Read this one. Part 25 was an audit assembled from notes and missed an entire research line. Part 27 rebuilt the inventory from all 87 posts and added a data-availability column. This post is the decision document: what to write for ICLR, ranked, with the evidence grade for each claim stated honestly enough that a reviewer’s first objection is already answered.

0. The one-paragraph version

We set out to design a better world model. We do not have one. What we have is a causal account of how a world model earns its keep — it shapes training, not decisions — measured in a design with no confound left to attack, and reproduced across two agents that exploit the model in completely different ways. That is the paper. Everything else here is either supporting evidence, a clean negative result worth a section, or dead.

1. The evidence grades used below

grade meaning
A n≥5, p<0.05, replicated, and the obvious confound explicitly controlled
B n≥4 with a clear effect, but one confound unaddressed or p between 0.05 and 0.2
C suggestive; n≤3, or p>0.2, or an in-sample statistic
D null or retracted

The campaign’s base rate matters when reading these: seven times an n=3 pattern has evaporated at n=5. Grade C here means “do not build a paper on this yet”, not “probably true”.

2. The candidates, ranked

#1 — Search is a training effect, not a decision-time effect · Grade A

Train TD-MPC2 with its planner and it scores 364.2 on hopper-hop (n=5). Train it without the planner and switch the planner on afterwards, on the frozen weights, and it scores 87.5 — it recovers 24%. On walker, across 8 checkpoints, adding the planner at deployment is a net loss (mean 0.960×).

Why this survives review. The comparison holds the policy identical across arms — same weights, same state distribution, same headroom. The reviewer’s standard objection to every “planning helps” result (“your baseline just had more room to improve”) has nothing to attach to.

Why it generalises. DreamerV3 has no search anywhere; it uses its model only to train the policy on imagined rollouts. It reproduces the same task pattern — hopper 2.40× (p=0.009, n=6), walker 0.95× null (n=13/11). A search-based explanation cannot produce that.

The mechanism, visible in one cell. A hopper seed whose policy scored 0.0 could not be rescued by the planner (0.0 with search too). MPPI searches through the learned model; a run that never learned a policy never collected the data to learn a usable model. Planning is not a module you attach to a failed agent.

What it kills: “train cheap, plan at deployment”. Measured, and the answer is no.

Cost to finish: the result is complete. Writing only.

#2 — Adaptive planning: the ceiling is real, and the obvious signals cannot reach it · Grade B/A

If the value is in training, the natural follow-up is plan only where it pays. Two measurements, both on frozen checkpoints, no training:

The ceiling (Grade B). Δ = Q(planner action) − Q(policy action) per state. Sorting by Δ and taking the top 10% captures a median 53% of capturable value, held out across 6 checkpoints (range 0.23–0.88). Δ is reproducible at r = 0.76 between two planner draws, so it is a state property, not dice. The planner costs ~35% of wall-clock, so a perfect gate at k=10% would pay ~3.5% for ~half the benefit.

The negative (Grade A). Nine candidate signals across three independent families — value uncertainty (Q-ensemble disagreement, spread, policy std, advantage gap), action sensitivity (a 3%-cost probe plan’s return spread and top-gap), and model reliability (one-step latent error, reward error, observation jump) — all show Spearman ≈ 0 against Δ and gate efficiency ≤ 0. Not one of them finds the states where planning pays.

Why this is a good section rather than a failure. It converts “someone should try gating the planner” into a measured statement: the opportunity is real and worth ~half of search’s value, and the three most natural feature families are provably blind to it. That is a well-posed open problem, not a shrug.

Caveat carried in the open: I first reported this ceiling as 0.83–0.91. That was in-sample — selection and evaluation on the same noisy draw. Held out it is 0.53. I then over-corrected to 0.22 by generalising from one checkpoint. Both corrections are in git.

Cost to finish: complete as a negative result. Turning it positive requires a feature family outside these three.

#3 — Reward structure sets the value of search, on walker · Grade A (walker) / D (as a law)

walker condition plan never gain p
stock (smooth) 807.4 (n=4) 705.4 (n=4) 1.14× 0.029
harder, conjunctivity unchanged 480.2 (n=4) 447.0 (n=4) 1.07× 0.029
conjunctive (hardened gate) 816.9 (n=5) 443.9 (n=5) 1.84× / 1.91× med 0.008

Making walker’s reward conjunctive nearly doubles what planning buys, at matched baseline. Making it merely harder does nothing. The planning arm is tight (sd 34.3) while the no-plan arm scatters (sd 163.4) — search rescuing runs that would otherwise fail.

