Michael Nielsen – Why aliens will have a different tech stack than us

Michael Nielsen and I discuss why scientific progress is far more mysterious than the standard “hypothesis → experiment → falsification” story suggests, and what that implies for AI-driven science, the future of technology, and how civilizations might differ from one another.

• The conversation starts with the Michelson-Morley experiment (1887), often misrepresented as the falsification of the ether that led Einstein to special relativity. In reality, Michelson continued believing in the ether until his death in the late 1920s, and Einstein himself was unsure whether he had even read the paper. The experiment ruled out some ether theories but not all, and Lorentz had already derived the correct mathematics (the Lorentz transformations) before Einstein—but interpreted them as dynamical effects of moving through the ether, not as properties of space and time themselves.
• Poincaré came even closer to special relativity than Lorentz, understanding the principle of relativity and the constancy of the speed of light, but he clung to a dynamical interpretation of length contraction as late as 1909. His very expertise may have been what trapped him—he couldn’t let go of the old framework. Einstein, a teenager who also believed in the ether in the 1890s, was less encumbered.
• The muon decay experiments of 1940 confirmed time dilation in a way that would have been very difficult for Lorentz’s interpretation to accommodate, but the scientific community had already adopted Einstein’s interpretation decades earlier, before that experimental confirmation. This shows that human science has some process for distinguishing theories that outruns formal verification loops—but it is not a clean, centralized, or easily articulated method.

The Copernican revolution illustrates the same pattern: Copernicus’s heliocentric model was neither more accurate nor simpler than Ptolemy’s when first proposed (it actually required more epicycles because Copernicus insisted on perfect circular orbits). What eventually made heliocentrism compelling was Newton’s gravitational theory, which unified terrestrial motion, planetary orbits, and tides under one set of ideas. The satisfaction came from explanatory unification, not from any single experiment.

• Aristarchus proposed heliocentrism in the 2nd century BC, but stellar parallax wasn’t measured until 1838. We didn’t need to wait for that measurement to accept heliocentrism—the theory was adopted for other reasons long before.
• Lucretius in the 1st century BC had an idea superficially resembling natural selection, but it was fundamentally different: he imagined a one-time generative filter in the past, not an ongoing gradual process, and had no concept of a tree of life connecting all organisms.

Natural selection took until 1859 despite being “conceptually easier” than Newtonian gravity. Several preconditions had to be in place:

• Deep time: Charles Lyell’s geology in the 1830s established that Earth was hundreds of millions of years old, making gradual evolution plausible. Without this, evolution would need to operate on human-observable timescales, which it doesn’t.
• Biogeography: Colonial-era voyages revealed patterns of species distribution that demanded explanation.
• Fossil evidence: Paleontology showed intermediate forms and a tree of life.
• The near-simultaneous independent discovery by Darwin and Wallace suggests these building blocks were necessary—the idea couldn’t crystallize until enough pieces were in place.

AlphaFold is often cited as proof that AI can accelerate science, but Michael argues the real story is decades of experimental work (X-ray crystallography, NMR, cryo-EM) and billions of dollars to build the Protein Data Bank. The AI component, while impressive, was a small fraction of the total investment. More philosophically, AlphaFold is a 100-million-parameter model with no explanatory reach—it won’t predict something like Mercury’s orbit the way general relativity did. It may contain extractable explanations (interpretability work could mine it for principles), or it may represent a genuinely new type of scientific object that we don’t yet have the right concepts to evaluate.

• The Ptolemy worry: if you train a model on observational data without the right inductive biases, you might just keep adding epicycles forever. Gradient descent alone may not make the locally-worse-but-globally-better leap from Ptolemy to Copernicus.

Einstein’s path from special relativity to general relativity illustrates what a real theoretical revolution looks like: special relativity immediately created a crisis because Newtonian gravity allowed faster-than-light signaling, which is incompatible with relativity. Einstein was forced to find a new theory of gravity. The intermediate stages were messy and wrong in various ways, but the final theory was shockingly simple and beautiful. This kind of progress requires starting from deep principles and thought experiments, not from fitting data.

