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Under review as a conference paper at ICLR 2027

Invent the Questions, Compile the Consequences: Learning Executable Structure from Terminal Feedback

Abstract

Can terminal feedback reveal not only a computation's outcome, but also the structure needed to execute and revise it? We study replayable tool systems with hidden states, unknown action targets, and no intermediate observations. Under explicit projective and identifiability conditions, we recover action-aligned coordinates, call laws, and functional dependencies from experiments that each return a scalar. Our central construction uses measured action relations to align state decoding and tool dynamics in one representation. For type-A actions, we recover matrix multiplication from a noisy measured Lie bracket and extract this representation using a spectrally separated anchor. The calibration has explicit perturbation bounds and polynomial complexity in dimension and conditioning parameters, without initialization near the unknown solution. Complementary reset constructions expose local information without assuming independent state control. For one-dimensional records, suitable reset conditions identify bounded-degree complete maps without requiring an open set of jointly reachable states. When stage outputs are retained as final records, additional local-law conditions permit recovery of local laws and minimum parent sets without expanding the composed program. After acquisition and initialization, the learned interface evaluates unseen legal sequences of learned tools and propagates argument edits within a fixed schedule without further terminal queries. Finite-noise guarantees account for discovery, conditioning, and error amplification during execution. Together, these results show how the execution interface itself can be learned from terminal feedback under explicit structural conditions.

Primary area:
learning theory
Keywords:
representation learning, system identification, identifiability, experimental design, Lie algebras, terminal feedback, compositional models

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_WKS2OpenReview ↗
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3(+1)
Confidence
3
Informativeness
2
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2
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Paper summary

This paper studies how to learn executable structure in a black-box system from scalar terminal feedback when internal states, action targets, and intermediate outputs are hidden. It develops two identification routes: one uses action relations to recover state decoding and tool dynamics in a common representation; the other uses selective resets to identify functional laws without independent control of every state variable and recovers local dependencies under additional assumptions.

The paper provides guarantees for noisy calibration, conditional identifiability, and execution error. Separate synthetic experiments examine structural recovery, adaptation to new objectives with frozen dynamics, query design, and computation updates. These results support the feasibility of learning and reusing executable structure under the stated conditions.

Critical strengths
  1. The paper provides a concrete recovery procedure with error control. Theorem 4.2 addresses noisy measurements that need not satisfy exact Lie algebra identities, giving a construction for recovering a common representation and explicit perturbation bounds without requiring initialization near the true solution. This goes beyond an existence result.

  2. The paper connects identification mechanisms to structural reuse. It analyzes non-identifiability under a restricted query language and demonstrates benefits when adapting to new scoring objectives with frozen dynamics. For example, at a noise level of 10-8 and with 16 additional observations, top-1 selection accuracy is 99.4%, compared with 85.2% for direct fitting with an additive readout. This supports the usefulness of the recovered representation beyond fitting the acquisition objective.

Critical weaknesses
  1. The robustness of the complete discovery pipeline remains insufficiently validated. The main experiments supply the dimensions, a spanning design, and the readout class. Appendix F.2.6 shows that, without supplied dimensions, the original discovery procedure returns a complete result in only 7 out of 72 trials at a noise level of 10-6. The supplementary rule improves recovery of dimension labels, but the paper explicitly notes that these labels alone do not provide a stable factor representation or a qualified executor. The reuse advantages in the main experiments therefore do not yet establish reliable performance of the complete discovery pipeline.

  2. The independent practical benefit of recovering local dependencies remains unclear. In Appendix F.6, whole-map models using the same learned coordinates retain most of the decision benefits; in Appendix F.7, checkpointing is faster than local propagation. The authors report these limitations candidly, but the evidence primarily supports reuse of learned coordinates and laws. It does not clearly establish the additional practical value of recovering minimum parent sets. The theoretical benefit of avoiding exact composition expansion should also be distinguished from the performance of whole-map approximation at finite precision.

Questions for authors
  1. Without supplied dimensions, and with discovery failures or abstentions included in all attempted runs, do the gains on new objectives reported in the main experiments persist? Can the existing results support a success rate for the complete pipeline from discovery to reuse, together with the total acquisition cost?

  2. Do any existing experiments isolate the additional benefit of local parent recovery over a whole-map model in the same coordinates combined with checkpointing? If the current contribution is primarily theoretical identifiability rather than a practical performance advantage, please clarify this scope.

5 comments
AuthorsOpenReview ↗

Response to Reviewer WKS2 (1/3): from discovery to reuse

Thank you for recognizing Theorem 4.2's constructive calibration and the reuse evidence, and for two precise distinctions: reuse of an identified model versus reliable discovery, and local identification versus practical savings. In short:

  • W1 and Q1. Yes, in the main two-factor family at every tested noise level. In the paper, all 168 attempted closed-loop cells at noise 0, 10⁻¹⁰ and 10⁻⁸ discover the dimensions and keep the reported gains (including the 99.4% versus 85.2% at 10⁻⁸ that you cite), with a budget of 1,267,312 endpoints plus 16–256 reads per new objective. New experiments on fresh worlds with a revised discovery rule, each fixed in advance and counting every attempt, extend this to 10⁻⁷ (all 72 cells complete; gain 14.2 points) and to 10⁻⁶, where the learner repeats reads only when that rule abstains (all 144 cells complete; gain 6.0 points, at 1.04 times the fixed-design cost). No cell at any level returns a wrong dimension. A further new experiment keeps a significant gain at 10⁻⁸ and 10⁻⁷ with 17% of the budget.
  • W2 and Q2. On the same decoded pairs, local laws are more accurate than the paper's whole-map model in the same coordinates (a new world-level test: lower mean edit error in 14 of 19 worlds, p = .009). As you suggest, we position this part primarily as an identifiability result.

W1 and Q1: removing supplied dimensions. In the original two-factor family, F.2.6 infers the total action dimension, number of factors and factor sizes before the corresponding acquisition steps; it can abstain. At the tested noise levels 0, 10⁻¹⁰ and 10⁻⁸, Table 7 reports 24/24, 72/72 and 72/72 complete dimension outputs. These 168 attempted cells come from 24 independent worlds, which our intervals resample. The spanning-raw design and readout class are supplied in these cells; our next comment removes the readout class and explains the design.

