The Prepared Mind: What Disappears When Robots Run the Lab
Self-driving labs can pipette, run assays, and design experiments around the clock. So who is left to notice when something doesn't go to plan?
This is the second of a two-part series on AI, robotics, and the future of laboratory science. The companion piece asked whether robots can match the manual dexterity of working scientists. This one asks whether, even if they can, the science we get out the other end will still be science.
The Lab Tour Guide
In March 2025, Insilico Medicine, an AI drug discovery company with labs in Hong Kong, Boston, and Suzhou, unveiled what it called the first bipedal humanoid robot deployed in a drug discovery laboratory. The press release was heavy on vision: the machine, named “Supervisor,” would learn from human scientists, work “hand-in-hand” with researchers, and eventually perform tasks like pipetting and operating lab equipment. But the fine print told a smaller story. Supervisor assists with lab tours. It provides telepresence. It generates training data so that future AI systems might one day learn to do what scientists do. The first humanoid in a drug discovery lab is, for now, a tour guide.
But Supervisor symbolizes a real trajectory. AI systems will, within a decade, pipette, operate equipment, run assays. Whether they will succeed at the experiments is one question. Whether what they are doing will count as science is another.
A scientist trains in technique, theory, taste. The hardest skill to name sits underneath all of these: an openness to what you weren’t looking for. That, in a phrase, is serendipity. It is also a word that gets dismissed as luck, with luck taken to be too democratic an element to deserve credit for a great discovery. Scientists, the implicit argument runs, succeed by intellect, not by accident.
This reading of serendipity is lazy. The word was coined by Horace Walpole, 18th-century British politician and writer. In a letter to Horace Mann dated January 28, 1754, he described how he caught a connection between two Italian noble families while leafing through an old book of Venetian heraldry. He named the experience after a fairy tale, “The Three Princes of Serendip,” in which the princes “were always making discoveries, by accidents and sagacity, of things which they were not in quest of.” Walpole insisted on what the word did and did not mean. “You must observe,” he wrote, “that no discovery of a thing you are looking for comes under this description.” Serendipity, in its original sense, was not luck. It was the conjunction of accident and sagacity—the noticing—and it described, by definition, the case where what you found was not what you set out to find.
This is what happened in Stephen Kuffler’s lab at Johns Hopkins in the spring of 1958. David Hubel and Torsten Wiesel set out to record from individual neurons in the visual cortex of anesthetized cats. No one had ever seen what a single cortical cell did while the eye was looking at something. The technology barely existed. To get stable recordings from cortical neurons, Hubel had spent his previous posting at Walter Reed Army Institute of Research learning metallurgy from a department machinist and building his own tungsten microelectrodes.
The recording sessions were tedious, often running well into the morning. Hubel and Wiesel projected spots of light onto a screen and watched the audiomonitor for any cell that fired. For about a month, nothing did. They tried everything they could think of, including, at one point, slides clipped from magazine photographs of women, on the off chance some neuron in the cat’s visual cortex had a reason to care.
“Lawyers do not make serendipitous scientific discoveries. You have to be open enough to see that a mistake or a failure or something is actually more interesting than what you were looking for.” — Stuart Firestein
Then, partway through another uneventful session, the audiomonitor “went off like a machine gun,” as Hubel later described it in his 1981 Nobel lecture. He had been sliding a glass slide into the projector to swap stimuli. The cell was not responding to the spot they were trying to show the cat. It was responding to the faint shadow cast by the edge of the slide. Rotate the slide, and the firing dropped. The neuron, it turned out, was tuned not to spots but to oriented contours. It was the first evidence that the cortex was doing something with what the retina and thalamus sent it—that it was not just relaying signal but extracting structure.
Hubel and Wiesel are explicit about how to read this moment. In Brain and Visual Perception, the book about their twenty-five-year collaboration, they wrote1:
People hearing the story of how we stumbled on orientation selectivity might conclude that the discovery was a matter of luck. While never denying the importance of luck, we would rather say that it was more a matter of bullheaded persistence, a refusal to give up when we seemed to be getting nowhere. If something is there and you try hard enough and long enough you may find it; without that persistence, you certainly won’t. It would be more accurate to say that we would have been unlucky that day had we quit a few hours before we did.
Persistence deserves credit. Luck and serendipity are not quite the same thing—you can be unlucky, but you cannot really be unserendipitous; serendipity is, at most, a subset of luck. And in Walpole’s sense, this discovery was exactly the meeting of accident and sagacity: the accident of the slide casting a shadow, the sagacity to notice what the shadow was doing. (Your sleuthing correspondent wishes to report that the word “luck,” in one form or another, appears in Brain and Visual Perception thirty-four times. They truly did not deny its presence.)
