Compressing a legal planner into a network

Take the one expensive planner in this repository whose advantage is built only from information a real player can see, label every legal move at fifteen thousand positions with what that planner thinks, and try to teach a small network to reproduce it cheaply.

Why this teacher, after seventeen failures

Seventeen learned models in this repository have failed, and an audit sorted them by cause. The largest group — six of seventeen — failed at ranking the moves that were not played: the model learned the outcome of the move the data happened to contain, and deployment then asked it to choose among alternatives it had never seen labelled. That is the sibling trap, and it is the single most repeated lesson here.

The next largest group failed for a different and more fundamental reason. Their teacher was an oracle that read hidden numbers or the future, so a large part of what it knew was a function of information the student can never have. No amount of training data fixes that.

The flow ceiling work produced a teacher with neither defect. Its legal planner samples complete guesses of the hidden board, solves a short window exactly against each guess, and plays the best column on average. It never reads a hidden value or a future disc, and a mechanical gate proves it: replace every hidden number and the entire future, and it chooses the same column. Its advantage over the reference search is therefore public by construction — and it costs hundreds of exact window solves per move, which is precisely the sort of expense a learned evaluator exists to amortise.

That made it the first distillation target here whose signal is, in principle, representable by a public student.

How it works

1. Run the teacher for 160 whole games and keep the thing it normally throws away. The planner computes a value for every legal column and then discards all but the best; this corpus keeps the whole vector, along with the resolved board after each column, and the same 256 guessed hidden boards are used to score every column at a position, so the comparison between siblings is fair by construction.
2. Also record the value from each half of the guesses separately. That one extra field is what makes it possible, for the first time here, to ask how much the teacher agrees with itself.
3. Make the student a function of the board after the move, not of the move itself. An afterstate evaluator cannot use "which column was this" as a shortcut, because it never sees one. The number of discs the move itself clears is supplied by the search rather than learned, since that is not a property of the board that results.
4. Train it to rank, not to predict. The loss compares all the columns at one position against each other, with an explicit margin term weighted by how far apart the teacher put them; plain value regression is kept only as a weak anchor on the scale.
5. Gate it offline before any gameplay, against the unmodified reference search scoring exactly the same positions, split by whole origin game — and write the pass/fail rule down first.

The thing nobody had measured

Here is a concrete example of the problem this approach uncovered, on the held-out positions.

Split the teacher's 256 guessed hidden boards into two halves of 128 and let each half choose a column independently. The two halves disagree on one position in six (they agree 0.8318 of the time). That sounds like a noisy teacher. But when they disagree, the two columns they cannot tell apart are worth 0.0765 discs apart, out of an average spread of 2.2643 discs between the best and worst column at a position — about 8% of the range.

The label is sharp about value and blunt about which column wins. Which means a training target and a grading rule built on "did the student pick the same column?" are scoring the student on the least reliable part of what the teacher knows. Nothing in this repository had measured that before.

What happened

The gate failed, in every fold, at both model sizes.

The student is not empty: a ranker with a constant board score gets 35.7% and 42.2% on those two statistics, and the student gets 48.5% and 73.6%. It simply did not clear a bar that was fixed in advance, so no gameplay cohort was opened and the shared evaluation seeds were left untouched.

But the dominant explanation is upstream of the student, and it was not what was being tested. Before training anything, this work played the teacher and the unmodified reference search over the same 160 fresh futures. The teacher beats it by +16,777 points with a 95% lower bound of −19,143 and +5.18 moves with a lower bound of −4.56 — neither distinguishable from zero. It wins 85 games of 160 on score and 75 of 160 on lifetime. Its board fills at +1.4798 cells per five-move cycle against the reference's +1.4813: the same number to three decimals. Both policies die of the same thing. A distillation can only transfer what the teacher has, and at this configuration the teacher has almost nothing to transfer.

Calibration was good; ranking was not. The student's value head predicts the teacher's number with a held-out correlation of 0.8742 and a mean absolute error of 1.699 discs against a target spread of 3.958. That is the repository's oldest lesson restated on a brand-new kind of teacher: a well-calibrated value head is not a good move ranker.

Capacity was not the constraint. A model with four times the parameters lands within 0.002 of the smaller one on every held-out statistic.

The sibling problem itself is genuinely fixed. 108,462 labelled (position, column) pairs across 15,833 positions, zero missing labels on legal columns, zero labels on illegal ones, action completeness 1.0000 — the defect that killed six of the seventeen earlier models is simply absent here. That is a real engineering result even though the gate failed.

And the student does carry signal the search does not already have. Compared as a policy it loses badly, which was foreseeable: the reference search spends 615,090 board evaluations per decision and the student spends one per column. Compared as what it was meant to be — an opinion mixed into that search — and with the mixing weight chosen on a separate validation split, it cuts the search's ranking regret by 13% and improves pairwise ordering from 0.7961 to 0.8117, with both improving on both splits. The top-1 improvement appears on the held-out split but not on validation, so it is not claimed.

What this taught us, and what is still open

• Re-measure a teacher before distilling it. The single cheapest thing that would have changed this experiment costs one paired comparator run. The teacher's strength had been carried forward from an eight-game cohort; on a representative sample it is 40% smaller and its lifetime advantage contains zero. Any future distillation should open with that run and only then spend training time.
• Stop targeting the teacher's chosen column. The information is in the value vector, not in the winner. Ranking regret — where half the teacher's own compute scores 0.0073 and the student scores 0.1915 — is the better primary measure, and it is the one the blend probe improves.
• Compare a leaf as a leaf, not as a policy. Pitting one model call against a 615,090-evaluation search and reporting that the model lost was foreseeable. The comparison that predicts deployment is the blended one, and it should be the preregistered headline next time, with the weight fixed on validation.
• A negative result that rules something out. This does not refute distilling a legal planner in general; it rejects this teacher, this target, this loss and these two architectures. What it establishes positively is that successor-closed sibling labels are now achievable here, and that they are not sufficient.
• Still open: the stronger teacher. The seven-move, 256-guess planner was budgeted at about 17 seconds per decision and never run — though the flow ceiling page's later re-baselining suggests its headroom above the reference search is also small.