The correction
At one point in our discussions, the suggestion came up that some still-unknown principle might connect evolution, development, learning and culture into the runaway cumulative intelligence we see in humans. The pushback was immediate, and it reshaped the project:
Life in the universe has had billions of years to emerge and form, and the computational complexity of such systems is absurd compared with anything we can compute. That may be exactly why we've built simpler, designed systems for narrower problems rather than generalized ones.
A blank agent trained on a modest cluster shouldn't be compared casually with the end product of evolution, development and culture. The biological system had planetary-scale parallelism over geological time.
"Physics performs the computation"
Organisms don't pay to simulate chemistry. They are chemistry, interacting with real physical processes. Every bacterium testing a mutation is running an experiment that a simulator would have to compute at great expense. In that sense the universe has been a very large, very parallel search process for a very long time.
We treat this as an analogy, not a calculation. There's no agreed way to convert biological history into FLOPs, and we don't know the minimum artificial cost of similar capability.
Nature's historical expenditure is not a proven lower bound on what similar capability requires. Much of that history was contingent. Useful artificial abstractions needn't simulate chemistry or replay the evolutionary path.
And it isn't established that compute alone explains the gap between artificial and biological open-endedness. Compute is a central constraint, not the whole story.
Search is amortized across timescales
A new learner never starts from nothing. Prior search is stored at several timescales:
Model pretraining is an artificial example of the same move, even if learned parameters aren't a lossless archive of their training data. So are engineered architectures, optimizers and datasets. They're shortcuts that reuse human discoveries. That's fine, as long as we don't mistake a shortcut for evidence that a blank system rediscovered intelligence on its own.
A striking pattern in that sequence is that evolution eventually produced faster optimizers than itself: lifetime learning, then culture. An artificial open-ended system may likewise need to produce new optimization processes, not run one fixed outer loop forever.
The bitter lesson, and its limits
Rich Sutton's "bitter lesson" is that general methods which scale with computation have repeatedly beaten methods built on human knowledge. That's a strong argument against prescribing milestone chains. But it's also an argument that cuts the other way here. The methods that won (search and learning) still rely on carefully engineered machinery, and they scale given the compute. If you don't have the compute that evolution had, you need to know which general structure buys the most.
The middle ground: general inductive biases
Hypothesis
Two failure modes keep recurring. Prescribing the discoveries undermines the autonomy we want to study. Requiring everything to emerge from scratch probably makes the experiment unaffordable. The way between them that we find most promising:
Engineer a system that can learn how to search, while leaving the discoveries, and increasingly the search methods themselves, open to change.
Concretely: extract general principles from biology, reuse prior discoveries, and supply the smallest useful set of general inductive biases, leaving goals, skills, concepts and strategies open. Candidates we've discussed include:
- Memory, so discoveries persist
- Plasticity, so the system can keep changing
- Prediction, so experience becomes reusable structure
- Locality, so changes have bounded effects
- Inheritance, so competence crosses generations
- Recombination, so discoveries can be combined
- Modularity, so parts can vary without breaking the whole
This is a list for generating hypotheses. We haven't settled on it, and we haven't shown that all of these are necessary. The interesting experiments would remove one at a time.
Unrestricted search doesn't always fail, and engineering doesn't guarantee efficiency. What makes progress impossibly slow is a vast space of possibilities, expensive evaluations, and little guidance. The aim is to change those three conditions without prescribing the answer.
Simulation, and the real world
Environments like Minecraft offer something valuable: an executable world where consequences can be tested repeatedly, branched and compared. But "millions of worlds" isn't millions of affordable, fully trained agents. A rough estimate for a population-based version of our full ambition (ten million actions of experience × 100 lineages × 100 generations) comes to about 1011 environment interactions. That pushes toward shared world models and many policies rather than thousands of independent agents each rediscovering gravity.
In the real world there's no full simulator at all. But a learner doesn't need to simulate reality to decide whether an experiment is worth running. It needs good enough predictions about the consequences that matter, and an understanding of where those predictions are unreliable. Optimizing software can be tested directly. A physical process may need a limited model plus a small trial. Demand may need real observations. A general learner would have to learn where cheap reasoning is enough and where evidence is worth paying for.
The same problem, for evolution
We felt this constraint most sharply when designing evolving agents. If each generation needs days of real-world exposure, and only a handful of individuals can be run at once, evolution over full neural networks is far too slow to pay for itself. Evolution is competitive mainly when the search space is discontinuous, evaluation is cheap, and what's being evolved changes slowly, such as learning rules, priors and hyperparameters, rather than billions of weights. The details are on the Heredity page.
The full budget of a frontier discovery loop
Test-time compute research shows that how inference effort is allocated matters in the mathematical settings studied. For Rubedo, a meaningful comparison counts proposal tokens, verifier computation, tool calls, retrieval, archive storage, communication, failed searches and wall time. Post-training cost should be reported separately and amortized only across an explicit number of future tasks.
Investigation. Compare accuracy–cost curves for a stronger single model, additional independent samples, verifier-guided search and coordinated agents. Keep tool access and task splits matched, and report both latency and total computation: parallelism can improve one while increasing the other. The learning-versus-search pilot asks where training is worth its upfront cost and where inference remains cheaper.
What we don't know
- What to supply up front, what to learn, and how to compare the trade-off fairly.
- Whether a small set of general biases is enough to make cumulative discovery tractable at any interesting scale.
- How to compare approaches at equal total cost, including the cost of discovering learned mechanisms.