📌 Living index — this is the running master summary of the whole program, kept pinned to the top and updated in place as new results land (last updated 2026-07-08; its date is bumped on each update to stay on top). For the dated week-by-week narrative see Parts 1–10; for artifact-level detail see ITERATION_LOG.md in the paper repo.

This is the whole map. Roughly eighty experimental iterations over the life of the program, grouped into seven phases, each with what it tried, where the artifacts are, and the lesson it left behind — followed by a focused post-mortem of this week’s two SOTA bets, which failed in an informative way. If you read one thing, read the law at the end: in a value-based planner, structure and reweighting buy nothing the TD value pathway doesn’t already consume. Everything below is the evidence for it. All numbers are read from the append-only ledger.

How to count “an iteration”

An iteration here is one falsifiable experiment with its own GO/NO-GO: a proposed change, a matched control, a multi-seed read, a verdict. By that definition the program has run ~80: ~15 foundational redundancy nulls, ~60 numbered campaign iterations (#1–#60), 5 “next-phase” bets, and 3 SOTA bets. Full artifact-level detail is in ITERATION_LOG.md in the paper repo; this post is the readable tour.

Phase 0 — The six mirages (~15 iterations)

The founding question: does adding structure to TD-MPC2 — structural-entropy (“glass”) latents, entity/graph world models, calibration-shaped or jumpy models — buy anything on control? Iteration after iteration returned null: structure ties vanilla at matched budget, and its extra couplings go unused by the value head. A single mechanism check (does the value pathway consume the new coupling?) predicted each null before the GPU bill. Lesson: the SimNorm latent is already value-sufficient (held-out value-decode \(R^2 \approx 1\)).

Phase 1 — Can abstraction solve Panda PickCube? (#1–#17)

We inserted abstraction into a hard contact task every way we could: skill-options, demo-seeding, warm-start, in-loop residuals at persistent authority, curricula, learned grasps. Abstraction-in-loop climbed from ~0.24 to ~0.79 real success — but matched-budget PPO won the asymptote (~0.81–0.83), and the last ~17% turned out to be a physical ceiling: 99.88% of the far-reach tail is kinematically infeasible to grasp upright. Lesson: abstraction buys sample-efficiency and interpretability, not a higher ceiling.

Phase 2 — The beat-PPO campaign & the benchmark (#18–#42)

We turned anecdotes into a matched benchmark and hunted for a clean beat. The one that survived: an abstraction-as-curriculum that warm-starts then releases to free RL — ≥0.95 on OpenCabinet at ≤19.66M steps vs PPO’s 29.49M, 4/4 seeds. Most other “beats” (energy-shaping, CPG, OSC class-controllers) evaporated the moment we ran a same-budget vanilla-PPO control and collapsed to sample-efficiency claims. Lesson: a cross-budget baseline manufactures fake wins; always match the budget.

Phase 3 — The LeCun bets: hierarchy and JEPA (#43–#60)

We tested LeCun’s arguments directly: hierarchical planning, a faithful decoder-free H-JEPA with an anti-collapse term, structural-entropy latents. H-JEPA was a multi-seed null on PandaPickCube — the bottleneck was the low-level motor primitive, not abstraction. Anti-collapse turned out downstream-dependent: the exact term that helps a geometric goal-conditioned nav latent hurts value-based control. Lesson: a non-generative predictor’s information term is not free — its sign flips with the objective.

Phase 4 — Five bets, four nulls (Parts 6–7)

Five falsifiable bets: planning-as-exploration, behavioral-prior taxonomy, glass-as-variance-reduction, pure-JEPA done right, SE-structured latents. Four came back null-to-harmful — planning-as-exploration decisively refuted on CartpoleSwingupSparse, novelty-MPPI worse on 4/4 matched seeds, SE and uniformity both hurting control. This is the pivot of the whole program: every attempt to add structure to win reproduced the oldest finding, so we stopped adding and started explaining.

Phase 5 — The dissection (Papers 3–4)

Instead of “what can we add to beat PPO,” we asked “why does the planner beat PPO, and what inside it does the work?” Three results:

  • A categorical wall. Tuned PPO hits 0/5 seeds ≥ 200 on HopperHop at 472M steps and survives the entropy knob (×3, ×10); TD-MPC2 clears it 6/6 by ~1M. The wall needs contact-criticality — contact-free-but-unstable Acrobot has no wall.
  • A mechanism. A five-loss ablation over four tasks: the value and policy losses are individually fatal (without the TD value loss the agent can’t even learn to stand); the reward head only feeds the planner; and the consistency loss — the “world model” — is the mildest cut of all.
  • A sufficiency law. Trained OFF from scratch, the consistency loss is removable only on HopperHop (n=8) and load-bearing on the planner-led tasks (Walker −23%, Cheetah −38%, Acrobot −44%). It is a rollout-quality regularizer for the planner.