Charles Gilbert, a neurobiologist at Rockefeller and a former student of Wiesel’s, put the point another way. Other labs in the late 1950s aimed more sophisticated instrumentation at the same problem. They did not find what Hubel and Wiesel found. “It wasn’t until David and Torsten were fiddling around with a much cruder basis of instrumentation,” Gilbert told The Scientist, “that they actually discovered this property of orientation selectivity.”
Hubel and Wiesel said something much the same about themselves. Looking back on the years of recordings in Brain and Visual Perception, they wrote:
We have generally used as wide a range of stimuli as we could dream up. We varied our stimuli as much as our imaginations would permit; indeed, our very sloppiness in devising stimuli must have added to the variety.
When Louis Pasteur said that chance favors the prepared mind, he did not mean that chance does the work. A mind that has spent years in close contact with its material is the only one that can recognize when the material is doing something strange. That takes preparation, but also openness: the willingness to see an anomaly as something worth following. Albert Szent-Györgyi, who won a Nobel Prize for isolating vitamin C, put the active half more sharply: the trick is to look at the same data everyone else has seen and see something different.
Stuart Firestein, a neuroscientist at Columbia and the author of three books on the scientific process, Ignorance, Failure, and the upcoming It Could Be Otherwise, put it more plainly. “Lawyers do not make serendipitous scientific discoveries,” he told me. “You have to be open enough to see that a mistake or a failure or something is actually more interesting than what you were looking for.” Serendipity, in other words, is not an event that happens to a scientist. It is a capacity that scientists develop, slowly, through years of proximity to their material.
You can’t optimize your way into new science
A new generation of laboratories is now being built to run themselves: AI-driven systems that design experiments, execute them, and decide what to do next, with no human at the bench. The metrics they optimize for are exactly the ones that, in 1958 in a basement at Hopkins, would have sanded out the shadow at the edge of the slide before anyone heard the audiomonitor go off.
Where these labs come from is half a century of work on the same problem. From Leonard Skeggs’s AutoAnalyzer in the 1950s through the high-throughput screening platforms of the 1990s, lab automation has been, in essence, the project of eliminating deviation. The point of an automated assay is that the next run looks exactly like the last one. Every shadow at the edge of every slide is the same shadow. Reproducibility and throughput are the twin virtues in this philosophy.
The current wave inherits this premise and presses it further. A-Lab at Berkeley runs robotic synthesis of new inorganic materials. Polybot at Argonne does the same for polymers. The University of Liverpool has built mobile chemist-robots that wheel between benches. The Acceleration Consortium has committed two hundred million Canadian dollars to scaling these systems. Private capital has done more: Lila Sciences raised five hundred and fifty million dollars to industrialize the approach, Radical AI fifty-five million, FutureHouse and Emerald Cloud Lab carve up the rest of the field. The shared promise, sometimes called “Level 3” autonomy in this literature, is the laboratory that runs itself.
These systems are likely to improve science by increasing throughput. The search space of interesting molecules, for instance, will widen, with meaningful consequences for drug development. But it’s hard to imagine them producing paradigm-shifting science.
The lab-automation story has, at this point, run into a result Kenneth Stanley and Joel Lehman call the deception of objectives. In their book Why Greatness Cannot Be Planned, the two AI researchers show that algorithms set to optimize for a target often fail to reach it, while those set to search for novelty solve the same problems reliably. “When objectives are ambitious,” they write, “the only reward you’re likely to receive is deception.” The metric points in one direction; the path to the answer goes in another. To optimize for the metric is to walk away from the answer.
Hubel and Wiesel started with a reasonable hypothesis. Their mentor Kuffler had shown that retinal ganglion cells and thalamic neurons fired in response to small spots of light; the natural assumption was that cortical cells would do the same. They didn’t. For many labs at the time, this would have been the end of the road—a disappointing negative result on a clean hypothesis. For Hubel and Wiesel, free-ranging experimentation turned the dead end into the doorway.
The pipetting isn’t where the discovery is. The trouble is that the pipetting is where the discoverer comes from.
One could argue that automation would have found orientation selectivity eventually. Set the objective to maximizing the firing rate of individual V1 neurons, give the system a way to search the stimulus space, and the oriented edge is sure to emerge. The technology to do this arrived sixty years after Hubel and Wiesel fumbled with the slide projector. And even then, the approach misses something important about how the cortex actually works: the modern view is that what matters is the joint activity of neuronal populations, not the maximal firing of any one cell.
