
professor at the Institute for Advanced Study in Princeton and was starting to interact with
Dmitry Kotov, a former high-energy theorist who was searching for an interesting problem to work
After several months of discussion, we formulated a simple mathematical model in which the memory
capacity becomes decoupled from the dimensionality of the space. This new model allows for a denser
packing of memories, and we called it the dense associative memory as a result.
Looking forward, we hope that the idea of useful computation by physical systems
will not only become helpful in hindsight for interpreting computational algorithms in existing
AI architectures, it may also inspire a new generation of collective physics-inspired
AI networks. What I have done in science rests on the experimental and theoretical studies
of experts. I have great respect for experts willing to interact with those outside their
disciplines, welcoming physics into new territory. Physics, at its best, is a point of view
for understanding the totality of man and his universe. Thank you.