But it does not generalise to hopper. There, breaking the conjunction left the gain intact (3.53× → 3.87×, p=0.343) while making the task easier destroyed it (3.53× → 1.21×). The two tasks disagree, at n≥4 on every cell. Publish this as a dissociation on walker, not as a law.

#4 — How claims decay: the methodology paper · Grade A (it happened)

Seven times an n=3 pattern died at n=5. The causes are documented with timestamps:

  • arrival-order bias — the cheaper arm finishes first, so a speed-vs-quality ablation is biased by the very effect it studies
  • in-sample selection — sorting by a noisy quantity and scoring the sort with the same noise (my own oracle frontier, 0.91 → 0.53 held out)
  • within-cell spread exceeding the effect — hopper’s cells span 258–578, wider than any hopper effect ever claimed here
  • silent instrument bugs — a Q function that randomly subsamples 2 of 5 heads per call; a torch.compile graph that freezes the planner’s RNG so two “independent” draws are byte-identical; a budget cap that announced enforcement it could never perform because vastai was not on cron’s PATH

Workshop paper, not main track. Real, and we have the receipts.

3. What is dead, and should not be revived without new evidence

direction verdict grade
H4 on hopper ablating the consistency loss at 50k/150k/250k vs never: +46.5 / +38.0 at n=5, p ≥ 0.72. The n=3 “+165.9” was the control drawing three low seeds D
Conjunctivity as a general law tasks disagree; hopper says difficulty D
“Train cheap, plan at deployment” 24% recovery, negative on walker D
Structural entropy as a latent regulariser 13–16 levers, all null D
Jumpy / temporal abstraction the flagship +60% was reward-hacking (0% real success) D
Planning-as-exploration fails a controlled plan-vs-policy test three ways D
Hierarchy, options, H-JEPA, SE latents null — all tested where the flat policy already worked D

The last row has a re-reading worth one sentence in the paper: every one of those was tested on tasks whose plain policy already succeeded, which is precisely where #1 predicts nothing to gain.

#5 — The world model’s contribution is front-loaded within a run — on walker · Grade A (confirmed n=5)

Added after this document’s first version, and it reverses what §3 said about H4.

ablation point walker (n=5) p hopper (n=5) p
off @ 50k −18.4 0.008 −56.9 0.468
off @ 150k −12.8 0.016 +46.5 0.722
off @ 250k −7.2 0.230 +38.0 0.722
per-cell sd 3.6 – 8.9   96 – 131  

This is the first pattern in the campaign to survive the n=3 → n=5 jump. It went −25.7/−17.8/−10.2 → −18.4/−12.8/−7.2: tighter, still monotone, two cells significant. The previous seven all collapsed at n=5.

Removing the world-model loss costs 25.7 points at 50k, 17.8 at 150k, 10.2 at 250k — a monotone decay, exactly the shape H4 predicted, on the task H4 did not name.

Why hopper shows nothing is a fact about hopper. All 12 walker runs span 39.5 points (4.9%); a single hopper cell spans 289–573. The instrument resolves a 10-point effect on walker and cannot resolve a 200-point one on hopper.

This is worth a paragraph in the paper regardless of how #5 resolves. We chose hopper as the primary task because its planning gain is the largest in the suite (3.53×) — and it is the task where nothing is measurable at achievable n. Most of the seven retracted n=3 patterns are hopper results. Selecting the biggest effect selected the worst signal-to-noise.

Why it strengthens #1. Candidate #1 says the model’s value is in training rather than decisions. This says that value is concentrated early in training. Two independent instruments — a frozen-checkpoint planner toggle and a training-time loss ablation — on two different tasks, reaching the same conclusion. Promote both together.

4. The one positive result that is not ours to claim, and should be

A coding agent iteratively writing a programmatic controller (Weng’s Learning Beyond Gradients) took PandaPickCube from 0% → ~9% real success in hours, on a task where gradient RL reward-hacked to literally zero (hovering banked 89% of return; box_target_max = 0.0000). It is the only thing in nine months that solved a task gradient RL could not.

Its value was diagnostic, not competitive: it answered is this task solvable at all? when RL’s answer was an opaque zero, and then generated the demonstration data nothing else could produce. Ceiling: ~9% open-loop vs a properly-budgeted PPO’s ~66–83% closed-loop.

