Open almost any surgical journal this year and you’ll find a new AI model. A neural network that predicts anastomotic leak. A risk calculator trained on a single institution’s registry. A computer-vision system that labels the phases of a laparoscopic cholecystectomy. A bespoke tool for predicting graft patency, rupture risk, or readmission. Each is presented as a small, hard-won victory where domain experts encode clinical knowledge into a tightly scoped algorithm that does one surgical thing well.
There is a pattern in the history of artificial intelligence that should make us cautious about every one of these. It has played out in chess, in Go, in vision, in speech, and is now playing out in ML approaches to medicine and surgery. The pattern has a name, and it is worth understanding before we invest another decade of surgical research effort building things the history teaches us will not last. Surgery, and medicine, are learning the Bitter Lesson.
The Bitter Lesson
In 2019, Richard Sutton, the godfather of reinforcement learning, wrote a short essay called “The Bitter Lesson” (it’s short, go read it). Its point is simple. He explains that across seventy years of AI research, the approaches that ultimately win are not the ones where humans carefully encode their domain knowledge into the system. Despite what our egos would rather us believe, the approaches that do win are general-purpose methods that scale with computation, specifically learning and search, given enough data and enough compute.
The lesson is “bitter” because researchers find it genuinely unpleasant and must keep being forced to relearn it as AI expands from domain to domain. Researchers would rather their idea be the secret sauce that unlocks the next jump in model performance. Instead the solution has been to just use more computers and build a bigger general model. We are domain experts. We want our hard-earned knowledge of anatomy, of disease, of operative judgment to be the thing that makes a system intelligent. As humans, we want to wrap the computational layer in our intuition or knowledge. Sutton’s point is that, over and over again, the human-knowledge approach produces a satisfying short-term gain and is then overtaken decisively by a more general method riding a larger wave of computation. Now, it’s our field’s turn to learn this lesson.
Real physician voices, twice a week
Free, and one click to unsubscribe.
The classic example is chess. For decades, the assumption was that a great chess engine had to encode the heuristics of human grandmasters. The engines that eventually dominated did the opposite. They instead leaned on massive search. Deep Blue beat Kasparov in 1997 not by thinking like a human but by evaluating enormous numbers of positions. The handcrafted-knowledge engines lost.
Go was supposed to be different, but it would also eventually be forced to learn the Bitter Lesson. The board is too large, the positions too intuitive, the game too “human” for brute computation. Then in 2016 AlphaGo defeated Lee Sedol (as an aside, definitely check out the documentary if you haven’t). The decisive blow came a year later. AlphaGo Zero learned the game from nothing but the rules and self-play, with no human games at all, and surpassed every prior version. AlphaZero then generalized the same approach to chess and shogi and, in a matter of hours of self-play, exceeded the strongest specialized chess engine that humans had spent decades tuning. The specialist did not just lose. The specialist was rendered obsolete by a more general system that had been pointed at the problem with more compute.
The same story repeated quietly in computer vision and speech recognition, where hand-engineered features, the carefully designed edge detectors and phoneme models that represented the field’s accumulated expertise, were swept aside once large models could simply learn the features themselves from data. The 2012 ImageNet result (AlexNet) was the moment that became undeniable, and the field never went back.
Sutton’s conclusion: Build systems that get better as you add computation, not systems that get better as you add your own cleverness. In the long run, general and scalable beats specialized and clever.
Attention, and the architecture that made generality win
If the Bitter Lesson explains why the general approach wins, a single 2017 paper explains how the current era became possible. Vaswani and colleagues published “Attention Is All You Need,” introducing the Transformer architecture (if you’re interested in AI architecture and only want to read one paper, this is the one). It discarded the recurrent and convolutional machinery that everyone assumed was necessary for sequence modeling and replaced it with a mechanism, called self-attention, that is almost embarrassingly general. It does not know anything about language, or proteins, or images, or clinical notes. It learns relationships between elements of a sequence, whatever that sequence happens to be.
The Transformer is a platform that improves predictably as you scale it. The papers that followed quantified exactly how predictably: the scaling-law work showed that model performance improves as a smooth power law in compute, data, and parameters. Performance became something you could buy rather than intuit. And when GPT-3 demonstrated that a sufficiently large general model could perform tasks it was never explicitly trained for, simply from a prompt, the path was reinforced. Subsequent work on alignment, training models to follow instructions and human preferences, turned raw capability into something usable at the bedside.
For a surgeon, the relevant translation of all this is that the engine of progress is no longer a specific clever algorithm for a specific clinical problem. It is a general architecture that absorbs more capability every time the underlying model is scaled and retrained. Anything you build narrowly today is competing against a general system that gets better on a schedule you do not control.
June 2026: The Bitter Lesson arrives for medicine
This is the context in which the recent Nature Medicine paper should be read, and why, despite all the drama on LinkedIn, no one should have been surprised by it.
Vishwanath, Oermann, and colleagues performed a blinded comparison of specialized clinical AI tools against general frontier models. They pitted two widely adopted clinical products built on top of LLMs (OpenEvidence and UpToDate Expert AI) against three frontier general models (GPT-5.2, Gemini 3.1 Pro, Claude Opus 4.6). They tested medical knowledge (500 MedQA questions), alignment with expert clinicians (500 HealthBench items), and, most importantly, 100 real clinical queries pulled from physicians during live care, each rated by blinded clinicians.