F.2.6 also reports that correct dimensions leave subsequent queries unchanged and that replayed acquisition observations match the original cells exactly. Consequently, at these tested levels, the downstream frozen models and new-objective evaluations are unchanged when dimensions are discovered. All attempts are included. At 16 new reads, top-1 is 100.0%, 100.0% and 99.4%, versus 84.4%, 84.7% and 85.2% for additive direct fitting. The paired gains are 15.6, 15.3 and 14.1 percentage points, with world-bootstrap 95% intervals [12.6, 19.1], [12.2, 18.8] and [11.4, 17.3]. On top-1, construction beats both direct-fit readouts (additive and bilinear) in every world at every read budget at these noise levels. The direct-fit control retains its known dimensions.

New experiment: the closed loop on fresh worlds. To test the complete pipeline beyond the paper's cells, we ran it from discovery to new-objective decisions on 24 worlds that no earlier study had used, at noise 10⁻⁷ and 10⁻⁶ (72 cells each). The worlds, the discovery rule and the analysis were fixed before any of these worlds was generated, and the scripts were first checked to reproduce stored cells of the paper exactly. The rule replaces the paper's ratio gates: it counts the singular values above the paper's noise floor, abstains when a rejected one comes within a factor of two of it, and then applies the count identity of F.2.6, which fixes the factor sizes when the dimension is 16. It adds no query. The direct-fit control keeps its supplied dimensions.

At 10⁻⁷, a level the paper's motion experiments had not tested, all 72 cells return the correct dimensions. With every attempt counted and 16 new reads, the closed loop reaches 97.0% top-1 against 82.8% for direct fitting: a gain of 14.2 points (world-bootstrap 95% interval [10.3, 19.2]), positive in all 24 worlds and equal in size to the paper's gain at 10⁻⁸. With 256 reads it is 97.8% against 83.7%.

Our next comment gives its 10⁻⁶ results and a second experiment that repeats reads where this rule abstains.

The revision reports the closed-loop results, their cost and the 10⁻⁶ results in Section 7 (page 9), and the new experiments in Appendices F.2.12–F.2.15 (Tables R5–R8, pages 54–57).

AuthorsOpenReview ↗

Response to Reviewer WKS2 (2/3): noise 10⁻⁶ and the supplied priors

We first complete Q1 at 10⁻⁶, then address the two priors that the noisy motion study supplies, the readout class and the spanning-raw design.

Noise 10⁻⁶: the revised rule, with repeated reads where it abstains. At 10⁻⁶ the paper's discovery mostly abstains and never returns a wrong dimension (Table 7: 7/72 complete). On the 24 fresh worlds of our previous comment, the revised rule with single reads completes 63 of 72 cells at 10⁻⁶ and returns no wrong dimension either; its nine abstentions are three worlds whose weakest action direction lies below the noise floor, and with them counted the all-attempt gain does not extend to 10⁻⁶. A second experiment, again fixed in advance, keeps the revised rule of our previous comment and lets the learner average R = 2, 4, 8 or 16 reads per endpoint only where that rule abstains, charging every read; new-objective reads stay single reads at 10⁻⁶. On 48 further worlds whose factors no earlier study used, all 144 cells at 10⁻⁶ return the correct dimensions (138 already with single reads, 6 with two) and every construction returns, so each cell yields an executor scored on new objectives, not dimension labels alone.

With every attempt counted, 16 new reads give 89.9% top-1 against 83.8% for the direct fit trained, as in the paper, on that level's acquisition prefix and validation reads: a gain of 6.0 points (world-bootstrap 95% interval [3.9, 8.3]; ahead in 39 of 48 worlds; 6.5 points [4.3, 8.8] against a bilinear direct-fit readout), at a mean cost of 1,320,015 acquisition endpoints per cell, 1.04 times the fixed design.

Applied post hoc, the same rule also completes all 72 fresh cells of our previous comment (nine with two or four reads; gain 3.3 points [0.8, 6.0]) and all 72 of the paper's own cells at 10⁻⁶ (three with two reads; gain 5.4 points [2.6, 8.5]); since its one constant was chosen on the paper's cells, the test fixed in advance is the one above.

The readout class can be removed. The constructed states and dynamics come from first-order and bracket responses; the readout class enters only the final readout fit. A new experiment therefore replaces it, in the main noisy study, by the Gaussian-kernel ridge of F.2.5, which assumes no parametric form for the score. We froze the constructed models of the paper's 72 cells at 10⁻⁸ and of the 72 fresh cells at 10⁻⁷ and refitted only this readout; the direct fit keeps its supplied class. Since discovery returns the correct dimensions in all these cells, this is the closed loop with neither the dimensions nor the readout class supplied. With 256 new reads it reaches 95.7% top-1 against 85.2% at 10⁻⁸ (gain 10.4 points [7.7, 13.6], ahead in all 24 worlds) and 91.6% against 83.7% at 10⁻⁷ (7.9 [4.1, 12.2]); at 10⁻⁸ it already leads in 22 worlds and trails in none with 128 reads. The readout class is thus a sample-efficiency prior rather than a requirement: it is what lets 16 reads suffice.

The CIFAR-10 worlds of F.2.5, whose score is a frozen classifier, show the same: discovery returns 12/12 (Table 7), and for nine new class-score objectives the kernel readout on 512 reads (.04% of the acquisition) gives 96.4% top-1, versus 41.0% for a readout that erases call order (F.2.2).

The spanning design. This prior is a richness condition on the tools, not knowledge of them: the raw tool directions span the action algebra, so the bracket table can take raw tools as pivots. The learner is not told which tools these are or what they do; a pivoted solve selects 16 of the 18 raw directions from the replies. Tool sets that reach some directions only through brackets are covered by the general construction: the Hall entrance takes depth-two bracket words as pivots (Section 4.1, Appendix A.1), and Appendix A.2 gives a repeated-word alternative. Appendix E (Theorem E.1) proves this for a family with randomly drawn parameters in which as few as 2q − 1 tools act on a record with q² − 1 action dimensions: the depth-two brackets span the full algebra almost surely, and the interface is learned from polynomially many reads.

AuthorsOpenReview ↗

Response to Reviewer WKS2 (3/3): acquisition cost and local-parent recovery

Acquisition accounting. Dimension discovery uses the already-acquired first-order and bracket observations; it adds no discovery-specific online probes in this main closed-loop setting. The learner's budget is:

  • 1,254,528 first-order/bracket endpoints, including the 1,244,160-endpoint dense bracket design;
  • 12,272 other acquisition endpoints, including 256 noise probes;
  • 512 validation endpoints, which construction does not use.

This totals 1,267,312 endpoints before the 16–256 reads for each new objective. Because correct dimensions leave every subsequent query unchanged (F.2.6), the closed-loop learner pays exactly the supplied-dimension budget. In these 168 cells, the direct-fit control is trained on the original acquisition prefix and validation reads: 1,267,056 endpoints.