There is an old Russian children’s story of a boy named Deniska who receives a mediocre grade in singing despite singing with tremendous force—so loudly, he believes, that he could be heard from across the street. When his teacher tells him he’ll never achieve the fame of the great tenor Ivan Kozlovsky, Deniska’s only thought is: how could Kozlovsky possibly sing louder than that?
A laboratory designed to eliminate violations of its protocol is, by construction, a laboratory designed not to find what Hubel and Wiesel found. But the problem isn’t only about what the machine notices. It’s about who is there to notice—and what they had to do, for years, to be the kind of person who could.
The Drudgery Is Where the Discoverer Comes From
“Some of my best ideas came while I was mindlessly pipetting stuff from one place to another,” Firestein told me. “Somehow or another, it lets your mind wander. Whereas if you’re letting some robot do it and you’re sitting in a room trying to have good ideas, that never seems to happen, at least to me.”
One promise of automation is that it will free scientists from the parts of the job that aren’t really science—the pipetting, the buffer-making, the late-night data wrangling—and let them spend their time on the parts that are. The intellectual stuff. The argument is hard to argue with: the pipetting isn’t where the discovery is. The trouble is that the pipetting is where the discoverer comes from.
There are people in a lab, Firestein told me, who have what he and other PIs call “good hands.” “When they do the experiment, it works, and when somebody else does it, it doesn’t work as well. And none of us know what that is. It’s tacit knowledge. And a great deal of what we do is this sort of tacit knowledge.”
Tacit knowledge is the term Michael Polanyi used for the kind of expertise you can demonstrate but cannot fully describe. The phrase has been picked up across the philosophy and history of science to name what separates a scientist who can get an experiment to work from one who can’t, even when both are following the same protocol. It is the part of laboratory craft that doesn’t make it into the methods section. It is also, by definition, the part of the work that you cannot acquire by reading.
Firestein bristles at the language we use to describe how scientists are trained. “I know they call this graduate school,” he told me, “but it’s not. It’s got nothing to do with school whatsoever. This is a job. The work you do here is real stuff.” Graduate students aren’t just learning techniques; they are producing knowledge that will enter the scientific record. And they are learning how to notice when the neat experiments they came up with on paper refuse to behave on the bench.
That kind of noticing does not come from lectures or manuals. Firestein calls graduate training what it really is: an apprenticeship. “That’s where the tacit knowledge comes from,” he said.
Grace Chahyadinata, a third-year graduate student in a Harvard neuroscience lab who performs delicate brain surgeries on mice, is living through this apprenticeship right now. The technique she relies on for finding her targets in the brain—she calls it going “based on vibes”—is exactly the kind of knowledge Firestein describes: hard-won, hard to articulate, hard to teach.
“The PhD is more about character building than learning the technical stuff,” she told me. “You learn persistence, you learn how to deal with emotional ups and downs, and how to find yourself in the process.” Alongside the manual labor of doing science is a parallel cognitive labor: building intuition, learning when to trust an implicit decision over an explicit one. Every graduate student learns these things, but they are hard to teach explicitly. You learn on the job.
Firestein’s most counterintuitive claim is that waste and failure are not bugs in the system but features of it. “Nobody wastes money like a graduate student,” he said, laughing. “They just blow money on everything, and it’s getting more and more expensive. But it’s important for them to fail at some of these things they do.” Most experiments do not work. Many ideas go nowhere. And yet, almost without exception, the insight that makes a dissertation cohere arrives near the end.
“Almost everything that makes the thesis happens in the last eighteen months. Always,” Firestein told me. It’s what happened to me and to virtually everyone in my graduate program. “But I don’t know how to get to that last eighteen months without the first four years.”
Automation promises to compress this timeline—to reduce waste, minimize failure, and route around years of seemingly unproductive labor. But in doing so, it risks removing the conditions that make discovery possible.
The optimistic version of automation cannot tell the difference between the four years and the eighteen months. It looks at the early years and sees inefficiency — pipetting, buffer-making, runs that fail for reasons no one can name. It is right that all of this is wasteful in a narrow accounting sense. It is wrong about what the waste is producing. The waste is producing the noticer.
A self-driving lab is, by construction, a laboratory in which no one is doing the first four years. There is no apprentice at the bench. There is no mind wandering between samples. There is, in the long run, no scientist to be the prepared mind that the next slide-edge shadow needs.
Serendipity is not locally efficient: it emerges from prolonged exposure to things that mostly do not work.