The frontier general models won on all three. The specialized clinical tools formed a distinctly lower performance tier. And the detail that should stop every surgeon-scientist cold: On the real-clinical-query benchmark, those purpose-built medical tools performed no better than Google’s auto-enabled search AI Overview. The dedicated clinical product, with its domain framing and curated medical content, was statistically indistinguishable from the thing that pops up above your search results.
The online reaction treated this as a shock. This should not have been surprising, other than perhaps the alleged non-disclosure of conflicts of interest and API access restrictions, and some important technical comments on benchmark engineering which will be sorted out in other places. Instead, we should recognize this for what it is: the Bitter Lesson arriving in our domain. The general system, riding a larger wave of compute, data, and alignment, overtook the specialized system that had encoded medical knowledge by hand. Chess, Go, vision, speech, and now medicine.
To their credit, the authors are careful, and so should we be. They note that this is a snapshot of a fast-moving field, not a permanent ranking. If the returns to scaling eventually flatten (while beyond the scope of the article, some experts do suggest the scaling era is ending and we may go back into a research era, but what most people mean by research here is deep ML research, not domain-specific ML optimization research) and that deeply subspecialized tasks may still reward sophisticated, dedicated adaptation. Those are real caveats. But they are caveats about timing and edge cases, not about the overall direction of the arrow.
The harness question and why “building on top” is not a moat
The other position we see online is individuals and companies touting that their small surgical model, or their clinical tool, is safe from the Bitter Lesson because it is built on top of a large LLM. Here, the base model provides general intelligence, and the team adds a harness over a curated knowledge base, helping guide prompt engineering, adding guardrails, orchestrating workflow integration, or filtering for domain-specific needs. The claim is that this harness is the durable contribution, immune to the rising tide because it sits above it.
I am not saying that the harness or control layer don’t matter. That is not in dispute, because engineering scaffolding well is real work, and in the short term it produces a better product. But a harness is not a moat. The reason is structural, and it is worth stating plainly. Whatever knowledge lives in your harness today, the next version of the base model tends to absorb. The retrieval layer that gave you an edge, feeding the model the right guideline, the right dosing table, the right operative caveat, is compensating for a gap in the base model that the base model’s makers are actively closing with every training run. When the base model improves, two things happen at once: the marginal value your harness adds shrinks, and your harness itself often needs to be rebuilt and re-tuned to keep working against the new model. You are running on a treadmill whose speed is set by someone with vastly more compute than you. The harness can even degrade performance by pulling in irrelevant material that can worsen a strong base model’s answer rather than improve it.
There is probably one important exception, and naming it sharpens the argument rather than weakening it. The harness that includes private, proprietary, or real-time information, which for now at least the frontier model cannot absorb, is the main exception. A surgical model whose only advantage is that someone organized the literature well is living on borrowed time. A system whose advantage is privileged access to data the giant model will never see has an actual claim to permanence.
What a surgeon should actually do with this
None of this means AI is a distraction from surgical care, and none of it means our clinical expertise is worthless. It means our expertise is best spent on the parts of the problem that scale will not solve for us.
First, as we tell the intern, read more. Become the most AI-enabled version of yourself. Go read “The Bitter Lesson.” If you are still looking to understand more about how AI works without getting too into the math, watch the 3Blue1Brown video on how neural networks actually work, then, if you liked that, the one on the Transformer architecture. Next, read the scaling law papers or read summaries of them. If still looking for more, then listen to Andrej Karpathy’s “Software is Changing (Again)”. Finally, listen to the Dwarkesh podcast with Richard Sutton on the way home from work and appreciate carefully what he is saying: experience and human knowledge always get their lunch eaten by the methods that are truly scalable. He doesn’t believe that LLMs will get us to AGI, but that’s beside the point.
Second, be skeptical of the small specialty model presented at your next conference. Ask the authors the Bitter Lesson question directly. Ask, when the next frontier model arrives, what about this is still valuable? If the honest answer is “The model just knows this now,” you are looking at a result with a short half-life.
Next, treat curated-knowledge tools as conveniences, and demand independent, real-world evaluation before any of them touches patient care. The most striking lesson of the Nature Medicine work is not which model won, it is how little independent evidence existed before tools were adopted at scale, and let’s be honest here, every intern is already using OpenEvidence to correct your patient’s potassium or choose their anticoagulant regardless of what the result is here.
Finally, invest your scarce research effort where it compounds rather than where it erodes. The defensible work is in problems the frontier model structurally cannot reach. This includes rigorous evaluation on real clinical tasks, systems grounded in private institutional data, safety and failure-mode analysis, and the parts of operative care that are not yet captured as data at all. The surgeon’s or physician’s judgment about what question is worth asking, what outcome actually matters, and what a safe answer looks like is the contribution scale does not hand you for free.
The bitter part of the Bitter Lesson, for us, is that decades of carefully encoded surgical expertise may not be the thing that makes the next great clinical tool intelligent. The liberating part is that it tells us, clearly, where the real work now lies.
David P. Stonko is a vascular surgery fellow.