The gain does not need this budget. A new experiment reran the complete pipeline with fewer contexts and derivative nodes, discovery (the revised rule) included and charged, every attempt counted, against the direct fit trained on its full acquisition. With 32 contexts and 5 nodes the closed loop uses 212,208 endpoints, 17% of the direct fit's; all 144 cells return the correct dimensions, and the gain at 16 new reads is 12.2 points [9.6, 15.0] at 10⁻⁸ (97.4% against 85.2%, ahead in all 24 worlds) and 7.9 [4.3, 11.9] at 10⁻⁷. With 64 contexts and 5 nodes (407,088 endpoints, 32%) it is 13.7 and 12.7 points, close to the full design's 14.1 and 14.2.

A second complete pipeline (Q1). Q1 also asks for a success rate and total cost from existing results. Besides the motion pipeline above, the paper's reset-route service (Appendix F.5) runs from unknown-target discovery to query-free decisions, under its stated public forms and complexity bounds. It uses 49,577 endpoints. With the reported numerical fallback, 19 of 20 attempts complete at each tested noise level 10⁻⁷, 10⁻⁶ and 10⁻⁵ (the twentieth abstains), with exact parents and payload writes in all 57 completions. On two planning tasks at 10⁻⁵, the deployed models' mean regret is 79 to 260 times lower than that of a GRU/MLP predictor or direct screening, each given 50,000 endpoints for the two tasks together, and lower than both in each of the nineteen completed worlds (Table 13).

W2 and Q2: local laws versus the whole-map model. On the same decoded pairs, local laws are the more accurate model, and a new world-level test of the stored records shows that this holds across worlds: in F.7 their mean edit error is lower in 14 of 19 worlds (Wilcoxon p = .009), with 29 against 65 of 1,824 edits above the 10⁻³ error threshold, and their plan regret averaged over the two F.6 tasks points the same way (lower in 12 worlds, higher in 5; p = .045). The speed advantage stays with whole-map checkpointing (F.7), so these tests show higher accuracy, not an operational speedup.

Theorem 5.2 is therefore best read as an identifiability result. It answers a distinct structural question: from the permitted preparations, it identifies the internal local laws and unique minimum parent sets without expanding the composition. As you note, this theoretical benefit should be distinguished from finite-precision whole-map approximation: the exact-degree example explains a representation cost, not an approximation lower bound. The demonstrated decision benefit comes from the learned coordinates and laws. The revision states this scope in Sections 5.2, 7 and 8 (pages 7 and 10); our general response gives the theorem-to-experiment map.

Thank you for asking that discovery failures and abstentions be included in all attempted runs: the new closed-loop experiments were built around exactly that count.

Reviewer_G36vOpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
2
Soundness
3
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Paper summary

The paper studies when replayable systems with hidden records and unknown action targets can be converted into executable models using scalar terminal observations. Its main algebraic construction recovers a common representation for state decoding and tool dynamics from a noisy type-A Lie bracket, using an invariant cubic to reconstruct multiplication and a separated anchor to extract the defining representation. Separate reset-based results characterize information lost by grouped queries, identify bounded-degree complete maps from lower-dimensional preparations, and recover local laws under retained-output and nondegeneracy assumptions. Learned laws support query-free execution and fixed-schedule updates after acquisition and initialization. Synthetic experiments test calibration, frozen-dynamics transfer, reset information, and maintenance, with different experiments exercising different subsets of the theoretical contracts.

Critical strengths
  1. A substantive constructive calibration result. Theorem 4.2 and Appendix A.4 address measured tables that need not satisfy Jacobi, rather than assuming an exact Lie algebra or an initialization close to the desired representation. Recovering the symmetric product through the invariant cubic, then extracting a left ideal through right multiplication, gives a concrete route to compatible state and action coordinates with explicit conditioning dependence. Theorem 4.1 explains why this common representation also fixes physical-duration scaling. This is the strongest reason for acceptance.

  2. The reset results clarify an actual identifiability boundary. The grouped-query cubic kernel and the nested-preparation construction distinguish a lack of information from an optimization failure. The local-law result further separates recovering a composed map from recovering its stages. The empirical discussion is unusually careful about what these results do and do not imply: it retains failures, charges acquisition, and reports where whole-map models or checkpointing are competitive.

Critical weaknesses
  1. There remains a substantial gap between the conditional recovery theorems and a single demonstrated acquisition-to-execution procedure. The motion route needs projective type-A structure, visibility, excitation and a compatible native frame; the reset/local-law routes instead require specific reset separation, retained outputs, and own-source nondegeneracy. The principal noisy motion experiment supplies dimensions and a spanning raw design and does not test native payload dictionaries or program recovery. Conversely, the larger native-compilation study uses population endpoints, and its finite-noise implementation is reported unstable. The paper acknowledges these distinctions, but their combined effect limits how broadly the headline claim can be applied. The main text would benefit from making the exact theorem-to-experiment coverage directly inspectable.

  2. The quantitative guarantees currently provide limited guidance at practical noise and cost levels. Appendix F.1 gives a representative sufficient noise radius of 5.52×10^-18 and an amplification bound of 1.13×10^16, while observed behavior is much better. The main scalar-acquisition study uses 1,266,800 endpoints before validation. Thus the theorem is meaningful as a polynomial, conditioning-dependent existence/construction result, but its constants do not certify the demonstrated operating regime. Moreover, Appendix F.6 finds that whole-map fits retain much of the decision benefit, and F.7 finds checkpointing faster than local propagation. These results leave the incremental operational value of recovering parent structure less established than the value of recovering reusable coordinates and dynamics.

Questions for authors
  1. Scope clarification: Could you provide a compact table mapping each main theorem to its supplied priors, independently required identifiability conditions, recovered objects, and actual experimental implementation? In particular, which demonstrated pipeline combines unknown-target discovery, native-coordinate recovery, local-law identification, and noisy deployment without evaluator-provided coordinates? This would materially clarify the end-to-end claim.

  2. Quantitative clarification: Can the stability analysis be specialized to the experimental family to yield a non-vacuous sufficient tolerance, or can you identify which steps cause the largest gap between the theoretical radius/amplification and the measured behavior? I do not require an optimal uniform bound, but this affects the strength of the finite-noise contribution.

