The capstone. Part 6 laid out five concrete bets after a supervisor review; we ran them in parallel on two GPU boxes. This post is the scorecard — including two appealing hypotheses that controlled ablations killed. Each thread has its own living log (linked below) with the full numbers; here is the synthesis.

Scorecard

bet one-line verdict state
A — planning as a directed-exploration operator (flagship) NULL — planning is sample-efficiency + exploitation, not exploration Thread A
B — “when does a behavioral prior help RL?” taxonomy the surviving positive contribution (speed-not-ceiling) Thread B
C — abstraction as variance-reduction NULL — the 6/16 “wins” are a wash Thread C
D — JEPA anti-collapse, done right reversal — pure JEPA doesn’t collapse (state/pixels/narrow) Thread D
E — SE for structure discovery folded into A3; deprioritized once A went null Thread E

Two of the five were genuine, testable, appealing hypotheses — and the controls said no. That is the point of running controls.

The flagship went null — and it’s the most useful result here

Part 6’s flagship was the strongest new story: that the real reason model-based planning beats PPO on exploration-hard tasks is exploration — “planning is a directed-exploration operator.” The sharpest datapoint was TD-MPC2 beating PPO on HopperHop 367 vs 33. The claim: planning explores its way to states (and hence policies) that on-policy PPO never reaches.

The honest test isn’t TD-MPC2-vs-PPO (that confounds the model/algorithm with planning). It’s planning vs a policy-only ablation of the same agent — MPPI on versus off, everything else held fixed — with state-space coverage logged across training. We ran that three ways:

  • A1-core (HopperHop, from scratch). No coverage gain from planning. But nothing learned in the budget, so inconclusive.
  • A1-full (WalkerWalk, learns). Planning narrows coverage post-competence (directed exploitation onto the gait manifold) — the opposite of the hypothesis — yet reaches competence ~1.5–2× faster (training return leads the policy-only arm by +130–160 through the whole competence phase, converging by ~120k). Coverage does not mediate the benefit: planning covers less and learns faster.
  • A1-decisive (CartpoleSwingupSparse, sparse and exploration-hard — the quadrant the thesis needs). The clean test of “does planning discover reward where policy-only stalls?” Answer: no. Both arms discover the sparse reward 3/3; the policy-only arm discovers it slightly earlier (140k vs 157k). Planning’s advantage is entirely post-discovery exploitation (final return 540 vs 331).

Three controlled tests, one conclusion: planning is not a directed-exploration operator. Its real, repeatable value is sample-efficiency and exploitation — faster to competence, higher and steadier returns once the reward is found. That is the campaign’s “speed, not ceiling” law, restated at the level of the planner itself. The HopperHop 367-vs-33 remains real, but it is a TD-MPC2-vs-PPO fact (a better model + value learning), not a planning-vs-no-planning one — the planning-vs-π-only return edge there was only +1.7.

Because the mechanism was exploration, A2 (novelty-seeking MPPI) and A3 (SE-discovered exploration subgoals) — and with them Thread E — were deprioritized: there is no exploration effect to amplify or direct.

A correction we made on ourselves

The first A1-full read reported “policy-only slightly ahead, a flat null,” from a noisy single-episode eval at 140k. Reading the clean (n{=}3) training curve overturned it — planning has a large, consistent mid-training lead. The verdict is not “planning does nothing”; it’s “planning buys speed/exploitation, not exploration.” The lesson: read the training curve, not one eval snapshot.

The JEPA thread reversed — cleanly, four ways

Part 5 reported a “downstream-dependent anti-collapse taxonomy.” Part 6 flagged that we had tested it on the wrong object — TD-MPC2 is value-anchored, not a pure JEPA. Testing it right reversed the story:

  • D2 / D2-ext (pure JEPA on DMControl state). A pure self-predictive latent (encoder + jumpy predictor + EMA, no reward/value loss) does not collapse. The zero-anti-collapse arm has the best readouts; the collapse is prevented by the predictor+EMA (BYOL) asymmetry, not by any explicit repulsion. Adding anti-collapse ranges from neutral to harmful, and the earlier geometric-vs-value split was nav-specific, not a law.
  • D3 (pixels). Same picture in the high-dim regime LeCun’s argument actually targets — no collapse, uniformity maximizes effective rank but gives the worst readouts.
  • D1 (SE arm on TD-MPC2). On a value-anchored latent, structural entropy hurts value-control just like uniformity, and SE+uniformity combined is worse than either — a redundancy result, correctly scoped.
  • Open cell (narrow / on-policy data). Does a narrow, reward-seeking data distribution collapse a pure JEPA? No — effective rank stays 10–22 as the buffer narrows; the value-R² that falls just tracks the narrow buffer’s low value variance, not encoder collapse.

So the collapse regime is narrower than any data-distribution story: pure JEPA is robust on broad DMControl (state and pixels) and on narrow/on-policy data. The one setting that did collapse — the closed-loop online nav H-JEPA — is not explained by data breadth, which points at the value/goal closed loop itself as the trigger. That is the honest open question, and it is a much sharper one than we started with.

What survives: the taxonomy (Thread B)

The quiet result is the real one. Across Panda and DMControl, injecting a behavioral prior (an analytic skill, a hand-controller, a structured latent) is governed by two axes — prior-fit × exploration-difficulty — with the escape-difficulty frontier operationalizing the second. A fitting prior is a speed lever (~1.6–7× faster to competence, same ceiling); a mismatched one is dead weight; on exploration-hard tasks only the prior-equipped agent survives at a practical budget. The Part-7 planning result slots straight in: planning is another speed lever, not a ceiling or exploration lever. This is the paper — an empirical taxonomy, honest about what abstraction does and does not buy. Finalizing it is the next step.

The meta-lesson

Two appealing, publishable-sounding hypotheses — “planning is the exploration breakthrough” and “abstraction reduces variance” — did not survive controlled tests. A third — “JEPA needs anti-collapse” — reversed once tested on the right object. None of that is failure; it’s the controls doing their job. The through-line of this whole program holds: abstraction and planning buy sample-efficiency — speed, not ceiling — and the fastest way to a true result is a matched-budget control and the discipline to read the (n)-seed curve rather than the number you were hoping for.

Every figure and number above is pulled from the disk-backed results ledger; the nulls are reported as deliberately as the positives. Per-thread detail lives in the five linked living logs.