This belongs in the related-work and discussion, not as a contribution — but leaving it out would misrepresent what the campaign learned.

5. Recommendation

Write #1 as the paper. Title it around the finding: the world model’s value is in what it makes the agent collect and learn, not in what it computes at decision time. It is the only Grade A result with a mechanism, a cross-agent replication, and no confound left standing.

Include #2 as the second half. It is what #1 implies (gate during training, not deployment), it has a measured ceiling, and its negative is clean enough to be a contribution rather than an apology.

Use #3 as a supporting section on walker, stated as a dissociation.

Submit #4 separately to a workshop.

What I would not do: keep hunting for the single sentence that explains both hopper and walker. Two tasks, two answers, at n≥4 on every cell — that is the finding, and forcing a resolution would mean ignoring one of them.

Added 2026-08-10 — two gaps, one scoping correction, and the proposals they generate

Everything above was written as though “does planning help?” were a question about planners. Two objections raised on 2026-08-09 show it is not, and both were correct. They change what §5 recommends, so they are recorded here rather than folded silently into the text.

6.1 The JEPA objection — our flagship claim is narrower than §2 states

The objection. A JEPA/DINO-WM agent is a next-state predictor plus a planner: no policy, no RL, and it works. If planning can carry a task with no policy anywhere in the system, then “planning’s value is that it shapes what the policy collects” cannot be a claim about planning in general.

This is right, and candidate #1 must be scoped. What reconciles it is a variable we never isolated — what the model was trained on:

  TD-MPC2 JEPA / DINO-WM
model trained on its own self-collected stream broad, diverse, off-policy data
objective value-equivalent pure prediction
accurate where the current policy already goes over a wide region
can you search it cold? no (24% recovery) yes — that is the whole method

So the honest form of #1 is: in online model-based RL where the model is trained on self-collected data, the planner must be present throughout, because it is what keeps the model’s training distribution good enough to search. The deployment toggle did not fail because planning is intrinsically a training-time phenomenon — it failed because that agent’s model was only ever trained on data from a bad policy.

This is a better framing than the one we had, because it makes a prediction: give TD-MPC2 a model trained on broad off-policy data and the deployment toggle should start working.

6.2 The behaviour-cloning gap — the baseline we never ran

The objection. In practical game AI, supervised behaviour cloning routinely beats both RL and planning, and we never considered it.

Also right. BC appears in this campaign exactly once as a real arm — Part 25, distilling the analytic controller out into a policy, where “BC / warm-start / DAPG all failed”. That failure is specific: the controller is non-Markov, so cloning it into a Markov policy is ill-posed. It says nothing about BC as a demonstration-based baseline, which we never ran.

We even had the demonstrations and used them for something else: the HL-loop programmatic controller (§4) produced working PandaPickCube trajectories, and we spent them seeding TD-MPC2 rather than establishing a baseline. Without that baseline, “planning helps” is measured against a weak alternative, and a reviewer will say so.

6.3 A retracted framing: “MBRL has a circular dependency”

I first pitched §6.5 below as breaking a circular dependency — the planner needs an accurate model, the model is only accurate where the planner has been. Withdrawn on two counts. MPPI has no parameters, so nothing about the planner is learned and no loop closes through it. And the residual loop — model → behaviour → data → model — is not specific to MBRL; model-free RL has exactly the same thing. That framing dresses up ordinary on-policy distribution shift as a discovery.

The real asymmetry is a train/query mismatch, and it is specific to planning:

  • a policy is queried where it is trained — at visited states;
  • a planner is not. MPPI evaluates 512 action sequences over horizon 3, sampled with noise around the policy’s actions, so by construction it queries the model at latents that were never visited. Asking “what if I did something other than what I do” is an off-distribution query.

Nothing in the training objective targets the query measure. Model-free RL has no analogue, because the critic is queried where it is trained.

6.4 The candidates these generate, ranked

S1 — World models in MBRL are representation learners, not simulators · RUNNING

Claim. The world-model loss earns its keep by shaping the encoder, not by producing a simulator worth rolling out.

Why the existing evidence points here. On cheetah, planning is worth ~1.00× — search through the model buys nothing — yet removing the model loss costs 58–127 points (n=5). Something is bought that is not simulation. DreamerV3 reproduces the task pattern with no search anywhere. And sixteen explicit-abstraction levers nulled precisely because the model loss was already doing the representation work they duplicated.

