The DARPA Quantum Benchmarking program, the precursor to today's Quantum Benchmarking Initiative, started from a question that sounds like it should have a short answer: should the US government procure quantum computing capability at all, and if it should, is the cost worth it?

Answering it took three years, multiple organizations working in parallel, and a great deal of very careful science. Yudong Cao, CTO at QuEra's partner Zapata, spent those years working the full length of that effort, from the top of the funnel where candidate applications are first identified down to detailed resource estimation on a fault-tolerant machine. His assessment of what the field got for the trouble is unusually candid, and it is not flattering.

This post presents Cao's argument, drawn from his talk "Quantum Applications, Algorithms, Circuits" at the QuEra Quantum Alliance 2026 Annual Meeting (QQA 2026). It is a speaker's critique of an industry-wide practice rather than a QuEra position, and we are publishing it because it is a serious argument made by someone who helped build the thing he is criticizing. The separate portion of his talk, on formal verification and LLM-generated circuits, is worth its own post.

A Funnel That Narrows Fast

The top of the funnel was interview work. Zapata, together with L3Harris and several other enterprises, sat down with domain experts across seven to nine fields to ask where a quantum computer might plausibly help. That produced somewhere between 150 and 200 candidate application instances. Cao is explicit that these were first cuts at the problem space, not scientifically established results. Chemistry and differential equations stood out as the areas most worth pushing to the next stage.

Three years later, roughly ten of those instances had been carried all the way down: crossed T's, dotted I's, end-to-end resource estimates reaching physical qubit counts and wall-clock runtime.

Ten. Out of roughly 150-200 application instances.

The Ship Whose Hull Is a Sphere

The reason the funnel narrows that sharply is that each surviving instance is enormously labor-intensive. Electronic structure calculation, the chemistry problem closest to Zapata's own expertise, follows a relatively well-worn path from molecular system down to physical resources. Other problems are far less obvious.

Cao's example is computational fluid dynamics: estimating the drag on the hull of a ship. Before a quantum solver can touch the problem, it has to be reformulated into something a quantum algorithm can even approach, which is a research project in itself. Then the estimation begins. Two years in, the paper is still being updated, with small refinements still surfacing and independent improvements landing in the literature in the meantime.

And the end-to-end estimate that emerges does not answer the original question. It answers a version of the question in which the hull of the ship is a sphere. Talk about spherical cows, as Cao put it.

What the Landscape Plot Does Not Show

Anyone who has spent time in the benchmarking ecosystem has seen the resulting plot: application instances scattered across axes of resource cost, a tidy map of the quantum application landscape. Zapata, along with other performers in the QB program, generated those dots. Every one of them came from a process like the ship hull problem.

What the plot does not communicate is that every dot was time-boxed. The work stopped because the program ended, not because the analysis was finished.

"We knew that we could still go further, but the program has to end and we have to turn in our deliverable," said Yudong Cao, CTO at Zapata. "There are orders of magnitude improvement you can make if you just give us six more months. But we had to stop because that was when the buzzer rang."

The plot looks authoritative. It is, in its author's own description, a snapshot in time, taken as of March 2025, of an analysis nobody had finished optimizing.

The False Precision Problem

The sharper version of the critique arrived later, when Cao moved into advisory work and began talking to enterprise clients about how they actually think about quantum. What he ran into there was a problem of false precision.

"If you sit across the table from someone who runs logistics for a living, they don't know what it means for an application to take 5 million qubits and five hours," said Cao. "They speak in a very different language."

Two failures are stacked on top of each other here. The first is translation: a resource estimate expressed in physical qubits and hours carries no intuition for an executive deciding whether to fund a program. The second is more serious. Even for a reader fluent in the units, the number is not stable. Any of these estimates can move by orders of magnitude on the strength of a single new result in error correction, compilation, or algorithm design. A figure presented as a coordinate on a chart is really a reading taken on one particular day, by a team that had to stop when the clock ran out.

The Arithmetic Nobody Wants to Do

Then comes the part of Cao's argument with real teeth.

Hardware companies, QuEra among them, are now making concrete public commitments about what will exist and when. QuEra's own roadmap puts Libra, a 256-logical-qubit fault-tolerant system built from over 10,000 physical qubits, on Amazon Braket in 2028, with named partners attached to that delivery. The field is on the hook for dates.

So run the numbers on the application side. If three years of coordinated, well-funded, multi-organization effort produces roughly ten fully fleshed-out applications, and those ten are not even optimized, what does the catalog look like by the early 2030s? Another twenty, maybe thirty, at that rate.

Cao's question is whether that is an acceptable return given the scale of investment the field has absorbed. He spent three years of his career producing that plot, and he describes the result as nowhere near as satisfying as he wanted it to be. Coming from a principal investigator rather than a critic on the sidelines, that is worth sitting with.

Screen First, Commit Later

The proposed fix is not more rigor. It is a different allocation of it.

The pharmaceutical industry does not subject every molecule to a full clinical program. It screens fast and cheap across an enormous candidate space, then spends its expensive, rigorous testing budget on the small set that survives screening. Quantum application discovery currently does the opposite: it applies the expensive method to whatever instance happens to be in front of it, and spends years finding out whether that instance was worth the trouble.

What Cao wants instead is a lightweight predictive model for quantum amenability, trained on the small number of precise, hard-won data points that programs like Quantum Benchmarking actually produced, and used to generalize across a much wider search space. The goal is to identify problem instances that are classically hard and quantum easy in weeks rather than years, and to curate a collection of good candidates rather than a handful of exhaustively documented ones.

The second half of the idea matters as much as the first. Because hardware roadmaps shift and error-correction approaches keep improving, the estimates themselves should be living objects that track the state of the field, not static data points frozen at the moment a deliverable was due.

Why We're Running This

Cao is describing a gap between two halves of the same industry. Hardware timelines are getting more specific, more public, and more accountable. The inventory of rigorously vetted applications those machines are meant to run is growing at a rate measured in single digits per multi-year program.

QuEra has a stake in this. A committed 2028 delivery date raises the stakes on the application question rather than settling it, which is a large part of why the company's co-design work with customers focuses on identifying quantum-relevant workloads and testing them against classical baselines before anyone commits to a larger program. Nothing about that resolves Cao's critique. If anything, it depends on the same thing he is asking for: a faster, more honest way to tell which problems are worth the expensive analysis.

The three-year, ten-application pace was never going to scale. It is a useful thing for the field to admit out loud, and better still coming from the people who set that pace in the first place.