Small experiments, honestly reported

1. Evolving a weight generator for MNIST

February 2026 · Run

Question. Can evolution find a compact developmental program that produces networks which learn quickly? That's the Baldwin effect in miniature (see Evolvability).

Setup. Each genome was the parameter vector of a small CPPN, a network that takes the coordinates of two neurons and outputs the weight between them. Each CPPN was "expressed" into a three-layer MNIST classifier (784 → 256 → 128 → 10). Input neurons sat on the 28×28 pixel grid and hidden neurons along a line. That network then trained for just 20 steps of Adam on batches of 128 images. Fitness was the average test accuracy measured at steps 0, 5, 10 and 20, an area-under-the-learning-curve score that rewards starting well and improving fast. Each generation kept the top 15% as elites and filled the rest with Gaussian-mutated copies. Every generation was compared against freshly initialized random CPPNs as a baseline.

What happened. The results weren't good. Evolution made little convincing progress, and the suggested fixes felt like patches rather than answers. So we stepped back to ask what a CPPN fundamentally is and isn't suited to.

What we think it means.

• Geometry mismatch. CPPNs are pattern generators, biased toward symmetry, repetition and smooth spatial variation. The first layer has real geometry, since pixels have positions. Deeper fully connected layers don't. Hidden neurons have no natural order, so we were imposing a spatial prior on a space that isn't spatial.
• Smoothness and compression. We were describing about 300,000 weights with a few thousand generator parameters, which assumes the solution is a smooth geometric function. Good MLP weights are often irregular, so a performance ceiling shows up early.
• A long, noisy causal chain. Genome → CPPN → weights → network → training → accuracy. Each mutation ripples through every step, so the selection signal is delayed, indirect and noisy.
• Search settings. A small population, the wrong mutation strength or a noisy fitness signal could each have stalled progress. These are the classic failure modes of indirect encodings, and we didn't explore them systematically.

What we took away. CPPNs have worked best where solutions really do have spatial regularity: vision, sensor grids, gaits, motor coordination. Their most promising role isn't to replace gradient descent. It's to generate starting points and structure (initial weight patterns, connectivity masks, layer scalings), with gradient descent handling the fine detail. A better next version would use a convolutional architecture, where geometry is real. This experiment also led to the genome-versus-generator collapse analysis, which we think is the more important result.

What it doesn't show. That indirect encodings can't work, or that evolution can't shape learning. It shows that this encoding was a poor fit for this architecture at this scale.

2. Can heredity become protected under pressure alone?

February 2026 · Run

Question. If passing on information is costly and noisy, will selection alone push replicators toward compact, robust, genome-like encodings, without anyone defining a genome? (Background: protected heredity.)

Setup. Each digital organism was a byte string with an energy budget that drained every tick. Reproduction copied the parent's program with random bit flips, at an energy cost proportional to the program's length. A child was viable only if its program passed a fixed validity check. We ran two worlds:

• World A had copying noise, a cost proportional to length, and no help after birth. A child had only what it inherited. Prediction: programs shrink toward a minimal viable, robust encoding, and the population stays stable.
• World B was the same, except parents could cheaply "patch" a child after birth, a side channel around heredity. Prediction: programs bloat, and no pressure toward compact heredity appears.

What happened. The world we expected to show emerging heredity went extinct almost immediately. The "route-around" world thrived, with bloated, highly variable programs. Our prediction was wrong, and it's worth being plain about that.

What we think it means. World A crossed the error threshold. Copying noise was 0.3% per bit, so a 25-byte (about 200-bit) program picked up roughly 0.6 bit flips per copy. Viability depended on a header byte and a checksum over the whole program, with no redundancy, no error correction, no repair and immediate death. Almost any flip was lethal. Viable reproduction fell below what the population needed to replace itself. Selection pressure can only shape lineages that survive long enough to be selected. Pressure guarantees selection only if survival is possible. And World B confirmed the other half: give selection a cheap side channel and it ignores heredity entirely.

What we took away. This turned the error catastrophe into a concrete research topic. The interesting regime is the narrow band where lineages can approach the fidelity boundary without crossing it. Mechanisms to test next include redundancy and error correction, producing several offspring and selecting before birth, graded instead of all-or-nothing failure, modularity, and recombination as an error filter. It's the same bottleneck early life had to get through.

What it doesn't show. That protected heredity can't emerge under pressure. It shows that our parameters started past the threshold, so the question was never really tested.

3. Proposed: a laboratory of 2-D landscapes

Proposed · Not run

Strip intelligence away and look only at search. Two-dimensional optimization landscapes can be built to contain local minima, deceptive valleys, plateaus, narrow bridges, distant superior optima, and environments that change over time. On them we can compare gradient descent, random search, evolution strategies, population methods, adaptive mutation, diversity preservation, novelty search, restarts, exploration bonuses and meta-optimization.

A 2-D landscape isn't intelligence. It's a cheap, transparent lab for the tension between exploitation and exploration, and especially for watching whether a search process can learn to adjust its own settings: mutation strength, selection pressure, exploration rate. You can see exactly where each method gets stuck.

4. Proposed: a small toy market

Proposed · Not run

A population of 5 to 20 non-reproducing learning agents in an artificial market with hidden environmental regimes, public and private information, assets, trading, costly communication and incomplete information. Agents would have recurrent memory and structured actions (see Agents), and could start from conventional methods such as centralized training with decentralized execution (MAPPO).