The decisive ablation. Stock TD-MPC2 cannot separate the two, because its consistency loss

L_c = Σ_t ρ^t ‖ dyn(z_t, a_t) − sg(enc(s_{t+1})) ‖², z_0 = enc(s_0)

sends gradient to both the dynamics head (through dyn) and the encoder (through z_0); the target is already under no_grad, so z_0 is the encoder’s only path. Run a second latent rollout for the consistency term starting from z_0.detach() and the two are separated:

arm dynamics head encoder shaped cheetah return n
A stock consistency + value/reward yes 900.6 (sd 17.0) 5
B WMP_CC_SG=1 consistency + value/reward no 817.9 (sd 102.1) 5
C consistency_coef=0 value/reward only no 656.4 (sd 98.1) 3
(off at 50k, for reference)     842.8 (sd 66.2) 5

Because .detach() changes no values, the consistency loss is numerically identical in A and B. Verified on a fixed batch before spending the compute — same loss to the last digit (0.016058076173067093), same dynamics gradient (0.043782633957885744), encoder gradient 0.00626 → exactly 0.0:

== STOCK ==  {"consistency_loss": 0.016058076173067093,
              "encoder_grad_norm": 0.006258090169236204,
              "dynamics_grad_norm": 0.043782633957885744}
== SG ==     {"consistency_loss": 0.016058076173067093,
              "encoder_grad_norm": 0.0,
              "dynamics_grad_norm": 0.043782633957885744}

Reading. B ≈ A → the loss buys a simulator, S1 is wrong. B ≈ C → the loss is an auxiliary representation objective and the “world model” is not modelling the world in any way the agent uses.

FINAL (2026-08-10, both tasks n=5): S1 is REFUTED, and walker settles it

  A stock B stop-grad C no loss encoder shaping (A−B) dynamics training (B−C) whole loss (A−C)
walker 809.4 (sd 6.5) 806.1 (sd 5.4) 736.7 (sd 39.9) 3.3 — p=0.43, 4% 69.4 — p=0.008, 96% 72.7, p=0.008
cheetah 900.6 (sd 17.0) 817.9 (sd 102.1) 722.7 (sd 114.5) 82.8 — p=0.056, 47% 95.2 — p=0.18, 53% 178.0, p=0.008

Walker is the instrument that can answer this — its arms have sd 5–7, so it resolves a 10-point effect. It says the encoder-shaping channel is worth 3.3 points, 4% of the loss’s value, p=0.43. Essentially zero.

The consistency loss earns its keep by training the dynamics head, not by shaping the representation. Encoder shaping is significant on neither task (p=0.056, p=0.43); dynamics-head training is significant on walker (p=0.008) and is the larger share on both.

Two corrections to what this document said earlier today, both from adding seeds:

  1. Cheetah’s arm C moved 656.4 (n=3) → 722.7 (n=5) once seeds 4 and 5 came in at 809 and 835. The quoted split moved with it, 34/66 → 47/53. The n=3 figure was exactly as unreliable as the campaign’s base rate predicts, which is why it was flagged rather than quoted.
  2. I called encoder shaping “the still-interesting half — 83 points on a task where planning is worth ~0”. That does not survive. It is p=0.056 on the noisy task and 3.3 points on the precise one.

What this leaves is sharper than what S1 proposed. Combine it with the campaign’s other two results and a specific mechanism falls out:

planning’s value is in training, not decisions (#1) · the model loss’s value is in the dynamics head, not the representation (here) · yet on cheetah planning is worth ~1.00×

So an accurate dynamics head matters without being searched. The remaining channel it can act through is the reward and value losses, which are computed over the latent rollout at horizon 3. That makes the world model a multi-step credit-assignment device — not a search substrate, and not a representation regulariser. That claim is specific, falsifiable, and directly testable by varying the horizon of the value/reward losses independently of the planner’s horizon.