• The Uranus/Neptune vs. Mercury/Vulcan contrast: both planets had anomalous orbits. For Uranus, the Newtonian fix (predicting Neptune) worked beautifully. For Mercury, the same approach (predicting Vulcan) failed completely—the real answer was general relativity. A priori, you can’t tell which situation you’re in. Science is full of apparent anomalies that turn out to be mundane (the Pioneer spacecraft anomaly was just asymmetric thermal radiation), and you can’t distinguish the revolutionary exceptions from the boring ones in advance.

Michael’s most striking claim: alien civilizations would likely have radically different technology stacks, because the “tech tree” of science and technology is vastly larger than we realize, and exploration of it is path-dependent.

• We tend to think of science as something you do early—understand the universe’s basic laws, then you’re done. But even within physics, we keep discovering new phases of matter (superconductors, superfluids, Bose-Einstein condensates, fractional quantum Hall systems) that we can increasingly design.
• Computer science began in the 1930s with Turing and Church establishing the theory of computation, but we’ve spent 90 years discovering deep new ideas within that framework (public-key cryptography, consensus algorithms underlying cryptocurrency). Knuth was once told computer science wasn’t real until it had a thousand deep theorems—it clearly does now.
• Different civilizations, with different sensory modalities and cognitive biases, would explore different branches of this enormous tree. A civilization that is more auditory than visual, for instance, might develop fundamentally different mathematics and physics.
• This implies enormous gains from trade between civilizations—comparative advantage would be massive because each civilization would have explored different regions of the tech tree. This makes friendliness much more rewarding than in a convergent-tech-stack world.

The “low-hanging fruit” argument for diminishing returns in science is misleading. While any static snapshot might show the best discoveries already made, new fields keep opening up (computer science arose from esoteric questions in mathematical logic), and when they do, progress becomes easy again and young people flood in. The bottleneck is often external—institutions, capital allocation, security for researchers—not intrinsic to the structure of knowledge.

• Empirical studies (e.g., Bloom et al.) show that maintaining constant progress in fields like semiconductors requires exponentially more researchers each year. But these studies focus on narrow, well-defined metrics and miss the creation of entirely new fields.

On quantum computing: the field didn’t emerge in the 1950s despite von Neumann’s expertise in both computation and quantum mechanics because two things converged around 1980: personal computers made computation salient to a broad community, and the Paul trap made it possible to manipulate single quantum states. Richard Feynman got one of the first PCs around 1980-81 and was so excited he tripped and hurt himself carrying it—this historically contingent coincidence of a quantum mechanics expert being exposed to computing at exactly the right moment helped launch the field.

• Michael entered the field in 1992 when his professor Gerard Milburn gave him a stack of papers including Deutsch’s 1985 paper. Very few people were working on it. He was drawn by the deep, provocative questions (can a quantum Turing machine simulate any physical system?) and the sense that fundamental discoveries were still to be made.
• Quantum computing may enable a qualitatively different kind of AGI, since it can compute a strictly larger class of problems. We’ve only been thinking about it for ~40 years without the benefit of working devices, so we may be radically underestimating its potential—just as someone in the 1700s couldn’t have anticipated Bitcoin from knowing about AND/OR gates.

On open science: the movement’s main success is making it a live political economy question—should publicly funded science be openly accessible? The attribution economy in science (journals, priority claims, reputation) is a social construct, not a natural law. Physicists and biologists have opposite explanations for why they do or don’t use preprints, showing that these norms are constructed, not determined by the nature of the science.

• The LHC is a good example of collective science where no individual understands all the levels: accelerator physics, detector physics, vacuum physics, inverse problem solving, quantum field theory, and data processing are each deep specializations. Papers have over a thousand authors who can talk at a high level but don’t understand each other’s specialties in depth.

On learning and creative work: Michael distinguishes between routine work (where you should optimize for speed and avoid procrastination) and high-variance creative work (where you need to be willing to spend long periods stuck, exploring, talking to people). Most people are good at one but not both. The “equal odds rule” (Dean Keith Simonton) suggests that the probability any given output is important is roughly constant—what determines total impact is volume of output.

• For deep learning, you need a forcing function: a concrete problem, a creative artifact (essay, class, project), or a demanding context. Michael hired a physicist friend to create practice problems for him on special relativity because textbooks alone don’t force real understanding. The key question is: what is the equivalent of “do 64 laps” for your particular domain?
• AI chatbots are seductive because they provide an easy substitute for the hard intermediate thinking that actually produces understanding. They’re useful for routine work but can become a way to avoid the demanding cognitive work that leads to real internalization.