TL;DR. Yoon’s critique of Part 32 was that we had findings, not claims. He is right on both counts. The planner result now has a rule and a mechanism: planning is a scaffold for a not-yet-good policy, its value is set by the policy’s distance from ceiling, and that predicts a perfect rank ordering across our four tasks (rho = 1.000, n=4) and explains the 49% decay between 200k and 400k steps. The measurement work, as posed, has no hypothesis — “a good metric should ignore irrelevant clutter” is a sanity check, and discovering that SI fails it is not a result worth a paper. Hierarchical planning is the focus, and it shares the planner work’s through-line: both are about what search buys.

⚠️ Correction, same day

The within-task prediction below is refuted by our own data, and we found out by testing it. Every eval.csv already contains the full budget curve, so the claim was checkable without new runs. Planner advantage (full − none) across training:

task 50k 100k 200k 300k 400k policy alone, 50k → 400k
walker-run 227 160 115 71 71 523 → 735
acrobot-swingup 189 202 210 199 170 58 → 327
cheetah-run 50 4 −20 44 66 450 → 851
hopper-hop 2 18 100 149 175 14 → 152

The post claims “within any task, the planner’s value should decay monotonically with training budget”. It decays on walker, is flat on acrobot, and grows 80-fold on hopper. The prediction is false as stated.

What the data supports instead is a two-factor account. As training proceeds the model gets better, so the planner has something better to search through — pushing its advantage up. The policy also gets better, so the planner is needed less — pushing it down. Whichever moves faster sets the direction. Hopper’s policy stays far from ceiling throughout (14 → 152 of ~1000), so the model effect dominates and the advantage grows. Walker’s policy closes most of its gap (523 → 735), so the policy effect dominates and the advantage halves.

The cross-task ordering below still holds (rho = −1.000, n=4) — but it is now evidence for the policy half of a two-factor account, not for the single-factor scaffold story. Section 1 should be read with that substitution.

The critique

Three points, paraphrased:

  1. The planner work is another “which tasks need a planner” result. More tasks buy more empirical suggestions, never a principle. We need a rule.
  2. The measurement work has no hypothesis. We are testing that a measure should be invariant to visual clutter and reporting that SI is not. That is a property a metric ought to have, not a claim about the world.
  3. Hierarchical world models are where to focus.

All three land. Below is what we do about them.

1. The planner result, restated as a rule

The finding was: a planner at ~3% of MPPI’s compute recovers 91% of its value on hopper and 46% on walker. That is a catalog entry. Here is the rule underneath it.

Claim: planning is a scaffold for a policy that is not yet good, and its value is set by how far the policy is from its ceiling.

Two pieces of evidence, one within a task and one across tasks.

Within a task. Walker at two budgets, everything else fixed:

arm 200k 400k gain
no planner 652.0 735.1 +83.1
cheap planner 754.9 767.8 +12.9
full MPPI 791.5 806.4 +14.9

The planner’s advantage falls from +139.5 to +71.3 — a 49% decay. And the mechanism is visible in the columns: the gap closes because the policy caught up (+83.1), not because planning got worse (+14.9). Planning was standing in for a policy that could not yet act well on its own.

Across tasks. If that is the mechanism, then the planner should be worth most exactly where the policy alone is worst. It is:

task policy alone headroom to 1000 planner gain relative gain
hopper-hop 152.5 847.5 +174.8 1.146
acrobot-swingup 327.4 672.6 +169.8 0.519
walker-run 735.1 264.9 +71.3 0.097
cheetah-run 851.4 148.6 +65.7 0.077

rho(policy-alone return, relative planner gain) = **-1.000** — a perfect rank ordering across all four tasks. With n=4 that is p = 0.083 two-sided, so it is a hypothesis with a perfect ordering, not an established law. But it is the right shape: it predicts, rather than cataloguing.

What it predicts, and how to kill it:

  • Within any task, the planner’s value should decay monotonically with training budget, and approach zero at convergence.
  • Across tasks, relative planner value should track policy headroom — so “which tasks need a planner” is not a task property at all, but a training-state property.
  • Falsifier: a task where the policy is near its ceiling and the planner still helps a lot. Or a task where the policy is far from ceiling and planning does not help.

This also retires our own earlier framing. We had reported cheetah as “saturated, so the planner does nothing” as though saturation were a quirk of that environment. Under this rule, saturation is the explanation — cheetah’s policy is at 851 of ~1000, so there is nothing for a scaffold to hold up.

