Last week I was in the UK for the Faraday Institution LEAP project’s industry day, where I chaired a panel discussion. LEAP is the successor to the Degradation project and currently runs three main workstreams - one on squeezing out the maximum from incumbent high-Ni NMC chemistries, a second on low-cost LMFP and blends with NMC, and the third a more speculative punt at high energy “anode-free” cells. So I asked the panel - comprised of Ian Ellerington, Rob Gruar and Dame Clare Grey - a deliberately unfair question: if LEAP had to narrow to just one, which one would it be and why?
To my surprise, allowing for some hedged answers, the discussion favoured anode-free, including (later) from an audience member representing an anode manufacturer, advocating for making his company’s own product obsolete. I also had the question turned back on me, and put on the spot I also lent my support for the anode free workstream, surprising myself to hear the words come out of my mouth. But my reasoning was simple - I felt drawn to the high risk, high reward option, and if it can be made to work, there’s a rare opening for the UK to build a (niche) manufacturing industry around it where the incumbent Asian cell makers have enormous sunk costs in current technology. In this case, the relative lack of a UK cell industry is not purely a handicap.
Then I spent the rest of the morning session and the subsequent coffee break arguing against myself.
The case for the LMFP workstream, which I had defended before, is arguably stronger: bigger addressable market, nearer-term, more certain. And, depending on who you ask, LMFP development by the big Asian players is starting to run out of steam, potentially indicating a gap for an academic breakthrough. But what does success mean in each case? A breakthrough in LMFP most plausibly means licensing IP, with the bigger share of the value going to whoever already owns the factories, who are not in the UK. On the other hand, success in anode-free could result in more or all of the value remaining in the UK, precisely because nobody’s factories necessarily give them a head start (and there are numerous players with a potential interest in niche, high value cells). In this case it’s not about a comparison of two technologies on their technical merits, it’s about two different scenarios of how value is created. (Also note, I’m talking probabilities here, not inevitabilities.)
Then, following later discussions, I realised my answer also depends on who’s asking. If I was having this discussion as part of my day job, I’d be saying that we shouldn’t touch anode-free with a bargepole - on any heavy vehicle OEM’s planning horizon it’s irrelevant, and I don’t think anyone in that discussion would be arguing with me. (I might also make the same argument at an academic meeting in Sweden for related reasons, which I’ll touch on shortly.) Each discussion reaches a different verdict, and in their specific cases each verdict would make total sense.
It might be tempting then to read this as “there’s no right answer, research whatever you like” - but I believe it’s the opposite. Once it’s clear who’s asking, the correct options narrow significantly and many become wrong. The question I put to the panel wasn’t unfair because it was unanswerable, it was under-specified, partly because I gave no scenario for why LEAP should narrow to one workstream.
The more general relevance here for applied research is the value of a certain level of discipline in what we could call receptor matching: the question “what should we research?” has little meaning without the follow-up question “into what does the result emerge?”. Applied research needs a receptor - a company, industry, capability - that can absorb it and do something with it. The argument for anode-free in the UK works because the receptor could plausibly be created. In Sweden on the other hand, with an automotive-heavy industrial base and post-Northvolt even less of a cell manufacturing ecosystem, anode-free emerges into a sparser ecosystem. Existing industry in Sweden would likely be better off absorbing something else.
So perhaps a test for any publicly funded applied research programme, which is harder than “is the science good”: name the domestic capability or stakeholder that can absorb, scale or compound the result if it works. If the honest answer is “nobody, yet”, that’s either the argument for the moonshot (create the receptor alongside the science), or it’s a tell that the science, regardless of how wonderful it might be, has nowhere to make real impact. The same fact can be either opportunity or indictment, but telling them apart probably means asking some harder follow-up questions still.