Serendipity, in this reading, is not preserved by carving out time for the scientist to think. It is produced by years of physical contact with material-years in which the scientist becomes the kind of mind that can be surprised in the right way. Cut the contact and you do not get a scientist who is freer to think. You get a scientist who has nothing to think with.
The Bullshit Detector
The capacity Firestein describes—the trained nose for when something in the lab is wrong—has a twin. The skill that lets a scientist notice that something is interesting is the same skill that lets her notice when something is wrong. Both have always mattered. As AI moves further into science, the second one matters more.
Marc Aidinoff, a historian of science and former White House science policy adviser, told me: “Half of being an academic is developing a good detector for when something is off—whether it comes out of a machine or a professor. That nose takes many years to develop.”
What worries Aidinoff most about AI-mediated science is not that the machines will make mistakes but that the humans on the other end will lose the eye for catching them. “It’s not the single greatest risk of AI,” he said, “but it’s up there: if our scientists don’t have good taste.”
This is the same point Firestein was making about apprenticeship, but Aidinoff carries it one step further—into the political economy of who pays for the apprentices. When I pushed him on what is genuinely new about this moment, his sharpest claim was structural: “AI for science is being constructed in a way that assumes science does not need a university system to thrive.” Read alongside the funding numbers—federal research dollars contracting, hundreds of millions in private capital flowing to autonomous-lab startups—the claim begins to look less like a worry and more like a forecast.
The labor those startups are automating, Aidinoff pointed out, is graduate-student labor. The problem-solving, the digging through old scanned PDFs for esoteric protocols, the late nights in dark microscope rooms—this is the work the self-driving labs are designed to absorb. “If this keeps going,” he said, “they’re not going to have any more former grad students to hire.” A startup that automates the bench can run for a long time on the senior scientists it inherited from the academy. It cannot, on its own, produce the next cohort. It will, in the long run, have to hire from somewhere—and that somewhere is the system it is hollowing out.
“AI for science is being constructed in a way that assumes science does not need a university system to thrive.” — Marc Aidinoff
“We need junior people to have senior people,” Aidinoff said. “If we don’t have those training pipelines, that really worries me—that we’ll have hollow institutions.”
There is an obvious counter-reading here, and it deserves a hearing. Science has always renewed itself by absorbing new tools, and tools have always reshaped what it meant to be trained. The PC arrived; molecular biology absorbed it. Cryo-EM arrived; structural biology absorbed it. AlphaFold arrived, and overnight a thesis project that used to win Nobel Prizes became a Tuesday afternoon. Firestein himself, who is not nostalgic about any of this, told me his own thesis from the 1980s could now be done in a few days with modern optical imaging. The university system has been here before, and it has, more or less, adapted.
The question is whether the funding will allow it to adapt this time. AI gives funding agencies a tempting story: efficiency, fewer apprentices, lower costs. That story is wrong. If anything, this is the moment to double down. If the political economy continues to treat universities as dispensable, the institutions that produce noticers will hollow out—and there will be no one left to catch what the machines get wrong.
The bullshit detector that young scientists hone during their training is not a credential. It’s what catches the machine when it produces a confidently wrong answer-and over the next decade the machine will produce plenty of those. Today these bullshit detectors are people, trained slowly, by other people who were also trained slowly.
I have no doubt that we’ll find a way to engineer AI bullshit detectors. The fuzzier and equally important question is whether our institutions will still produce human scientists with the taste to know what to look for—and the room, in their work, for serendipitous discoveries.
Calibrating Surprise
It would be a mistake to read all of this as an argument against automation. Computers, Aidinoff pointed out, are not sterile or boringly predictable. “Computers — whether it’s AI systems or automation — never behave exactly as they’re expected to,” he told me. “They’re surprise-generating machines.” Used well, new tools introduce forms of randomness no one has seen before.
The challenge is calibration. “The question is: how do you calibrate the right level of things not behaving as expected, so you get innovation and don’t get stuck in a rut?” Too little surprise and the system is a treadmill. Too much and it is noise. Somewhere in between is a system that can produce the kind of deviation that might lead to interesting results.
Calibration is itself a craft, and Aidinoff’s prescription for it is unfashionable. “You really have to play,” he said. “You have to let yourself be at a point where you don’t know what the tool is going to do in order to come close to understanding it.” Play is the opposite of optimization. It is the stance Hubel and Wiesel were in when they were sliding magazine clippings into a projector at three in the morning. It is also the stance that is hardest to reproduce inside a system built on the premise that it will never behave unexpectedly.
