The Age of FFOAK and The Better Mousetrap Fallacy

He starts by rewinding about twenty years, and the point of the history is who actually drove progress. The venture capital of that era, retrospectively called Clean Tech 1.0, produced a few modest financial winners, one transformational company, and a string of failures in solar manufacturing and batteries, after which the industry went back to the internet, which paid better. So for most of two decades the engine of innovation was not laboratory breakthroughs or startups but economies of scale and learning curves, driven by large corporations iterating on existing products, and above all by the Chinese state, whose playbook he summarizes as raising manufacturing scale enormously while iterating just enough with each new factory to keep performance improving. The result is that solar and batteries now work, are reasonably affordable and are ready to deploy at very large scale, and he treats it as an encouraging milestone that the biggest remaining questions about them are geopolitical rather than techno-economic. He puts wind turbines, heat pumps and electric motors in the same category, and the grid and nuclear fission in an adjacent one where the technology works well enough and the constraints are policy and regulation.

That is not an argument that nothing more is needed, and he says so directly. Mature technologies still face headwinds, from the growing pains of solar and wind in key markets to the winter peak demand problem heat pumps will eventually run into, and some of the largest gaps are simply not addressable with what exists: no combination of panels and batteries decarbonizes shipping or aviation. Which is what made the last five years’ surge of venture capital back into deep climate tech worth having. He does not claim to know why it happened and offers four suspicions rather than causes: investors looking for something after the internet, a wave of corporate carbon commitments that implied a market for more ambitious technology, an unusual concentration of talented founders, and a government research program launched in 2009 whose seeds matured all at once. The result he describes as a cambrian explosion of options, of which a small fraction are now emerging as leaders with attractive costs, validation at modest scale and teams that have executed.

The pivot is that the only way to learn how those leaders behave at scale is to build them at scale, and because a learning curve needs more than one unit, what they need financed is not one plant but the first few. That stage is where the money stops. The pitch to investors combines technology scale-up risk with infrastructure returns, which he credits a colleague for framing, and the capital intensity is such that most funds cannot assemble a portfolio diverse enough to carry the exposure to any single project. He says plainly that nobody has cracked this, himself included, and offers two predictions instead of a solution: the very best companies will assemble the money from government, semi-philanthropic and creative sources, and some companies that deserve a chance at scale will not get one. That second half is why he calls the same period an Age of Winnowing.

The last move is the one the title promises, and it depends on the first three. Seed-stage investment has held steady even as later-stage capital tightened, which he mostly welcomes, but he argues the conditions that justified seeding everything have gone: capital was cheap five years ago and the field was empty, whereas now capital is scarce and the field is crowded, and the biggest barriers left are the financing bottleneck, regulation, infrastructure timelines and the home-court advantages fossil fuel holds in some sectors, none of which a better device addresses. Worse, he says the record shows his own community tends to overestimate new inventions and underestimate how far learning curves will take the ones already deployed. He scopes this carefully, twice: he does not want to discourage entrepreneurs, and backing new technology is his own job, so the claim is that the bar has risen rather than that it should be closed. His nuclear example shows the cost of getting it wrong, since he thinks the sheer number of competing reactor designs is itself an obstacle to governments and industry converging on a build program, and that picking very few designs and building five to ten in quick succession would do more. His test for what clears the bar has three forms: fundamentals several times better than the incumbent, an application the incumbent cannot serve at all, or a much better integrated product built on a foundational technology that is itself still improving.