What we'd look for: information sharing, specialization, reputation, deception, coalitions, arbitrage, collaborative inference and persistent roles, along with the population-health measures on the Collectives page. The point is that Rubedo doesn't have to build the grand vision all at once. A small environment can isolate one hypothesis.

5. Proposed: the diamond testbed

Thought experiment · Not run

Can an agent in Minecraft, rewarded only for diamonds, independently discover capital investment? The design has six constraints, six phases of gradually removed scaffolding, a set of measurements, and a catalogue of failure modes. Read the full design →

Proposed: four frontier learning pilots

October 2026 · Proposed · Not run

These extend the frontier learning agenda into comparisons small enough to inspect. They complement the earlier landscape and heredity work. We have not selected a model, implemented a benchmark, allocated compute or produced results. Begin with one cheap, independently checkable task family; add mechanisms only after a simpler comparison is informative.

A. Learning versus additional search

Question. Does training change transferable capability, or primarily the chance of sampling a correct response?

Design. Start with a small accessible base model and generated code tasks with executable specifications. Compare the base, supervised fine-tuning, RLVR and a frozen-model search harness. Treat teacher-assisted curricula and multi-turn agentic RL as separate arms when affordable. Keep problem splits, tool access and inference limits consistent; report training cost separately and across stated amortization horizons.

Measures and controls. Predeclare pass@1, a pass@k curve, actually selected answer accuracy, total compute, verifier errors and retention. Include original task families, compositional variants and a withheld family. Log teacher hints and failed attempts. A base model given more inference compute is an essential control.

Reason to revise. Higher pass@1 with no coverage or transfer gain supports improved sampling efficiency in this setting. If the gain requires extra tool access or teacher information, attribute it accordingly. Finite sampling cannot prove a hard capability ceiling.

B. Diversity as a useful stepping stone

Question. Do diverse candidate archives improve later problem solving beyond reward-ranked selection?

Design. Freeze the model, tasks and checker. Compare random search, reward-only evolution, novelty search and a bounded MAP-Elites-style archive of program strategies or tool workflows. Match generation and evaluation budgets; vary behavioral descriptors. Compare a fixed curriculum with random ordering and a learning-progress curriculum on the same final task distribution.

Measures and controls. Count independently checked solutions, held-out transfer, time to discovery, retained competence and archive cost. Replay archived candidates on later tasks; remove or shuffle the archive to test causality. Audit whether apparently different candidates have the same behavior.

Reason to revise. More occupied niches without downstream usefulness would weaken the preservation hypothesis. Gains erased by memory cost, descriptor choice or matched random search would argue for a simpler method.

C. Coordination and memory that repay their cost

Question. Can agents accumulate reusable evidence without producing an expensive consensus around the same mistake?

Design. Compare one agent, independent workers, coordinated workers and workers with shared memory, using the same total tokens, tool calls and storage limits. Include both decomposable and sequential tasks. Ablate role assignment, communication and memory separately.

Measures and controls. Record verified success, duplicate effort, latency, communication cost, disagreement and correlated failures. Rotate seeds and roles. Test a fresh agent's ability to reuse records; introduce stale, contradictory and untrusted memory entries in a restricted environment.

Reason to revise. If a larger single-agent budget matches the gain, coordination has not shown an advantage. Increased agreement without increased externally verified accuracy is a failure signal.

D. Bounded improvement of the search process

Question. Can changing the search procedure make subsequent investigations more efficient across multiple rounds?

Design. Allow a controller to change a small set of search parameters, archive policies or tool workflows around a frozen model. Keep executable evaluation code and final tasks outside its write access. Compare a fixed controller, hand tuning, random controller search and an evolved or learned controller under equal total optimization budgets.

Measures and controls. Test successive generations on fresh task families, tracking improvement per full search cost, rejected changes, regressions and retention. Include independent seeds, checkpoint replay and ablations of accepted modifications. Count proposal and evaluation costs even when a modification fails.

Reason to revise. Improvements confined to the tuning tasks suggest overfitting. Plateaus, growing evaluation costs or deteriorating transfer would constrain the recursive-improvement hypothesis. A positive result would establish bounded controller improvement in this setting, not indefinite self-improvement.

What every experiment should record

Whatever we run next, we've committed to recording: the question or hypothesis; the environment, including any hidden or supplied structure; model and learning assumptions; compute, memory, interactions and wall time; the comparison or baseline; results, including failures; evidence of retention and transfer; and the limits of interpretation. Above all, what humans supplied versus what actually emerged.

For these pilots, also freeze model and harness versions, training/validation/final splits, evaluator versions and stopping rules before comparison. Record token and tool budgets, hardware or API costs, archive storage, teacher contributions and all selection attempts. Use repeated seeds and report dispersion or uncertainty intervals; do not select only the best run. Keep audit tasks separate from repeated validation, and report contamination checks and unresolved provenance.

Run generated programs with least-privilege access and time/resource limits. Keep a separate audit of false acceptances, reward exploits, invalid proofs and memory poisoning. Changes to the checker require independent review and a new evaluation record. Publish reproducible artifacts and negative outcomes before increasing the scope of autonomous experimentation.