TL;DR. Part 36 gave the verdicts; this post gives the full case files for branches 1 and 2 — what was tried, in order; what failed, with the numbers; and what we would run next. The planner program’s arc: every stage’s conclusion was correct on the tasks it looked at and wrong as a generalization, until a 22-task sweep found the variable — action dimensionality — that all the earlier task selections had held fixed. The measurement program’s arc: five measures failed three ground-truth axes in three different ways (geometry, estimator sensitivity, trainedness), which is itself the finding: the failures are structural, not bad luck.

Program 1 — what is a planner worth, and what part of it?

What was tried, in order

Stage A (July): does the planner earn its keep at all? Deployment-time toggle on identical weights (cfg.mpc flipped at eval, paired eval seeds), our own trained-without-planner checkpoints, four DMC tasks. Result: yes — hopper-hop +175 points (p=0.002), and a cheap planner (32 samples × 1 iteration, ~3% of full MPPI’s compute) recovered 91% of it. Conclusion recorded then: the planner is worth having; its search budget mostly is not.

Stage B (Part 34, branch 1): decompose it over training. full − none = (full − cheap) + (cheap − none) across five checkpoints per task. Result: all the interesting variation — hopper’s advantage growing eighty-fold, walker’s decaying — lived in cheap − none (“having a planner”); full − cheap (“searching hard”) was small on every task and never grew. A two-factor account (model improving pushes planner value up, policy improving pushes it down) survived on 3 of 4 tasks; not claimed as confirmed.

Stage C (Part 34, branch 2): does representational capacity set planning value? Preregistered. latent_dim ∈ {4…512} × 3 seeds, planner toggled on identical weights. Result: flat across 128× (rho=+0.064, p=0.82). Refuted, as the prereg’s own decision rule demanded. Bonus finding: every column was flat — a 4-dim latent matched the shipped 512 on hopper-hop.

Stage D (Part 36, branch 1x): find the cross-task principles. The obvious weakness of stages A–B was n=4 tasks, all low-dimensional. The official TD-MPC2 release ships single-task checkpoints for 39 DMC tasks; we ran the three-arm toggle on 22 tasks × 3 released seeds (66 evaluations, 10 episodes per arm, paired seeds; quadruped dropped to a dm_control version incompatibility). Preregistered three principles: (P1) cheap − none tracks the policy-to-ceiling gap; (P2) full − cheap is small everywhere and if anything shrinks with action dimensionality; (P3) sparse-reward tasks need the planner more at matched policy gap.

What failed, with the numbers

All three predictions. P1: rho=+0.31, p=0.16. P3: residual test p=0.29. And P2 failed in the only way better than passing — refuted with the opposite sign, significantly:

full − cheap ~ action_dim: rho = +0.58, p = 0.006 (predicted ≤ 0).

The table that rewrites stages A–B:

task (action dim) none cheap full having extra search
humanoid-walk (21) 3 9 896 +6 +887
dog-walk (38) 26 95 843 +69 +748
dog-run (38) 60 87 723 +27 +636
walker-walk (6) 430 836 988 +405 +152
hopper-hop (4) 351 531 492 +180 −38
acrobot-swingup (1) 635 570 627 −65 +56

On 21–38-dimensional bodies, the released agents are almost entirely planner at deployment — the policy prior scores 3–60 out of ~1000 — and the cheap planner collapses with it, because 32 random samples cover a 4-dimensional action space and cover nothing in a 38-dimensional one. Stages A–B were not wrong about their tasks; they were wrong to generalize, because every task they looked at sat in the regime where sampling is easy. “Search depth buys little” was a task-selection artifact, and the artifact was ours.

What still stands from the earlier stages: on low-dimensional tasks the cheap-planner result is real and useful (hopper’s 91% recovery at 3% compute is untouched); the capacity refutation (stage C) is untouched; the two-factor account remains unconfirmed and now needs a dimension-aware restatement before it is worth testing again.

Caveats carried: the official checkpoints trained with the planner, so the toggle measures deployment-time value for search-trained agents — the same measurement across tasks, so the cross-task comparison holds, but absolute values don’t transfer to our trained-without-planner numbers. And having correlates rho=0.88 with per-task eval noise, so no having-based claim survives the prereg’s own sensitivity rule; the dog/humanoid search effects are the lowest-noise cells in the table.

What’s next, ranked by cost

  1. The sample-coverage curve (cheap, eval-only, ~$2). If the mechanism is coverage, planner value on dog should climb smoothly with samples: run the toggle at 32/128/512/2048 samples on dog-walk and hopper-hop. Prediction to preregister: dog’s curve saturates late and steeply; hopper’s saturates by 32. This turns the P2 refutation into a mechanism test.
  2. Prior-quality confound check (cheap). Is the dog prior useless because the task is planner-dependent in principle, or because 3M steps under-trains a 38-D policy? The released multi-task and larger single-task checkpoints give priors of different quality on the same task — measure whether having shrinks as the prior improves, which is the two-factor account’s dimension-aware form.
  3. Train-time vs deployment-time on one high-dim task (expensive, ~$15–30 GPU). Our June result says the deployment toggle understates train-time planner value (24% recovery). If that holds on dog, the true search dependence of high-dim tasks is even larger than +750. One task, two training runs (mpc on/off), only if the budget allows.

