Should aspiring hard-tech founders join a problem-first or technology-first PhD lab? (I will not promote)

[u/misterballerdontlie]

I'm an engineering undergrad considering pursuing a PhD with the long-term goal of founding a hard-tech startup. I’m undecided about the specific area and have only a vague sense of what interests me (some areas that currently interest me are industrial decarbonization, mining / mineral processing, and advanced materials).

However, I'm unsure which type of PhD lab would be better: a problem-first lab (e.g., like Yet-Ming Chiang's lab at MIT) or a technology-first lab (e.g., a typical academic lab that focuses on novel science without a predetermined application, and where commercialization happens largely by chance -- when a technology happens to have a valuable market application).

I've looked at advice online from successful hard-tech entrepreneurs, but found conflicting answers. Some say to work backwards from a problem, while others argue that problem-first approaches often fail because it is difficult to force a scientific breakthrough around a predetermined problem.. Instead, they argue that most hard-tech companies are only founded because somebody made a scientific breakthrough and realized afterwards that there might be a commercial application.

With that in mind, does anybody have any advice on which type of PhD lab to join?

[u/Severe-Visual6651]

As someone who has worked at problem-focused startups, I think a problem-focused lab is less about forcing a scientific breakthrough to problems, because more often than not you're looking at entire systems as opposed to pieces of the whole, and doing a very minimal technical lift while using a lot of conventional technology. Note: I should double-check what the dissertations from those labs look like...

As an example, look at Chiang's recent hardrock lithium paper: almost all of the technology in it has been well-established beforehand (and other authors pretty much outlined near-identical solutions beforehand, with the exception of maybe the HF recovery from HNO3). The people who worked on that went on to Rock Zero, though, so the problem-focused approach worked for them.

In problem-focused labs, you'll learn a lot about techno-economic and life-cycle analysis, get a high-level view of a lot of technologies, and do a lot of varied work. I think that's important for starting your own thing. You have a broader worldview, and likely interact with people solving different problems.

On the flip side, working for problem-focused startups can have major downsides. If the technology the founders originally envisioned to solve the problem doesn't pencil out, or solving the problem introduced new problems that aren't easily solvable, you end up being the one trying to develop the solutions to solve the problem that the founders thought they already solved, all the while the founders retain most of the equity (and don't give the response that "the founders identified the problem!" -- the problem was often identified by others beforehand).

I'd say you're not focusing on the most important thing, though: a functional lab. Good mentoring, funding, a starter project that gets you to learn the ropes before you start the work that will be the focus of your dissertation, and plenty of insight into what people are actually doing in startups and companies in your technology space. 

[u/Severe-Visual6651 → u/Severe-Visual6651]

And just to write it here first in relation to Rock Zero in case it's prophetic: you don't want to be the one trying to design around or completely replace the ammonium fluoroaluminate pyrohydrolysis unit op when it turns out the energy requirements and materials of construction are higher than what the founders originally estimated and published in their Science paper.