Lesson: a rigorous null program’s real output is a mechanism — “why X wins” is more citable than “we added Y and tied.”

Phase 6 — The SOTA push, and this week’s failure analysis

The sufficiency law hands you a constructive lever: if the consistency loss is a rollout-quality regularizer, make it better. We tried two ways, both this week:

  • Value-Aware Consistency (VAC): weight each latent dimension’s prediction error by its value sensitivity \(|\partial Q/\partial z|\). Result, paired vs matched vanilla at 5M: Walker −8.9%, Cheetah −4.4%. No-go.
  • Uncertainty/Rollout-reliability Consistency (URC): weight by the model’s own rollout drift (open-loop vs teacher-forced). Result: Walker ≈ −7%, Cheetah ≈ −9%. No-go.

Why both failed (the same way)

Both schemes concentrate the consistency gradient on some latent dimensions and de-emphasize the rest — VAC on the value-sensitive ones, URC on the currently-unreliable ones. The failure is identical and follows from what the planner does:

The MPPI planner rolls the latent dynamics forward over many candidate action sequences and ranks them. Which dimensions matter for that ranking is trajectory- and horizon-dependent, not fixed. A dimension that is value-irrelevant or currently-reliable now can become decisive three steps into a rollout under a different action. Starving its prediction accuracy degrades the very rollouts the planner depends on.

So the planner needs faithful dynamics on every dimension it might explore, and uniform consistency is exactly the objective that delivers it. Any reweighting is a bet that some dimensions matter less — and over a multi-step rollout, that bet is wrong often enough to cost 5–9%. (VAC has an extra early-training problem — \(Q\) is immature when its gradient sets the weights — but URC, whose weight comes from the dynamics model, fails too, which rules out “immature Q” as the whole story.)

What it establishes: the reweighting family is closed. Uniform consistency isn’t just load-bearing — it’s near-optimal in form. A clean negative that strengthens the sufficiency paper. Full write-up: REPORT_consistency_reweighting_failure.md.

What’s next — the one honest abstraction swing left

If you can’t improve the world model by re-emphasizing its objective, the only remaining lever is to change what the value pathway sees. That is the one route the redundancy work said structure could matter but never did. So the next bet (running when the boxes free) is a value-conditioned abstraction: a bisimulation-style latent metric — states pulled together by reward-and-transition equivalence — which is structure the value pathway consumes by construction, followed by a value-sufficient bottleneck if that nulls. Either outcome is publishable: a beat is the abstraction-SOTA we’ve chased for eighty iterations; a null is the definitive close of the redundancy question.

Two open mechanisms worth nailing (future work)

Two “why” questions we brushed but never mechanistically closed — each has a partial answer and one decisive, un-run experiment (full write-up: FUTURE_WORK_open_mechanisms.md):

  • Why is HopperHop unique? It is simultaneously the hardest task for PPO (the sharpest categorical wall) and the only task where the world-model loss is removable. The hypothesis — Hop is exploration-hard but execution-simple (a low-dimensional limit-cycle gait the policy executes without accurate multi-step rollouts), while Walker/Cheetah/Acrobot are execution-precision-hard (their return level needs the planner’s rollouts) — is stated but not tested. Decisive probe: policy-only vs MPPI at matched weights, Hop vs the dense tasks. Would turn Paper 4’s descriptive split into a predictive law.
  • Why does the JEPA latent collapse in nav but not in control? We showed closed-loop feedback amplifies it and data-width doesn’t cause it, but never isolated the trigger. Leading hypothesis: control latents are anchored by a dense TD value gradient into the encoder; nav’s goal-conditioning anchors weakly, so its rank collapses. Decisive probe: vary anchor strength (add a graded dense auxiliary target to nav H-JEPA) crossed with online/offline. Would yield the actionable rule “add anti-collapse only when the downstream signal is too sparse to anchor latent rank.”

The law that survived eighty iterations

In a value-based planner, structure and reweighting buy nothing the TD value pathway doesn’t already consume.

Abstraction buys sample-efficiency where its prior fits, and interpretability always. It does not raise the ceiling, and — as this week proved — it cannot improve a world-model objective that is already value-sufficient. The durable contribution of the program is therefore a dissection of why the planner wins and a near-optimality result about its world model, honestly earned across eighty tries, most of which said no.