Follow curiosity, switch fields: how physicists say discoveries happen

The Short Version

Three physicists describe discovery as something that happens while moving, not while executing a plan. Bernardo Huberman changed fields again and again, looking for beaches "with very few footprints" [1]. Neil Gershenfeld says nearly everything he worked on failed and that the failures produced the breakthroughs, a pattern he calls ready, fire, aim [2]. Andrew Strominger says what counts is the number of things you get right, not how often you are wrong, and that the places where theories break down are where the work is [3]. None of them recommends aimlessness, though: each pairs the play with serious preparation, and Strominger has spent a career on one stubborn paradox instead of leaving it [1][2][3].

Table of contents

What They Said

Bernardo Huberman: leave when the beach gets crowded

Huberman is a research physicist who worked at Xerox PARC, led the Social Computing Lab at Hewlett-Packard, and now works on quantum networks at CableLabs [1]. His career is a sequence of moves. His first paper was on tachyons, hypothetical faster-than-light particles [1]. He became one of the early researchers on chaos, and with a student showed that quantum systems are not chaotic in the classical sense [1]. Then he moved into computer science [1].

That move came from a book and a reversal. One sleepless night in Copenhagen he read John von Neumann's short book The Computer and the Brain and decided to flip his approach: instead of using computers for physics, use physics to study computers [1]. With students interested in economics he developed what he called the ecology of computation, treating networked computers as a market [1]. Later he worked on social networks and the economics of attention, studying the behavior of tens of thousands of people online [1]. Today his lab sends quantum signals over about 100 kilometers of fiber, against critics who said it only worked over 10 to 20, and he is researching how several large language models can collaborate on a problem [1].

He gives two reasons for moving. The first is pleasure: like falling in love, the start of a new field is thrilling [1]. The second is odds. His philosophy is walking on beaches with very few footprints, because when a field becomes crowded, the odds of doing something interesting shrink [1]. He has a temperamental dislike of crowds in general; he never cared for what he calls "mob behavior" [1].

He is frank about the price. A Berkeley colleague once told him he was up for the National Academy of Sciences but needed to publish more physics papers; he refused and never became a member, though he says he would not have minded prizes [1]. He never had true mentors, and his son Andrew describes him as "orphaned in science" [1]. Crossing into a field also means facing its gatekeepers: at an early chaos talk at Berkeley, a famous mathematician called his unproven claim "a lie" [1]. He recalls being laughed at by AI researchers decades ago for playing with neural networks [1].

Two more habits support the wandering. He treats famous scientists as brilliant but fallible; he once posed a problem to Richard Feynman, who guessed wrong and joked that he had not been thinking in color [1]. And he places value in the pursuit, not the achievement. After his son's first first-author paper in Science, he warned that he would soon worry he would never do it again, and advised him to return to what inspired him and pick a new problem [1].

Neil Gershenfeld: ready, fire, aim

Gershenfeld directs MIT's Center for Bits and Atoms [2]. He states his record flatly: "essentially, everything I've ever worked on has failed" [2]. He adds at once that in failing, something better happened [2].

His name for the method reverses a familiar order. In ready, aim, fire you do your homework, aim carefully at a target, and if everything goes right you hit it [2]. In his version you do a lot of work to get ready, try something without over-planning, and then look very carefully at where you actually hit: "You aim after you fire" [2]. His reason is a ceiling. If you aim first, he says, "the best you can hope is hit what you aim at" [2].

He gives two detailed cases. He was doing short-term work on low-cost shoplifting tags, studying how to sense several objects at once, which required a source of non-linearity and led him to look at how nuclear spins interact [2]. The approach failed for tags but could compute; with Isaac Chuang and others this led to early quantum computations running Grover's search algorithm and later Shor's factoring algorithm, whose control techniques live on in today's quantum computers [2].

The second case is bubbles. He and student Manu Prakash proposed to build a fluidic ribosome, and in his words "the project crashed and burned. It was a disaster" [2]. Bubbles kept ruining the experiments until Prakash suggested using them [2]. Bubbles in tiny channels can switch fluid flow, store a bit and perform logic when two collide, which is everything needed for a universal computer [2]. The same failure led to a 50-cent microscope and techniques used to transplant genomes for synthetic life [2].