  3. Contribution clarification: Is there an evaluated regime where recovering local parents provides a clear benefit over a whole-map model in the same learned coordinates and a checkpoint baseline, after acquisition and initialization are included? If not, I would regard that part primarily as an identifiability result, with the demonstrated practical benefit attributed to coordinate/dynamics recovery.

3 comments
AuthorsOpenReview ↗

Response to Reviewer G36v (1/3): theorem coverage and the end-to-end pipeline

Thank you for the close reading of the construction. Your review follows Theorem 4.2 from the invariant cubic to the separated anchor, and it names what the reset results are for: they "distinguish a lack of information from an optimization failure."

W1 and Q1: theorem coverage and the end-to-end pipeline.

The table you asked for is in our general response, with your four columns: supplied priors, independently required identifiability conditions, recovered objects and experimental implementations. It also answers what the other two reviews ask about the supplied information and about how the results fit together. The two acquisition routes have different contracts, so we answer the four-stage pipeline question for each.

Reset route (Appendix F.5). The Brier service combines unknown-target discovery, native-coordinate recovery, local-law identification and noisy query-free deployment, without evaluator-provided coordinates, in a finite-value family. Its public priors are native forms, five records, signature weight six, local/payload degree two and indegree at most one. Labels, groups, assignments, coordinates, rates, reset constants and coefficients are hidden. Scalar signature discovery and calibration/decoding precede joint acyclic parent selection.

Full acquisition uses 49,577 endpoints within a 50,000 cap. At each tested σ ∈ {10⁻⁷, 10⁻⁶, 10⁻⁵}, the fixed-cubic procedure with numerical fallback completes 19/20 acquisitions; all 57 completions recover exact parents and payload writes. Deployment makes no queries. F.6 evaluates this deployment at σ = 10⁻⁵ on two planning tasks: the deployed models' mean regret is 1.16×10⁻⁵ (plan choice) and 4.22×10⁻⁶ (call order), against 9.19×10⁻⁴ and 1.10×10⁻³ for a validation-selected GRU/MLP and 1.22×10⁻³ and 5.57×10⁻⁴ for direct screening, each given 50,000 endpoints for the two tasks together, and it is lower than both in each of the nineteen completed worlds (Table 13). A separate calibration-degree-selection follow-up uses twenty worlds, two fresh noise streams and σ ∈ {10⁻⁶, 10⁻⁵}: selected degree completes 80/80 attempts with correct parents/writes.

Motion route (Appendix F.2/F.2.6). Dimension discovery returns correct n, m and every q_f in 168/168 closed-loop cells at the tested σ ∈ {0, 10⁻¹⁰, 10⁻⁸}, from 24 independent worlds (24 + 72 + 72 cells); a new closed-loop experiment on 24 fresh worlds, with a revised discovery rule fixed in advance, adds 72/72 cells at 10⁻⁷ with an all-attempt new-objective gain of 14.2 points, and a second one, repeating reads only where that rule abstains, completes 144/144 cells at 10⁻⁶ on 48 further worlds with a gain of 6.0 points (see our response to WKS2). The subsequent pipeline performs constructive calibration, noisy scalar acquisition and query-free reuse. It supplies the spanning raw design and, in its main form, the readout class, which a new experiment removes (see our response to WKS2); native coordinates, payload writes and local parents are recovered in the reset-route service above rather than here, and F.9 demonstrates native compilation at population endpoints.

Thus the fully joined pipeline is the reset-route service; the motion results support compatible coordinate/dynamics recovery and reuse under their separate assumptions. The revision places a compact form of the coverage table (Table R1, page 8) and this distinction in the main text (Section 7), with the full table at the start of Appendix F (Table R2, page 38).

AuthorsOpenReview ↗

Response to Reviewer G36v (2/3): stability constants, stage by stage

W2 and Q2: quantitative stability and the gap to observed behaviour.

To answer both parts, we re-ran the six F.1 instances at (q, K, H, χ, γ) = (3, 2, 4, 2, 1) on the same noisy tables and recorded every intermediate object of the construction (22)–(26) against its exact counterpart. This instrumented run is new. Its end-to-end error is 0.17η (median, after the alignment of F.1), against the .18η reported there.

Which steps cause the gap? The recurrences (27)–(28) give a₁ = 1.13×10¹⁶, and the output-cap condition η ≤ (2K³a₁)⁻¹ sets η₀ = 5.52×10⁻¹⁸. The table compares the proven constant of each stage with the measured error divided by η, at η = 10⁻⁸ (median and range over the six instances; U and ρ are compared after aligning orthonormal bases):

StageProven constantMeasured error / η
Killing form Bb₁ = 42.80.39 [0.30, 0.43]
Invariant cubic Tt₁ = 1.54×10³0.099 [0.080, 0.108]
Inverse solve (raw product)j₁ = 1.37×10⁴0.15 [0.10, 0.18]
Trace product Cc₁ = 1.23×10⁵0.014 [0.010, 0.025]
Scale ss₁ = 2.01×10⁶0.0015 [0.00015, 0.0064]
Normalized product Jj₂ = 1.42×10¹¹0.65 [0.55, 0.82]
Right multiplication Rr₁ = 7.09×10¹¹2.3 [1.7, 3.0]
Anchor subspace Uu₁ = 4.08×10¹⁴0.83 [0.16, 1.02]
Representation ρa₁ = 1.13×10¹⁶0.84 [0.34, 1.95]

The measured error stays below 3.1η at every stage (below 11.5η over all 24 F.1 instances), and each ratio is the same at η = 10⁻⁸ and 10⁻⁴ to within 0.06%. The proven constant, in contrast, grows by fourteen orders along the chain. Relative to the measured stage errors, the bound loses about three orders in the anchor-subspace stage and about two orders at each of five stages: the Killing form, the invariant cubic, the trace product, the scale estimate and the scale normalization. No single step explains the gap.

Can the analysis be specialized to give a non-vacuous tolerance? Yes, a posteriori. Proposition A.4 bounds the error of an output from two quantities the learner can compute: the output's own norms and its bracket residual on the noisy table. If S, the output and their inverses have norm at most K′, and the residual r plus the table error η is at most (256q²K′³)⁻¹, the error is at most 4qK′⁶(r + η). With the measured values on the same six instances (K′ = 2.0–3.5, r = 1.5–2.0η):

  • the certificate holds at every tested table error from 10⁻¹⁴ to 10⁻⁶ on all six instances, against η₀ = 5.52×10⁻¹⁸;
  • at η = 10⁻⁸ the certified amplification is 1.2×10⁴ (median; at most 5.2×10⁴), against a₁ = 1.13×10¹⁶, so the certified error is at most 5.2×10⁻⁴; the measured end-to-end error is at most 2.7×10⁻⁹.