Designing automated labs that allow for play and serendipitous discovery will require more than maximizing throughput or minimizing error. An automated system that hopes to contribute to discovery must learn when not to optimize: when to flag the odd result instead of discarding it, when to preserve context rather than just outputs, and when to defer judgment to a human with a well-formed bullshit detector.
Michelle Lee, the CEO of Medra AI—a Bay Area startup building robots for flexible laboratory work—has seen what happens when the detector is missing. Traditional automation, she told me, doesn’t just cause spectacular failures—”stuff everywhere” when you come back to the lab. It causes silent failures too. “You run something, you come back when it’s supposed to be done, and you don’t even know something went wrong,” she said. “You look at the plate reader and your negative control has stuff growing in it.” A good human scientist would notice. An automated system optimizing for throughput, by construction, would not.
Serendipity has been accused of being a fuzzy concept, but the only fuzziness is in the eyes of those who need new spectacles. Some researchers and engineers are tackling it head-on. A recent paper introduced “SciLink,” a multi-agent AI framework designed to “operationalize serendipity” in materials research. The system creates automated links between experimental observations, novelty assessments, and follow-up simulations—an attempt to ensure that unexpected findings don’t vanish into the noise. Others have proposed “Serendipity Engineering” as a discipline in its own right, with four core principles: expand the observable space, retain anomalies in metadata-rich archives, surface rare patterns, and foster openness to the unexpected. These are all antennae today’s AI can be fitted with, if we reward it for picking up faint signals. Kenneth Stanley, who showed that optimizing for an objective often walks you away from it, now leads work on open-endedness at Lila Sciences.
Ken Goldberg, a professor of robotics at UC Berkeley, framed the same problem in pragmatic terms. “Good scientists cultivate the ability to understand what’s out there,” he told me, “and to know instinctively when something is new and interesting or counterintuitive. That’s what serendipity starts with.” There is no reason, he added, to believe that surprise itself is beyond the reach of machines. “If you ask ChatGPT, ‘what surprises you about this?’ it can actually answer that. And that’s actually interesting.” The capacity for surprise, he suggested, is not absent from AI; someone has to think to ask. And generating more experiments—expanding the volume of activity—increases the opportunities for unexpected results.
But abundance alone is not enough. There are always more ideas than there is time to pursue them, more anomalies than can be followed up. “We’re all looking for serendipity,” Goldberg said. “There are so many ideas out there—and only so many hours in the day. My students are working hard because we’re looking for serendipity too.”
The Division of Labor
There is a more optimistic version of this story, and it deserves a hearing. Grace Chahyadinata, the graduate student doing brain surgeries on mice, said something that pulls in the other direction. “I feel like I don’t have enough time to think,” she said. “I wish I just had even a week where I’m not doing anything and just reading or thinking.” The physical labor of graduate school can crowd out the cognitive space that serendipity requires. The repetition that develops tacit knowledge can also become a grind that leaves little room for reflection. Perhaps, as machines take over the drudgery, human scientists will have the time to think.
Michelle Lee imagines a future where scientists work alongside robots the way they now work alongside research assistants: teaching them protocols, correcting their mistakes, gradually trusting them with more. In this world, a graduate student learning how to do science would be free to read and think while the robot, having anesthetized and ear-barred the mouse, deftly hits the tiny target in the brain.
It is a beautiful image. It is also the image that Firestein’s whole argument was a warning against. If the drudgery is where the noticing comes from—if the vibes are learned through ten thousand repetitions—then handing the repetitions to a machine is not just a labor-saving move. It is a change in what kind of mind walks out of the lab at the end of five years. The graduate student who reads and thinks while the robot does the surgery is not a more enlightened version of the graduate student who did the surgery herself. She is a different scientist.
“I don’t think AI will do philosophy of science,” Firestein told me. “If AI is doing all the technical stuff and maybe even the physical labor of science, then maybe we’d be left doing philosophy of science and saying here’s why you should do this experiment. Which would not be the worst outcome I can imagine.” That is probably the best case. But the best case depends on something I’m not sure is true: that the philosophy of science is separable from the doing of it. Future generations will still be scientists. Their way of thinking will be different.
Torsten Wiesel, in an interview with The Scientist given at the age of one hundred, reflected on his career not in terms of hypotheses or discoveries but in terms of the posture that produced them. “It was like exploring nature,” he said. “You have to try different ways and it’s not that you know what you will find. It’s that you have to be humble. You have to listen to nature and see what you find.”
The hands may become robotic. The listening and seeing, for now, remain ours.
I wrote about Hubel and Wiesel’s discovery through this lens in a 2015 blog post. The accounts by Phil Jaekl in Nautilus and The Scientist are worth a read.