The Simple Rule Won Under Random Hazards

The learned projection controller had every reason to look stronger than a handwritten rule. It read the complete bounded Gaussian mixture, was trained on all six oracle action values, and received one capped correction on states visited by its own policy.

Under random observation hazards, it lost badly to a rule with one scalar threshold and two actions.

The simple rule recovered 85.1% of the oracle’s one-step gain and 54.3% over four steps. The corrected neural controller recovered -97.0% and -16.3%.

This result is scoped to fresh rollouts in two delayed-resolution benchmark families. It is not a universal claim that heuristics beat learning. It is a clean example of a causal feature, matched to the failure mechanism, traveling better than an amortized oracle policy.

The full evaluation and machine-readable claim audit are in dwrtz/ml-examples at source commit ddc9215.

What “random hazard” means here#

The two benchmark families begin with an ambiguous scalar belief and include a more informative observation channel that can resolve the ambiguity. In the known-schedule version, the future channel sequence is visible to diagnostic policies. In the stochastic version, the resolving channel arrives randomly. The controller knows the hazard model but not the realized future schedule.

This is the deployable information regime. At decision time the policy sees only the current approximate predictive belief, current channel and covariates, known model parameters, and causal diagnostics. It cannot peek at the future channel realization or the exact grid posterior.

The evaluation used fresh decision-state seeds and a fresh paired rollout seed. Each policy faced the same physical futures, so cost differences are not caused by one policy drawing easier trajectories.

The rule measures local approximation pressure#

The local-nonlinearity rule asks whether a single-Gaussian update is likely to be a poor local approximation. For the sinusoidal channels, it computes

where \(x\) is the current channel coefficient, \(f\) is its frequency, and the variance comes from the current approximate predictive mixture. The frequency-squared term reflects likelihood curvature. A Huber transform limits the influence of extreme values:

If \(h(r) > 0.5\), the rule selects the richer five-component branch-and-reduce projection. Otherwise it uses the cheap single-Gaussian assumed-density update.

That is the entire policy. It does not predict oracle values, infer future hazards, or remember previous steps. It reacts to a current causal quantity: local observation curvature multiplied by current uncertainty.

The final stochastic comparison#

After one bounded dataset-aggregation correction, the neural controller and all declared baselines were evaluated on fresh random-hazard states.

Recovery is measured relative to the gap between the full-information oracle and the best fixed action. Negative recovery means the policy was more costly than staying fixed.

The one-step neural failure was resolved at the grouped level: its 95% recovery interval was [-176.3%, -30.2%]. The four-step interval, [-47.4%, 10.3%], crossed zero, but the mean remained harmful. The simple rule, by contrast, captured most of the available one-step gain and more than half of the four-step gain.

Tail behavior pointed in the same direction. At one step, mean cost in the worst 5% of learned-policy rollouts was 3.10, versus 1.45 for fixed projection. At four steps it was 7.80 versus 7.23. The controller’s mean inference latency, 2.92 ms, was too small to explain these losses; they came from its actions.

Why the smaller policy traveled better#

The neural controller was distilled from a full-information oracle. During training, the target action values depended on the exact grid belief even though the network received only the bounded mixture and causal context. The offline state contained substantial signal, but the mapping was noisy, heterogeneous across physical groups, and partly aliased.

Repeated deployment added another mismatch. Each predicted action changed the next approximate belief, moving the controller onto states produced by its own mistakes. One correction improved that visited distribution, but it did not make the learned oracle target invariant to the information regime.

The local rule had a smaller ambition. It did not try to reproduce the oracle’s complete ranking over six actions. It identified one reason a cheap Gaussian projection becomes risky—the interaction of likelihood curvature and belief variance—and chose between one cheap and one rich operator. The feature was available online, its meaning did not depend on a future schedule, and the decision boundary was not learned from an exact-grid teacher.

This is a familiar bias-variance trade in an unusual place. The neural policy could represent a much richer decision surface. The simple rule represented a surface that stayed attached to the causal physics of the current update.

The known-schedule result is different#

The same corrected neural controller was promising when future channel schedules were known. Across all six benchmark families at four steps, it cost 3.0758 versus 3.5994 for the best fixed policy, a 27.8% recovery of oracle gain. Its grouped 95% interval was [-7.7%, 54.1%], so the aggregate result remained uncertain. Worst-5% cost improved from 17.88 for fixed projection to 8.58 for the learned policy.

That specialist result should not be averaged with the stochastic failure. The information contracts differ. Known schedules expose future context that the random-hazard policy does not receive, and the family-level gains were uneven. The result is worth a separately declared confirmation; it is not evidence for a general controller.

It also suggests an obvious gate: use the neural specialist when a schedule is known and the local rule when it is stochastic. That gate was proposed only after seeing these results. Testing it on the same opened rollouts would be selection, not validation.

The stopping decision#

The study declared one correction round, followed by a stop if the corrected candidate still lost to fixed projection and the best simple heuristic. The stochastic evaluation met that condition. We stopped rather than starting a second aggregation round, recurrent-model search, architecture sweep, or policy-gradient tuning on the opened benchmark.

A clean follow-on would declare the known-versus-stochastic gate in advance, freeze the two specialist policies, choose new physical groups and seeds, and report both aggregate and family-level tail risk. Until then, the deployable conclusion is deliberately narrow:

In the fresh stochastic B/F comparison, the local-nonlinearity rule was the best tested causal policy. No general neural projection controller was promoted.

That is a more useful ending than rescuing the larger model. It tells us which information survived deployment, which complexity did not, and exactly what a new experiment would need to confirm.