Certification thus reaches table errors eleven orders beyond η₀, and the amplification improves by about twelve orders, closing most of the seventeen-order gap between a₁ and the measured amplification; in the 210 runs where the certificate applies (four (q, K) pairs) the measured error never exceeds it. As an a posteriori bound, it certifies a computed output rather than predicting success, and like Theorem 4.2 it takes the norm cap and the table-error bound η as input. Specializing the a priori constants instead, by substituting the instances' actual singular gaps and scale for the proof's three worst-case lower bounds, lowers a₁ to 2.5×10¹²; those values are known only to the evaluator, whereas the certificate uses quantities the learner computes.

What F.1 already reports. The output norm caps 2K³ that the output-cap condition guarantees hold in every run with η ≤ 10⁻¹. Error remains proportional to η from 10⁻¹⁴ to 10⁻², fifteen orders of magnitude beyond η₀, with median amplification .18 (.12–.53 across the four (q, K) pairs), seventeen orders below a₁. At η = 10⁻⁸, sampled exponents are K^2.31 and K^2.89 (q = 3, 4) against bound exponents K^30.9 and K^31.0, and χ^.21 and χ^.43 against χ^2.22 and χ^2.57; over a sixteenfold γ range the error changes by only 5×10⁻⁷ relatively, whereas the bound scales as γ^−.78.

Finally, η bounds bracket-table/anchor error, whereas σ is scalar-endpoint noise; the two are related through acquisition and differentiation. The revision adds the stage-by-stage comparison (Table R3, page 40), the a posteriori certificate (Table R4, page 41) and the η/σ distinction to Appendix F.1.

AuthorsOpenReview ↗

Response to Reviewer G36v (3/3): acquisition cost and local parents

Acquisition cost (W2). The main scalar study uses 1,266,800 endpoints before validation; the dense bracket design accounts for 1,244,160 = 162·64·C(16, 2). A new experiment shows that the reuse gain does not need this budget. We reran the complete pipeline with fewer contexts and derivative nodes, with dimension discovery (the revised rule of our first comment) included and charged and every attempt counted, on the paper's 72 cells at 10⁻⁸ and on 72 fresh cells at 10⁻⁷; the direct fit keeps its full acquisition. With 32 contexts and 5 nodes, 212,208 endpoints in total (17%), 16 new reads give 97.4% against 85.2% top-1 at 10⁻⁸ (gain 12.2 points [9.6, 15.0], ahead in all 24 worlds) and 90.7% against 82.8% at 10⁻⁷ (7.9 [4.3, 11.9]). With 64 contexts and 5 nodes, 407,088 endpoints (32%), the gains are 13.7 and 12.7 points, against 14.1 and 14.2 at the full design. In this family (n = 16) this lowers the constants of the bracket design 162·64·C(16, 2); the general design 162·max(64, 3n)·C(n, 2) stays polynomial in n.

Q3: local parents versus the whole-map model.

In the evaluated comparisons, local laws are more accurate, not faster. On the same decoded pairs, a new world-level test of the stored records gives local laws a lower mean edit error in 14 of 19 worlds in F.7 (Wilcoxon p = .009; 29 against 65 of 1,824 edits above the 10⁻³ threshold), and their plan regret averaged over the two F.6 tasks points the same way (lower in 12 worlds, higher in 5; p = .045).

We agree with your positioning of this part primarily as an identifiability result. Under retained-output and own-source nondegeneracy conditions, Theorem 5.2 recovers the unique minimum parent sets and local laws without expanding the composed map. The demonstrated practical benefit is better attributed to reusable coordinate/dynamics recovery. The revision states in Sections 5.2 and 8 (pages 7 and 10) that Theorem 5.2 is an identifiability result, and in Section 7 (page 10) that the demonstrated benefit is the reuse of recovered coordinates and laws.

Thank you for questions that could each be answered by a table or a test; they made the paper's scope easier to state precisely. If another layout would make the coverage table easier to inspect, we would value your suggestion.

Reviewer_ieJ1OpenReview ↗
Rating
2(+1)
Confidence
2
Informativeness
1
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Soundness
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Paper summary

The paper studies recovering an execution interface from terminal feedback under explicit projective and identifiability assumptions. It considers two mechanisms in distinct settings: relations between tool actions and reset experiments. The paper claims that, under these assumptions, carefully designed experiments returning only scalar terminal feedback can reveal hidden computational structure, including states, tool dynamics, and functional dependencies.

Critical strengths

Inferring hidden structure or states from terminal rewards is of practical interest, as many agentic tasks provide only a single scalar reward at the end. Making better use of this limited feedback could help agents learn about the underlying task and improve their decisions.

Critical weaknesses
  1. I find the paper generally hard to follow. It reads like a dense collection of equations and theorems, without a clear central narrative or sufficient explanation of how the subsections connect. The main takeaway and motivation for each subsection are often unclear, making it difficult to understand how the individual results contribute to the paper’s overall objective.

  2. The theoretical settings also rely on strong structural assumptions, and the experiments use synthetic tools. It remains unclear how closely these assumptions match practical agentic tasks and whether the findings extend to more realistic settings.

Questions for authors
  1. Could the authors provide a concrete running example illustrating the central problem and proposed solution? In particular, what is hidden, what experiments can the learner perform, what does each scalar response reveal, and what can the learned interface subsequently do?

  2. Could the authors clarify how the different theoretical results fit together? Which results belong to alternative settings, and which can be combined into a single learning-and-execution procedure? I found it difficult to identify the main contribution and understand the role of each subsection.

4 comments
AuthorsOpenReview ↗

Response to Reviewer ieJ1 (1/2): the narrative in the revised paper, and a concrete example

Thank you for recognizing the importance of learning from terminal rewards and for asking for a clearer narrative. In brief:

  • Problem. A system has hidden state and tools whose effects are unknown. The learner sees one scalar score at the end of each run.
  • Result. Under explicit structural conditions, by choosing which runs to compare, the learner recovers the hidden state and what every tool does in one consistent model. It can then predict the outcome of new tool sequences without querying the system again.
  • Evidence. After the learning phase (acquisition), 16 reads of a new objective suffice to pick the best of 32 candidate tool sequences 99.7% of the time, against 11.4–58.6% for generic sequence models trained on the same observations (Table 3).