A third example shows the same drift over a longer path. A problem sensing a cellist's bow with electric fields, where the player's hand interfered, led to a student's thesis on 3D imaging with electric fields, then a magic trick in Las Vegas, and finally a car seat sensor that could tell an adult from a bag of groceries from a baby, after airbags were killing infants in rear-facing seats [2]. It became a $100 million-a-year business [2].

From this he draws a criticism of how research is organized. He faults Vannevar Bush's postwar report, which framed research as a pipeline from basic science to application; in his lab it usually runs backward, with applications leading to basic science [2]. Research funding and management, with milestones and deliverables, "doesn't anticipate this" [2]. He is equally critical of the startup slogan: "fail fast tends to miss ready and aim" [2].

His own path crossed boundaries from the start. He wanted to attend vocational school to learn welding and was told he was too smart; at Cornell he would cross the street from the physics department to the music department, where he played the bassoon [2]. What drew him to MIT was a "department of none of the above" inside the Media Lab [2].

Andrew Strominger: be wrong, follow the contradiction

Strominger, a theoretical physicist at Harvard, supplies the attitude toward error that the other two practice [3]. On Einstein, who doubted black holes and gravitational waves, he says: "It's not how many things you got wrong. It's not the ratio of how many you got wrong, how many you got right. It's the number that you got right" [3]. Of himself he says, "people are always sort of disagreeing with me. And they're usually right, but I'm right enough" [3].

His guide to where to work is breakdown. "My view is that there's no exact equation. Everything is an approximation," he says, and a singularity is a good thing because it shows where a theory needs improvement [3]. "Edges are wonderful because that keeps us in business" [3]. He traces general relativity to a contradiction that can be stated as an imagined experiment: nothing outruns light in Maxwell's theory, yet in Newton's gravity you could signal another galaxy instantly by moving a coffee cup [3]. He cautions that not every contradiction is deep; many are just mistakes [3].

He treats theories as provisional tools. Asked whether string theory is dead, he calls the framing a logical error: "What it is is a stepping stone" [3]. His comparison is Yang-Mills theory, invented to describe protons and neutrons, wrong for that, and then found to describe nearly everything else in the standard model [3]. He says of string theory describing our world, "I don't even believe it myself" without an experiment [3].

He did not arrive by plan. He jokes, "I wanted to reach Nirvana and I realized that wasn't going to happen," then wanted the meaning of life, then justice and socialism, and settled on the biggest problem with some prospect of progress [3]. He began as a reluctant string theorist, reading the papers out of duty, and says, "I grew to love it" [3].

And he keeps the option to move. Physicists should explore every route; he takes the one his nose tells him is best, and if someone on another route finds something promising, "I'm going to make a portage over the mountain and get on their stream" [3]. Not seeing the experiment yet is no reason to stop: "the fact that we can't see to the end isn't a reason not to do it" [3]. If the path were already clear, he says, it would be boring; Magellan had no map [3].

A note on the framing of this article: the summary of Strominger's conversation carries a heading about thought experiments, but its content is mostly about contradictions, approximation and being wrong, so that is what is reported here [3].

Where They Agree, and Where They Don't

Error is expected. Gershenfeld's projects fail into something better [2]. Strominger counts successes and ignores the ratio [3]. Huberman tells of Feynman guessing wrong and says he prefers humor and self-deprecation to taking oneself very seriously [1].

The map comes afterward. Gershenfeld aims after firing [2]. Strominger says that once he and his collaborators solve a problem, they cannot reconstruct how confused they were two weeks earlier [3]. Huberman's best-known turn came from one night's reading [1].

Institutions reward the opposite. Huberman lost an academy membership for publishing outside physics [1]. Gershenfeld says milestones and deliverables cannot foresee productive failure, and that junior faculty who try to game tenure are miserable and do not get it, while those who love their work do [2]. Strominger worked on quantum gravity when it was not considered interesting [3].

Love of the work is the engine. Huberman said he felt, when an idea finally worked out, like a child the night before a birthday [1]. Gershenfeld says, "You have to love what you're doing and believe in it" [2]. Strominger says he is as excited about current work as ever [3].

Where they differ: leave or stay. Huberman leaves a field when it fills up [1]. Strominger has stayed with what he calls the most fundamental paradox in physics, the clash between quantum mechanics and gravity, and was ready to spend his life in the wilderness on it [3]. Gershenfeld is somewhere between: his subjects range from cellos to quantum computing, yet he says of his work, "it's really just the same idea over and over again," how bits and atoms relate [2]. So movement means changing fields for one, changing targets for another, and changing routes toward a fixed question for the third.