The credit-assignment mechanism I proposed above is ALSO refuted (2026-08-11)

Proposed last night, tested overnight, dead by morning. WMP_LOSS_H=K computes the reward and value losses over only the first K rollout steps. At K=1 they use zs[0] = enc(obs[0]) alone, so the dynamics head is removed from credit assignment entirely — while the consistency loss keeps training it exactly as before. Verified before spending: dynamics gradient 0.00025 → exactly 0.0, encoder still learning at 0.0113.

walker arm n mean sd cost vs stock p
A stock (loss horizon 3) 5 809.4 6.5 — —
loss horizon 2 3 804.7 4.0 4.7 0.32
loss horizon 1 5 799.5 14.8 9.9 0.26
B stop-grad encoder 5 806.1 5.4 3.3 0.43
C no consistency loss 5 736.7 39.9 72.7 0.008

Cutting credit assignment to a single step costs 9.9 points. Deleting the loss costs 72.7. Loss-horizon-1 keeps 86% of the benefit and stands 62.7 above no-loss (p=0.016). Not the channel.

But the elimination is now almost complete. The consistency loss’s value survives removing encoder shaping and removing multi-step credit assignment, yet disappears when the loss is deleted. The remaining channel is the planner: the loss buys a dynamics head accurate enough for MPPI to search usefully while the agent is learning.

That does not contradict candidate #1 — it completes it. #1 says bolting a planner on afterwards fails. This says what the model loss buys is the planner’s quality during training. One claim:

search is a training effect, and the world model exists to make search worth doing while the agent learns.

CONFIRMED (2026-08-11): the world model and the planner are ONE mechanism

The 2×2, walker, 400k, n=5 per cell, arms interleaved within every batch:

  consistency loss ON loss OFF value of the loss p
planner on 809.4 (sd 6.5) 736.7 (sd 39.9) +72.7 0.0079
planner off 698.0 (sd 63.9) 715.4 (sd 49.8) −17.4 0.79

INTERACTION = 90.1 points, exact permutation p = 0.0439 (all 63,504 label permutations)

The world-model loss is worth 72.7 points when a planner is present and nothing at all when it is absent. Internal check for free: the planner-off cells (698.0, 715.4) bracket walker’s independently measured never-plan return of 705.4.

With the two alternative channels already eliminated on the same task — encoder shaping 3.3 (p=0.43), multi-step credit assignment 9.9 (p=0.26) — the account closes:

The world model exists to make search worth doing while the agent learns, and search’s value is what it makes the agent learn. They are one mechanism, not two.

That subsumes candidate #1 rather than competing with it, and it explains the campaign’s whole pattern of nulls: every abstraction lever was tested on tasks whose plain policy already worked, i.e. exactly where this mechanism predicts nothing to gain.

REPLICATED on cheetah, and more strongly (2026-08-11)

cheetah, n=5/cell loss ON loss OFF value of the loss p
planner on 900.6 (sd 17.0) 722.7 (sd 114.5) +178.0 0.0079
planner off 904.5 (sd 8.7) 888.9 (sd 23.3) +15.6 0.18

INTERACTION = 162.3, exact permutation p = 0.0187

Two tasks, same direction, both significant: walker 90.1 (p=0.044), cheetah 162.3 (p=0.019). The world-model loss is worth 178 points with a planner and nothing without one.

Cheetah was chosen because it makes the sharpest version of the claim. Its deployment-time planning gain is ~1.00× — search buys nothing when acting — and indeed the planner-off arm here scores higher than the planner-on arm (904.5 vs 900.6). Yet the model loss’s value still collapses without the planner. The planner earns its keep through what it makes the agent learn, even on a task where it is worthless for acting.

An aside that deserves its own line. On cheetah, full TD-MPC2 (900.6) versus an agent with no planner and no world-model loss at all (888.9) is +11.8, p=0.40. Where the planner does not help, the entire world-model apparatus is dispensable. On walker the same apparatus is worth ~100 points, so this is a fact about cheetah, not a general claim — but it is the cleanest statement yet of how task-dependent this machinery is.

What I will not claim. Walker’s p=0.0439 is not overwhelming and its planner-off cells are noisy (sd 64 and 50 against 6.5). On cheetah the planner-ON pair is cross-batch (Aug 8–10) while the planner-OFF pair was interleaved; same box, same config, same code path, but not the same batch — and a cross-batch stand-in already produced one wrong reading this week. Elimination plus interaction is still weaker than a direct demonstration. Two tasks is two, not many.

The superseded plan, kept for the record: turn the planner off and ablate the loss there (mpc=false, consistency_coef 20 vs 0, walker, n=5 each, arms interleaved within every batch). If the channel is the planner, the 72.7 largely disappears. If the loss is still worth ~72 with no planner anywhere, the elimination argument is wrong and all three channels are eliminated — which would be a genuinely puzzling and reportable result in its own right.