W1: the narrative is now in the paper. The revision places a running example (Section 3), a roadmap (Introduction), a purpose sentence at the start of each of Sections 4.1, 4.2, 5.1, 5.2 and 6, and a compact table of assumptions, recovered objects and experimental coverage (Table R1) in the main text. These additions are in blue on pages 2–8. The running example (Q1) follows below, and the roadmap (Q2) in our second comment.

Q1. What is hidden, and what can the learner ask?

Consider the two-record system in Appendix F.2. Each hidden record has three components whose common scale is irrelevant: only their relative values matter. There are 18 anonymous tools. Each changes one or both records, but the learner does not know which records it affects or how it changes them. The initial states and score coefficients are also hidden. After a sequence finishes, the learner receives just one noisy scalar score, never an intermediate state.

The learner can replay a legal history, append further calls, and choose positive call durations. Every terminal read is charged. It cannot inspect a record, execute an inverse tool, or set an arbitrary hidden state.

What do the replies reveal? One scalar does not identify a record or a tool. Instead, the learner compares carefully related experiments:

  1. Inserting a short call measures how that tool changes the final score at the current hidden state.
  2. Swapping two short calls measures their order-dependent interaction.
  3. The learner repeats such comparisons after many histories and with many follow-up calls, chosen so that their score effects can be told apart. Together they give a table of how pairs of tools interact (a bracket table). The table also shows which records each tool affects.
  4. Theorem 4.2 turns this noisy table into one set of matrices for the tools; Theorem 4.1 then decodes each hidden state in the same coordinates from independent responses at that state. Tools and states therefore share coordinates and the same duration scale.

What can the interface do afterward? Once acquired, it predicts scores of unseen legal sequences with new orders and durations, including the tested lengths up to 32 calls, without querying the service. For a new objective on the same dynamics, only the readout, the map from hidden state to score, is refitted. In F.2's objective-transfer study, 16 new reads at noise 10⁻⁸ give 99.4% top-1 accuracy (picking the best of 32 candidates), versus 85.2% for direct fitting.

A concrete instance (Appendix F.2.5). The two records are the colour balance of the centre and of the border of a CIFAR-10 test image: three channel gains each, of which only the ratios matter. The 18 tools are colour transformations whose targets and strengths are unknown. The only observation is the log-probability that a trained classifier assigns to the image after a tool sequence. From these scalars the learner builds the interface; with a readout fitted on 512 further reads, it picks the best of 32 candidate tool sequences 96.9% of the time, against 45.0% for a readout that erases call order and 3.1% for chance (ahead in all twelve independently generated systems, or worlds).

How do generic sequence models compare? In the 48 runs where these models were saved (24 worlds, noise 0 and 10⁻⁸), a GRU, a Transformer and a linear predictive-state model trained on the same observations reach 20.9%, 11.4% and 58.6% top-1 after refitting a linear output on 16 new reads, versus 99.7% for the constructed interface in the same runs (Table 3). The constructed interface beats each of them in all 24 worlds at every read budget (p < 2×10⁻⁵). This is the benefit you describe: learning the underlying task from terminal feedback so that new decisions need only a few reads.

AuthorsOpenReview ↗

Response to Reviewer ieJ1 (2/2): roadmap, and how the assumptions map to practice

Q2. How do the results fit together?

Section 3 fixes the access rules of our example and the goal: an interface that executes new call sequences and edits as the hidden system would. Two alternative acquisition routes follow, not consecutive stages; both feed one execution layer:

  • Motion route (Section 4). Section 4.1 turns scalar replies into a table of tool interactions without knowing the score function. Section 4.2 turns the noisy table into one representation (Theorem 4.2) and decodes states in it (Theorem 4.1). Theorem 4.2 is our main technical contribution. Measurement noise breaks the exact algebraic identities that a true table satisfies; under the theorem's stated conditions the construction still recovers the representation, with explicit error bounds, and it needs neither a repaired table nor a starting point near the unknown solution.
  • Reset route (Section 5). Selective resets erase chosen parts of the history, exposing how records are computed without controlling each record independently. Section 5.1 identifies complete bounded-degree laws under the reset contract (Theorem 5.1). With retained stage outputs and further local-law conditions, Section 5.2 recovers each stage's law and minimum parent set without expanding the composed program (Theorem 5.2).
  • Execution (Section 6). Either route's learned interface, once initialized, runs unseen legal sequences and argument edits within a fixed schedule without further queries. Section 6 also gives error bounds and costs.

Each route followed by Section 6 gives a complete learning-and-execution procedure. F.2 runs the motion procedure from scalar replies through calibration and decoding to query-free reuse. F.5 runs a finite-value reset procedure whose score is a Brier loss on real images: 19 of 20 test worlds at each tested noise level complete acquisition and recover every parent (the records a step depends on) and every write exactly. Section 7 reports these tests.

W2. Why simulated tools, and what is real? The tools are simulated so that identification can be checked against the true hidden states, tool actions and dependencies, which a deployed agentic system does not reveal. The learner itself never reads the simulator's states, tool definitions or score function; it sees only terminal scores. Two studies add real components. In the classifier instance of our first comment, the same learned dynamics also serve nine new objectives, the classifier's scores for the other nine classes: 512 reads each give 96.4% top-1, versus 41.0% for a readout that erases call order (ahead in all twelve worlds). The Brier study uses real data and a real loss. There the learned model chooses among 1,024 candidate tool sequences per decision. With the same 50,000 reads for two planning tasks together, its mean regret (the loss gap to the best candidate) is 79 to 260 times lower than that of a GRU/MLP predictor or of testing candidates directly. It is lower than both in each of the nineteen completed worlds (Table 13).

How do the assumptions map to practice? Section 3's access model asks that a run can be replayed and extended and that it returns a terminal score; replayable environments, such as simulators or sandboxes that can be restored to a saved state, offer this. The motion route also relies on tools whose call durations can be chosen, and the reset route on selective resets. The conditions of the motion route are not tied to our examples: Appendix E (Theorem E.1) proves that they hold in a family of tool systems with randomly drawn parameters, and that the interface is then learned from polynomially many reads. One safeguard is computed from the learner's own data: when it infers the number and sizes of the records from the replies, it abstains if they do not separate the action directions from noise, and no tested run returned wrong dimensions (F.2.6; our response to WKS2).

Access conditions are not a technicality: Theorem B.4 shows that grouped pair-reset queries cannot see certain cubic score terms, however many replies are collected. In a witness family (Section 7, Appendix F.4), noiseless grouped queries give .522 decision accuracy at matched cost, versus 1.000 when the same calls are interleaved. Hence the title: which experiments the learner runs determines what it can learn.