Where they differ: how much to plan. Gershenfeld deliberately does not think too hard about the target [2]. Strominger chooses problems with great care, looking for the rare one that is neither solvable-but-dull nor fascinating-but-hopeless, which he calls a "knife edge" [3]. Huberman, for all his restlessness, tells admirers of dropout founders to calculate the odds and build a strong foundation, because we only hear the success stories [1].

Where they differ: crowds. Huberman avoids them [1]. Strominger wants every person taking every route and is glad to join another stream if it looks better [3].

Why It Works

Aiming caps the result. Gershenfeld's argument is that a carefully aimed project can at best deliver what was imagined in advance, while looking at where an attempt actually landed can reveal something nobody proposed [2]. The tags that computed and the bubbles that did logic are his evidence [2].

Uncrowded fields have better odds. Huberman's reasoning is that the chance of doing something interesting shrinks as a field fills [1].

Tools travel. Huberman carried physics into computing and economics [1]. Gershenfeld carried electric-field sensing from a cello to a car seat [2]. Strominger notes that one assumption, that the world is made of strings, solved two separate problems, and that Yang-Mills theory found its real use far from where it was aimed [3].

Breakdowns point the way. For Strominger a theory that predicts its own failure tells you where to dig, and a contradiction between two good theories is a lead [3].

Fresh eyes ask new questions. Asked what theory could learn from the first black hole image, Strominger and colleagues treated the black hole as a mirror and found a question that, he says, had never been asked quite that way despite volumes of research [3]. Gershenfeld's rare valuable student is the one in a hundred who arrives saying, "you're wrong. Here's your mistake" [2].

Pursuit sustains itself. Huberman's advice to pick a new problem after a success is offered as protection against the letdown that follows achievement [1].

The evidence in all three cases is the speaker's own career, told afterward. Huberman himself warns about survivor bias in success stories, and that warning applies to stories of lucky failures too [1].

Where It Applies, and Where It Doesn't

The pattern fits research with slack in it. Gershenfeld's lab runs without formal proposals or charges for machine time [2]. Huberman worked at industrial labs and says he never worked for money [1]. Strominger is a theorist who was prepared to go a lifetime without a solution [3].

It fits poorly where a specific result must be delivered, which is exactly the setting Gershenfeld says milestones are built for [2]. It also carries career risk that not everyone can absorb: Huberman paid in recognition, and he recalls going without dinner as a broke graduate student [1].

It does not excuse skipping preparation. Gershenfeld's first word is ready, and he says both failed projects required a lot of homework before the attempt [2]. Huberman credits a demanding humanistic education with helping him think in broad contexts [1].

It does not mean every problem is worth wandering into. Strominger says that early in his career he erred toward unsolvable problems, and that timing matters [3].

And switching fields is not always wise. Huberman is skeptical of physicists wandering into neuroscience [1]. Strominger has not been able to say when, or whether, his main bet will be tested [3].

What To Do With It

1. Do the homework first. Gershenfeld's method starts with a lot of work to get ready, and Huberman advises a strong foundation [1][2].
2. Try the thing without over-planning, then study carefully where you actually landed, including what went wrong [2].
3. When an obstacle keeps ruining the experiment, ask whether it is the result, as with the bubbles [2].
4. Reverse a relationship you take for granted. Huberman's turn came from using physics to study computers instead of the other way round [1].
5. Notice when a field has become crowded and consider moving where there are few footprints [1].
6. Look for contradictions and for places where an accepted theory breaks down, and check first that the contradiction is not just a mistake [3].
7. Choose problems on Strominger's knife edge: interesting and with some prospect of progress [3].
8. Count what you got right, expect to be wrong often, and say so openly [3].
9. Be willing to carry your canoe to a better stream when someone else's route looks more promising [3].
10. After a success, go back to what inspired you and pick a new problem [1].

Sources

1. Dr. Bernardo Huberman on Curiosity, Physics, Chaos, Quantum Networks and a Joyful Life · Huberman Lab
2. Neil Gershenfeld on Self-Replicating Robots, Fab Labs and the Future of Digital Fabrication · Lex Fridman Podcast
3. Andrew Strominger on Black Holes, String Theory, the Holographic Principle, and Soft Hair · Lex Fridman Podcast