The n=4 reading (superseded, kept for the record)

contrast what it isolates Δ perm p
A − B the consistency loss shaping the encoder 82.8 0.056
B − C the consistency loss training the dynamics head 161.4 0.054
A − C the whole consistency loss 244.2 0.018

Roughly one third representation shaping, two thirds dynamics-head training — and the split runs against S1. On cheetah the loss’s larger job is making the dynamics head predict well, even though search through that head buys ~1.00×. The dynamics head still feeds the reward and value losses over horizon 3, so “useless for planning” does not mean “useless as a model”.

The arms are also monotone in how much consistency loss the run received, which is the internal check this design gets for free:

656.4 (never) < 842.8 (off at 50k) < 900.6 (stock)

That ordering independently supports the front-loading result (#5): a loss you drop at 50k costs 58 points, one you never have costs 244.

What survives. Not “world models are representation learners”. Instead a decomposition that nobody has published: the consistency loss has two separable jobs, they can be measured independently, and on this task neither dominates. Encoder shaping being worth 83 points on a task where planning is worth ~0 is still the interesting half — that value cannot be flowing through search.

Honest limits. C is n=3; the 34/66 split rests on it and could move materially. A−B is p=0.056 — the effect held its direction and magnitude from n=4 to n=5 (−99.1 → −82.8), which seven of eight patterns in this campaign failed to do, but it is not significant and I am not calling it so. Arm B’s spread is 6× the control’s (sd 102 vs 17).

A correction, made the same day. At n=4 I reported B as “landing at the level of deleting the loss outright”. That was wrong: the comparator I used (ccoff@50k, 842.8) is not deleting the loss outright, it is deleting it at 50k. The real delete-outright arm is 656.4, and B is well above it. The within-batch control is what caught this — which is why it was run.

Why ICLR still takes it: a falsifiable, counterintuitive claim about a whole class of methods, decided by an ablation anyone can rerun — and the ablation worked. Both outcomes publish, and this is the second one.

(Tooling: repro/cc_stopgrad.patch.py, repro/verify_stopgrad.py. The verification harness itself failed twice first — it read .grad after the optimizer had zeroed it, then recorded the second clip_grad_norm_ call, which fires after optim.zero_grad() in update_pi. Both read as a dead patch. The rule that caught it: verify the mechanism, never the log line.)

S2 — Train the model on the query measure, not the visitation measure · method

From §6.3. Measure first, the gap nobody reports: log the model’s k-step error separately on (a) visited transitions and (b) the latents MPPI actually queried during search. If (b) ≫ (a), the planner has been searching a model that is wrong exactly where it looks, and the size of that gap should predict how much planning is worth across tasks.

Then the method follows: draw the model-loss batch from MPPI’s rollout latents rather than from the buffer alone — a change to which states get gradient, with an argument that is not “circularity”. Kills it: error on queried latents is no worse than on visited ones.

S3 — Coverage decides whether a frozen model is searchable · theory + method

From §6.1. Train the same model three ways — self-collected, broad exploratory, demonstrations — then run the identical deployment toggle on each, with off-distribution model error as the mediating variable. Supplies the missing piece of the pretrained-world-model agenda: the condition under which a frozen world model can be planned through. Highest fashion, highest null risk.

S4 — The demonstration crossover · finding + method

From §6.2. Sweep N demonstrations upward, comparing BC / BC+planner / RL+planner / RL. There is a crossover; locating it is the contribution — “how many demonstrations make your planner pointless.” Partly defensive: it supplies the denominator #1 currently lacks.

6.5 What this does to the §5 recommendation

§5 stands — #1 is still the paper — with two amendments:

  1. State the scope. #1 is a claim about online MBRL with self-collected data, and §6.1 belongs in the paper as the boundary condition plus a prediction, not as a caveat buried in limitations.
  2. S1 outranks #12 as the next experiment. Both are mechanism work for #1, but S1 costs a day against #12’s four, its supporting evidence is already collected, and it publishes either way.

Betting order: S1 → S2 → S4 → S3. S1 because a cheap ablation can flip a widely held belief; S2 because it is the better method paper if the mismatch is real; S4 because the baseline has to exist before review; S3 last because it is the most likely to end in a null.

Every number here is read from logged JSON/CSV in SuuTTT/world-model-paper under data/, with per-seed values. The corrections — including two of mine from this week, and the retracted “circular dependency” framing in §6.3 — are in git history rather than edited away.