The central takeaway is that terminal scalars can reveal an executable interface when the action family and the available experiments provide enough structure.

Your Q1 asked what is hidden, which experiments the learner can perform, what each scalar response reveals and what the interface can then do; those four questions gave the example its order, and Q2 gave us the roadmap. Thank you for both.

Reviewer_ieJ1OpenReview ↗

Thank you for the detailed response

I appreciate the running example, roadmap, and coverage tables, which clarify the intended contribution and the relationship between the alternative acquisition routes. However, I am still not fully convinced that the paper communicates its central technical idea and development clearly enough to assess its significance. The connection between its specialized assumptions and practical agentic tasks is also not very clear. I therefore lean toward weak rejection, while acknowledging that the revision addresses part of my original concern.

Thank you for taking the time to revisit the paper and to continue this discussion with us. We particularly appreciate the concrete questions in your review: what each scalar response reveals and how the results fit together. They directly shaped the running example and the roadmap.

The technical idea. A model can predict terminal scores accurately without revealing what each tool does to the hidden state. Our aim is to recover that action structure, so that the learned interface can execute tools in new orders. Scalar comparisons measure how the order of two tools matters: their commutators. With exact commutators, algebra recovers the tools as matrices; measured commutators are noisy and violate the identities this relies on. Our construction recovers an approximate matrix product from the commutator table, then uses an anchor element with well-separated eigenvalues to extract the space on which the tools act as matrices. Theorem 4.2 bounds the resulting error under its stated conditions; the construction needs no starting point near the unknown solution. Theorem 4.1 decodes the hidden states in the same coordinates. After acquisition and initialization, the interface evaluates unseen legal sequences of the learned tools without further terminal queries. With 16 reads of a new objective, it picks the best of 32 candidate sequences 99.7% of the time; generic sequence models trained on the same observations reach 11.4–58.6% (Table 3).

The link to practice. The practical motivation is the situation you highlighted: learning about a task from a single terminal reward. For the motion route, the setting has two parts. Access: runs can be replayed and extended, as restorable simulators or sandboxes offer, and call durations can be chosen. Structure: each tool acts linearly, up to scale, on the records it affects. In the image instance of Appendix F.2.5, the records are the colour balance of two regions of an image, the tools are colour transformations, and the terminal score is a trained classifier's output. The motion route's conditions also hold in a family of tool systems with randomly drawn parameters (Theorem E.1).

We will carry both statements into the Introduction of the final version.

Comments on the paper

3 comments
AuthorsOpenReview ↗

General response (1/2): the contribution and its demonstrated scope

We thank the reviewers for identifying both the mathematical contribution and the explanations needed to assess it.

The question. A tool system has hidden state, and the learner sees only one scalar score at the end of each run. Can it learn a model that executes new tool sequences without querying the system again?

The answer. Yes, under explicit structural conditions, by designing which runs to compare. The scalar replies are first assembled into a table of how pairs of tools interact. Theorem 4.2, the constructive calibration that Reviewers WKS2 and G36v highlight, turns this noisy table into one representation in which states and tool actions agree, with explicit error bounds and without near-truth initialization, even though a measured table may violate the exact algebraic identities (Jacobi) of a true one. Theorem 4.1 then decodes states and applies tools in that representation.

The benefit. The learned structure is reusable when the scoring objective changes. With 16 reads of a new objective at noise 10⁻⁸, the constructed interface reaches 99.4% top-1 accuracy at picking the best of 32 candidate sequences, versus 85.2% for direct fitting. In the 48 runs where generic sequence models were saved (σ = 0 and 10⁻⁸), with only a readout refitted in every model, the same 16 reads give 99.7%, versus 58.6% for a linear predictive-state model, 20.9% for a GRU and 11.4% for a Transformer trained on the same observations (Table 3); construction beats each of them in all 24 worlds at every read budget. This is the paper's central distinction: identifying an execution interface, as opposed to only fitting a score predictor.

There are two alternative acquisition settings. Section 4 uses relations between tool actions (projective type-A motion). Section 5 uses selective resets to identify complete laws, or local laws when stage outputs are retained. They have different assumptions; they are not successive stages of one universal learner. Section 6 uses the identified coordinates and laws for query-free execution and fixed-schedule edits after acquisition and initialization.

The evidence answers two different end-to-end questions.

Motion route (Section 4). In the original two-factor motion family, F.2.6 removes supplied dimensions at the tested noise levels 0, 10⁻¹⁰ and 10⁻⁸: all 168 attempted cells (a cell is one world at one noise level and repeat) across 24 independent worlds return the dimensions and retain the original downstream queries and observations. At 16 new-objective reads, construction reaches 100.0%, 100.0% and 99.4% top-1, against 84.4%, 84.7% and 85.2% for the additive direct fit. At 10⁻⁶ the paper's discovery abstains instead of returning wrong dimensions (7/72 complete; Table 7). Four new experiments, each counting every attempt, extend this (our WKS2 response):

  • On 24 fresh worlds, with a revised discovery rule fixed in advance, the closed loop completes 72/72 cells at 10⁻⁷ with a gain of 14.2 points (97.0% versus 82.8%).
  • Repeating reads only where this rule abstains completes all 144 cells at 10⁻⁶ on 48 further worlds, with a gain of 6.0 points (95% interval [3.9, 8.3]) at 1.04 times the cost.
  • With discovery charged, 17% of the acquisition keeps a gain of 12.2 points at 10⁻⁸ and 7.9 at 10⁻⁷.
  • A kernel readout with no parametric form, replacing the supplied readout class, still gains 10.4 points at 10⁻⁸ with 256 reads.

Reset route (Section 5). The five-record Brier service in F.5 combines unknown-target discovery, native-coordinate recovery, local-law fitting and noisy query-free deployment under its stated public forms and complexity bounds. It uses 49,577 endpoints. With the reported numerical fallback, 19/20 acquisitions complete at each tested noise level 10⁻⁷, 10⁻⁶ and 10⁻⁵, with exact parents and payload writes in all 57 completions. On two planning tasks at 10⁻⁵, the deployed models' mean regret is 79 to 260 times lower than that of a GRU/MLP predictor or direct screening, each given 50,000 endpoints for the two tasks together, and lower than both in each of the nineteen completed worlds (Table 13).

Local laws are the more accurate model on the same decoded pairs (a new world-level test, in our WKS2 response). As WKS2 and G36v suggest, we frame Theorem 5.2 as an identifiability result: it identifies internal stages and their essential parents without expanding the composed map. The demonstrated practical benefit is the reuse of learned coordinates and laws under explicit access conditions.