Program 2 — a measure of information content for JEPA representations

The method that made failure meaningful

You cannot validate an information measure against unknown truth, so the program built axes where the truth is manufactured: grid (cube position quantised to g×g, so the image carries exactly 2·log₂g bits — must rise), nuisance (distractors in a side panel, scene pixels bit-identical, verified model-free: raw-pixel decodability drifts −0.9% — must stay flat), corruption (pixel noise — must fall; the axis itself had to be re-verified this campaign: σ ≤ 0.1 was inert, σ ∈ {0.2, 0.35, 0.5} moves raw decodability 0.997 → 0.429). Since Part 35, every axis test also carries a sensitivity check: correlate the candidate’s effect across levels with everything else the axis moves (representation rank, predictor R², final loss); |r| > 0.9 flags a probable artifact.

The five obituaries, in order

1. Variance and effective rank (the field’s standard health checks). Failed nuisance in the strongest possible form: effective rank rose 15.0 → 26.8 (exact p=0.0079, complete separation) while recoverable information was provably constant. Geometry is not content; adding unpredictable distractor dimensions adds directions. This was also the direct demonstration of Yoon’s H1.

2. InfoNCE (a genuine lower bound, the principled answer to the upper-bound objection). Inflated under nuisance (0.89 → 1.03, p=0.032) with its cap far away. A valid bound estimated from finite data with a learned critic is not a reliable measurement — the critic exploits nuisance structure. “Principled” and “trustworthy” came apart.

3. Structural information, five constructions deep. k-means proxy: no signal (+0.099 vs known bits). selib SE-optimal: a degree-matched null with no structure scored higher than the real graph (+0.322 vs +0.285) — every positive SI result vanished when the null was subtracted. Exact global-optimum certificate: worse than local search. Directed + self-loops (faithful to the proposal): fails, not flat. Differentiable soft assignment (the proposal’s own form): the only variant that robustly clears its null — stable, and constant: it does not track information content on any axis. Related casualty from the adjacent campaign: the coarse-graph “structure” result, 20/20 maps at p<0.0001, was an off-diagonal-mass sensitivity artifact (Part 35).

4. E2 — one-step predictability (“measure the part of the representation the model can predict”). Failed nuisance immediately: the distractors follow a random walk, and random walks are highly predictable one step ahead (predictor R² 0.97–0.99 on them). “Predictable” is not “task-relevant” — real nuisance is often predictable too.

5. E2b — the action-conditional spread (this campaign; preregistered). Fix E2’s flaw by measuring only what the action changes: distractors don’t respond to actions, so they cannot enter. Two statistics, both dead. action_eff_rank: no dynamic range on any axis — flat on grid (rho=−0.04, p=0.85) where truth spans 2→10 bits, flat on corruption, indistinguishable under nuisance. The rank of the action’s effect is set by the architecture, not by knowledge: E2b measures controllability, which is orthogonal to content. action_var: moves under nuisance where it must not (p=0.032, a shift 13× its entire grid-axis range), and its one apparent pass — falling with corruption, rho=−0.93 — was flagged by the sensitivity check at r=+0.992 with final training loss. It tracks how well the model trained. The check written after Part 35 caught its first fake pass within a day of existing.

The shape of the failures

Marginal statistics read the geometry of the embedding cloud. Graph measures inherit the estimator’s sensitivity to density. Predictor measures read trainedness and controllability. Three different failure modes, one common property: each measure is faithful to some real quantity — it is just never the quantity “task-relevant information.” Meanwhile the one number that behaved on every axis, readout R² against the true state, is the one you can only compute when you already have the answer. And the adjacent campaigns quietly removed the program’s motivation: capacity doesn’t set planning value (128× flat), and hierarchy’s planning advantage is not a representation property either.

What’s next, ranked by honesty

  1. Test the premise before the sixth candidate (cheap, data on disk). Yoon’s H3 says a good measure should predict planning performance. Readout R² did, on 15 agents (rho=+0.607, p=0.020). Extend that to the full ~200-run TD-MPC2 archive and the h3c sweep: if even the yardstick stops predicting planning value at scale, the program’s premise — that any representation scalar could — is dead, and stages 1–5 are explained at once. This costs nothing but analysis time.
  2. Reward-readout as the practical proxy (cheap). The RL setting always has one ground truth that needs no privileged state: reward. Decodability of reward/value from the frozen latent is computable in deployment and is at least anchored to the task. Run it through all three axes like every other candidate — it may die like the rest, but it is the only candidate whose ground truth ships with the problem.
  3. Write the obituaries up properly. Five measures, three validated axes, a sensitivity-check protocol, and two artifact catches (off-diagonal mass, loss-tracking) — as a negative-results methods paper. This project treats honest negatives as first-class output; this is the most complete one it owns.

Both programs’ raw data and analysis scripts resolve to files at commits on results/three-branch-2026-08-20 in SuuTTT/world-model-paper; the preregistrations and their dated amendments are in PREREG_extension.md on the same branch.