2. The measurement work: an honest verdict

The critique here is sharper and we accept it. Our test was: hold information constant, add visual clutter, see which measures stay flat. That is a sanity property. A metric that fails it is broken; a metric that passes it has demonstrated nothing except not being broken. Reporting that five SI variants fail a sanity check is not a contribution.

What would make it a hypothesis? Looking at what we actually measured, the candidate measures sort by what they read:

class measures result
the marginal p(z) variance, effective rank, embedding std fail — inflate on information-free clutter
a learned bound on I(Z;S) InfoNCE fails — inflates too
the transitions p(z'\|z) SI, five variants fails differently — tracks temporal smoothness
task-anchored held-out readout works, and needs labels

That table suggests a real claim: task-relevant information is not a property of a representation alone — it is defined relative to a decoder, so no label-free measure of it can exist. Every candidate we tested is measuring some surrogate — spread, smoothness — that correlates with usefulness in some regimes and not others. The falsifier is clean: exhibit a label-free quantity that predicts downstream performance across regimes.

We are not claiming that. It is an impossibility-flavoured hypothesis and we have four failed measures, which is evidence but not proof. What we will do is stop running the sanity check and stop reporting its failures as results.

The one thing from this line that survives on its own is narrower and we will state it narrowly: effective rank has zero correlation with planning performance (rho = -0.029, p = 0.923, 15 agents) while being used across the literature as evidence a representation is healthy. That is a warning about a specific practice, not a theory.

3. Hierarchical planning is the focus

And it shares a through-line with §1, which is why the two belong in one program rather than two.

The target is HWM — Hierarchical Planning with Latent World Models (Zhang, Terver, Zholus, Chitnis, Sutaria, Assran, Balestriero, Bar, Bardes, LeCun, Ballas). World models at multiple temporal scales in one shared latent space, trained purely by next-latent prediction; the long-horizon model’s predictions become subgoals for the short-horizon one. On a real Franka arm: 70% versus 0% for single-level planning, from a single goal image, with 3x less planning compute. Code and checkpoints are public.

Two papers independently name the same bottleneck. HWM: “to keep long-horizon search tractable, HWM learns an action encoder that compresses primitive action chunks into latent macro-actions.” Hi-LeWM: unconstrained high-level search “can select latent macro-actions that appear favorable under the learned model but produce poor control targets”, and constraining that space is worth +11.3 and +14.7 percentage points. Their diagnosis is explicit — the frozen low-level controller executes well-aligned subgoals fine, so subgoal generation is the bottleneck, not control.

The through-line. Section 1 says a planner is a scaffold whose value depends on how much the policy still needs it. Hi-LeWM says hierarchy’s value depends on whether the high-level search space is constrained to things the low level can execute. Neither is a claim about prediction quality — both are claims about what search is buying and when. That is the program:

Search in a world model is not a free improvement. Its value is set by what the rest of the system cannot yet do, and by whether the space being searched is one the controller can act in.

That framing makes §1 and §3 the same paper, and it demotes §2 to a methods note.

The plan, cheapest first.

  1. Load HWM’s released checkpoints, extract latents per temporal scale, and ask which measure predicts planning success across their conditions. No training. This is also the fair version of the test §2 kept failing to construct — HWM’s 0% → 70% is a real quality gradient we did not build and therefore cannot have broken.
  2. Use SI as a diagnostic on the learned macro-action space: does it separate working configurations from failing ones? Falsifier: if it cannot, SI adds nothing here and we stop.
  3. Only if both survive: an SI-derived constraint on high-level search — the only step that would be a method contribution.

What we are not proposing, stated so it is not re-proposed: not replacing HWM’s learned action encoder with a graph partition (that is the representation-swap pattern SE’s own case studies record as its main failure mode), and not using SE to choose the number of levels (already gated and killed — SE is provably indifferent between a multiway tree and its binary refinement, so it always returns a dendrogram; we measured branching exactly 2.00 and depth indistinguishable from a null).

What changed in one line

We had three directions and a pile of measurements. We now have one program with a claim — search is a scaffold, and its value is set by what the rest of the system cannot yet do — a rule that predicts rather than catalogues, and a target system where that rule can be tested on a real robot with released checkpoints.

Numbers above trace to SuuTTT/world-model-paper and SuuTTT/SE-JEPA. The planner-headroom ordering is n=4 and is offered as a hypothesis with its falsifier attached, not as a result.