AuthorsOpenReview ↗

General response (2/2): what each result assumes, returns and tests

The following separates the principal results from their experimental instantiations. Visibility, conditioning and legal buffered access are requirements on the system, not hidden states supplied to the learner.

ResultSupplied informationRequired conditionsRecovered objectExperimental coverage
Sec. 4.1 / App. A.1–A.2Anonymous names and structural contractSeparating terminal responses and a valid, conditioned probe designBracket table, factors and raw supportsF.2 supplies dimensions, spanning-raw design and readout class; F.2.6 and the new experiments remove the dimension and readout-class priors as described above.
Thm 4.2 / Cor. A.6Noisy table, dimension, norm cap and anchor or catalogueTable-error threshold and a suitably separated anchorCommon defining representation, up to its stated automorphismF.1 tests calibration and catalogue selection; F.2 uses calibration after scalar acquisition.
Thm 4.1Calibrated representation and terminal responsesNonzero responses; two independent same-state responses for orientation when q ≥ 3; compatible reference for native dictionariesState rays and tool actions on the physical clockF.2 tests raw-motion decoding and reuse. It does not identify native payload dictionaries or programs.
Thm 5.1Buffered reset contract and degree boundsReset separation, visibility, norming designs and finite-data gapsNative coordinates, complete laws, score and functional scopesF.5 gives a finite-value acquisition pipeline.
Thm 5.2Reset contract, local degree and indegree boundsRetained stage outputs decoded by terminal probes; own-source nondegeneracy, parent contraction, buffered preparation and finite-data gapsMinimum parent sets and local laws without composition expansionF.5 tests noisy local identification. F.8 runs two noiseless checks, the depth example and a shared-pool preparation (128 random all-reset histories, 54,818 terminal means). F.6–F.7 test use.
Sec. 6 / App. DIdentified laws, coordinates and initialized cachesAdmitted schedules, buffers, local defects and propagation boundsQuery-free execution and fixed-schedule updates, with conditional error boundsF.2 and F.5–F.7 test the execution mechanisms.

Query design. Theorem B.4 shows that grouped pair-reset queries cannot see certain cubic score terms, however many replies are collected. F.4 tests this obstruction in a witness family: at matched cost, noiseless grouped queries give .522 decision accuracy, versus 1.000 when the same calls are interleaved.

Why simulated tools, and what is real. The tools are simulated so that identification can be checked against the true hidden states, tool actions and dependencies, which a deployed system does not reveal; the learner itself sees only terminal scores. Two studies add real components. With a trained CIFAR-10 classifier as the hidden score, 512 reads of each of nine new class objectives give 96.4% top-1, versus 41.0% for a readout that erases call order (F.2.2). The Brier service of our first comment uses real data and a real loss. The conditions of the motion route are not tied to our examples: Appendix E (Theorem E.1) proves that they hold in a family of tool systems with randomly drawn parameters, and that the interface is then learned from polynomially many reads.

Revision. The revised PDF adds the following, all in blue:

  • Narrative (ieJ1). A roadmap (Introduction, page 2), a running example (Section 3, page 3) and a purpose sentence at the start of each of Sections 4.1, 4.2, 5.1, 5.2 and 6.
  • Coverage (G36v). A compact form of this coverage table in the main text (Table R1, page 8) and the full table at the start of Appendix F (Table R2, page 38).
  • Discovery to reuse (WKS2, G36v). The closed-loop results, their acquisition cost and the 10⁻⁶ results in Section 7 (page 9), and the new fresh-world, repeated-read, smaller-design and kernel-readout experiments in Appendices F.2.12–F.2.15 (Tables R5–R8, pages 54–57).
  • Local parents (WKS2, G36v). Sections 5.2, 7 and 8 (pages 7 and 10) separate local identifiability and the accuracy comparison from the demonstrated operational gains, with the world-level tests in F.6–F.7 (pages 61–62).
  • Stability constants (G36v). The stage-by-stage comparison of proven constants and measured errors (Table R3, page 40) and the a posteriori certificate (Table R4, page 41) in Appendix F.1.

We hope this clarifies the contribution and its scope, and we welcome further questions.

AuthorsOpenReview ↗

Revised PDF: summary of changes

We have uploaded a revised PDF. All new or rewritten text and all new tables are in blue. Theorem, equation, figure and table numbers are unchanged: the eight new tables are numbered R1–R8 and the new appendix subsections F.2.12–F.2.15. The title, abstract, figures, theorem statements and proofs are unchanged, and the main text ends on page 10.

Main text

  • Introduction: a roadmap of how the results connect and which of them combine into one procedure (ieJ1, G36v).
  • Section 3: a running example (ieJ1).
  • Sections 4.1, 4.2, 5.1, 5.2 and 6: each opens with a sentence stating its purpose (ieJ1).
  • Section 5.2: Theorem 5.2 is stated to be an identifiability result, with the accuracy comparison of local laws and the whole-map fit on the same decoded pairs (WKS2, G36v).
  • Section 7: a compact theorem-to-experiment table (Table R1); the closed loop from dimension discovery to reuse with every attempt counted, its cost, the fresh-world experiment and the 10⁻⁶ results; the comparison with generic sequence models; the one pipeline that joins all four stages (WKS2, G36v).
  • Section 8: the scope of local-parent recovery, what a practical system has to provide, and the a posteriori certificate (ieJ1, G36v).

Appendix

  • Opening of Appendix F: the full coverage table (Table R2) (G36v Q1).
  • F.1: the stage-by-stage comparison of proven constants with measured errors (Table R3), the a posteriori certificate from Proposition A.4 (Table R4), and the distinction between the table error η and the endpoint noise σ (G36v Q2).
  • F.2 and F.2.6: what the spanning design requires, and the closed-loop acquisition accounting (WKS2 Q1).
  • F.2.12–F.2.15 (Tables R5–R8): the closed loop on fresh worlds with a revised discovery rule fixed in advance; repeated reads at 10⁻⁶ only where that rule abstains, also fixed in advance; smaller acquisition designs with discovery charged; reuse with a class-free kernel readout (WKS2, G36v).
  • F.6–F.7: world-level tests of the stored local-versus-whole-map records (WKS2 Q2, G36v Q3).

Three short passages were folded into the new text: the two pointer sentences at the end of Section 3 are now covered by the roadmap and by the purpose sentences of Sections 5.2 and 6, and two sentences at the end of Section 7 are restated, with more detail, in its new paragraph. One pointer sentence in Section 7 was removed for space. No result or table row was removed.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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