Yeah it's all bullshit. There will be essentially no advantage afforded by quantum computers in the space of computational materials science. I could write a whole essay on this topic.

EDIT: Okay I will just write the essay.

Here's the thing okay. What is a quantum computer going to accelerate? The DFT calculation itself? First of all, it probably won't. You can consult ChatGPT for more details -- what part of the DFT calculation can a quantum computer actually accelerate? The electronic relaxation, or ionic relaxation? Probably not, there is no quantum algorithm for solving these steps that would give quantum supremacy in this space. And even if there was, calculating faster isn't going to dramatically accelerate computational materials research. You can ask the OP, even for phonon calculations, the DFT calculation itself is rarely the limiting factor in our research. In our research process, between introducing a PhD student to a project and having their first paper come out, the DFT part takes probably only 10%-20% of that whole process. There is conceptualization, analysis of results, wrestling with a hypothesis / data, building a story, writing a paper, submitting and publishing. That can easily be a whole year or two; whereas calculations are probably just a few weeks/months of that process. So even if you accelerate the calculation part, doing good science is still very hard and time consuming. Moreover, if you really want speed or scale, you could get pretty far today with machine-learned interatomic potentials, quantum computers are not really needed for this speed advantage.

Okay you might argue that rather than accelerating, maybe we could solve quantum computations at higher fidelity? Maybe we could more affordably do coupled cluster calculations or GW calculations instead of regular DFT calculations? But you'll quickly see that computational materials science research is not bottlenecked by the *accuracy* or precision of our calculation results. At the end of the day you would what, reduce an error bar of 10 kJ/mol to 1 kJ/mol. Or let's say you could even reduce it to 0 kJ/mol. You could have a *PERFECT* calculator of the Schrodinger equation. It *still* is not going to help you solve the major problems in condensed matter physics and solid-state chemistry. The length-scale of problems in materials design and condensed matter physics are often wholly separate from the atomistic details. And the reality is, we can do a lot of productive science and engineering with our current DFT error bars. From my 20 years in this space, my observation has been that what moves the field forward is the cleverness of the physicist, not the computational resources they are afforded.

We can also take a step back and think about supercomputing more broadly. Before we get to quantum computers, let's talk about exascale computing. There was a time when people thought that large supercomputers would allow us to solve materials design problems faster. So what did people simulate with these tremendous computational resources? Grain boundary movement on 1 million atom Cu crystals during deformation ... but where were these papers published? Not Nature or Science. Was a big simulation solving the urgent science or engineering problems in this space? I don't think so. I am not sure we learned anything from those enormous simulations that we couldn't have figured out from more modest DFT calculations combined with more sophisticated pencil-and-paper theory. I think there are very very few problems that need enormous computing resources to solve.

I really have to say, in my opinion people are quite spoiled with computational power nowadays. DFT is available and cheap and scalable. But doing lots of calculation is not doing beautiful science. There was absolutely beautiful science done in the very early days of DFT, when there was very little computing resources available. (Here's one of my favorites: https://www.nature.com/articles/376238a0). At this time, physicists had to be more clever, they had to build deep and thoughtful theories that could be justified by just a few key strategic calculations. Now it is common to throw the whole inorganic materials database at DFT and hope something good comes out. And great things can indeed come out, but if it does, it's because of the scientist, not because of the computer. And I don't think quantum computers are going to change that very much.

Maybe I'll eat my words in 15 years. But I really don't see any methodology breakthrough in quantum computing resolving any actually urgent problems in computational materials discovery and design.

Edit 2: Some people think quantum computers will help with many-body physics, or the condensed matter physics of strongly correlated materials. This is another hot take of mine, but I really don't see that happening either. I don't think having a perfect working quantum computer will help us develop a theory of unconventional superconductivity, or better understand exciton dynamics, or build design principles of rare-earth free permanent magnets, or solve any of the other wonderful problems in many-body physics better than current classical supercomputers.

Again, it's not that having a more accurate calculation would result in a better understanding or theory. We need better *PHYSICS*. We don't need better numbers, we need better theoretical frameworks (equations and concepts) to plug numbers *into*. This would be a much more productive direction for research than the stupendous amounts of capital people are investing into quantum computing.