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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
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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.
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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
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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.
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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
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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?
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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
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.
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.
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: 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).