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Under review as a conference paper at ICLR 2027

Same Prices, Different Responses: Counterfactual Response Surfaces in Learning Markets

Abstract

Learning sellers can produce similar price paths for very different reasons. Some may act independently, while others may react strongly to a rival's action. Observed market outcomes alone may therefore hide important differences in strategic behavior. We study this problem by measuring how a seller responds when a rival's action is changed. For each unilateral intervention, we compare an intervention rollout with a matched control rollout that starts from the same market state and uses the same future shocks. Repeating this comparison across intervention settings gives a counterfactual response surface that describes the strength and duration of the response. We show that observed trajectories alone cannot identify these responses when different policy systems generate the same observed outcomes. Matched intervention and control rollouts make the responses identifiable and allow them to be estimated over a finite intervention grid. Experiments with scripted and learned pricing policies show that the response surface separates policy systems that look similar from observed prices alone. It also improves identification under the same evaluation budget, predicts responses to held-out interventions, and improves targeting when intervention capacity is limited. These results show that how a policy reacts to a controlled change can reveal information that its observed market outcomes do not.

Primary area:
reinforcement learning
Keywords:
algorithmic pricing, algorithmic collusion, multi-agent reinforcement learning, counterfactual evaluation

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_AekwOpenReview ↗
Rating
2(+1)
Confidence
2
Informativeness
1
Presentation
2
Soundness
3
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Paper summary

The authors study how counterfactual actions reveal differences in sellers’ behavior in learning markets that may be hidden by similar observed prices. They propose measuring these effects through matched intervention and control rollouts, which produce a counterfactual response surface. They provide theoretical estimation guarantees and evaluate the method on scripted and learned pricing policies.

Critical strengths

None

Critical weaknesses
  1. The assumption that we can snapshot and replay the market seems restrictive. Although this is achievable in controlled simulators, it is unclear in which realistic applications we could restore every seller’s learner state and replay the same future market shocks. A clearer description of the intended users and the access they would require would help establish the method’s practical applicability.
  2. Although the paper demonstrates several uses for the response surface, I am not yet convinced that these experiments establish sufficient practical value. In particular, the targeting experiment measures recovery of labels assigned to scripted policy types, rather than the consequences of an actual market intervention. It would be helpful to explain more concretely how the response surface would inform a decision and what benefit that decision would produce.
  3. Overall, I remain unconvinced that the paper provides substantial enough additional insight or value. The theoretical results appear relatively elementary, so the contribution seems to depend mainly on the diagnostic method and its empirical benefits. A clearer explanation of what the full response surface adds beyond existing deviation-based diagnostics, and why that added value justifies the required access and evaluation effort, would strengthen the contribution.
Questions for authors
  1. In which realistic settings would we have the ability to restore seller learner states and replay market shocks?
  2. Could you give a concrete example of a decision informed by the response surface, particularly in the targeting application, and explain how its benefit would be evaluated beyond recovering scripted policy labels?
6 comments
AuthorsOpenReview ↗

Response to Reviewer Aekw (Part 1/3)

We thank the reviewer for the detailed and constructive comments. Below we address each point in turn.

In short, the access we need is routine for the parties that run pricing algorithms, and regulators and monitors can obtain similar access. On learned sellers, choosing which pairs receive a remedy by the response surface raises consumer surplus by 13.8%, against 7.5% when the same number of pairs is chosen by PCI. One reference cell costs 0.75% of the training transitions and keeps most of this value.

W1 & Q1: Realistic Settings for Snapshots and Shock Replay

The method is built for the parties that run the algorithms or oversee them, and for them this access is routine. With less access, the Frozen surface remains identifiable.

1. Who Already Has This Access

Parties that run the algorithms.

  • Developers who test a repricer before deployment.
  • Pricing-software vendors that host many clients' agents and hold every learner state. They are the "hub" in hub-and-spoke concerns.
  • Marketplaces that operate built-in repricing tools and set the rules for algorithmic sellers [6].

Parties that oversee them.

  • Competition authorities. The UK CMA can require a firm to disclose information to approved auditors and to cooperate with testing and inspections [4].
  • Monitors appointed under remedies. The 2025 settlement between the U.S. Department of Justice and RealPage, a vendor of rent-pricing software, appoints a monitor who can review the code, the model training records and the runtime logic of the software [3].
  • Testing regimes in which firms submit algorithms for evaluation, as discussed by Harrington [2], and AI regulatory sandboxes.

For all of them, a snapshot is an ordinary checkpoint of weights, optimizer state, buffers and the shock-generator state, and faithful replay from such checkpoints is an established tool in deep learning [5]. Shocks are shared exactly when the simulator draws them. Without shared shocks the estimate stays unbiased and needs more pairs (table below).

2. What Each Level of Access Identifies

AccessWhat is identifiedResult
Snapshot and shared shocksRFR^F and RAR^AAUROC 0.94 at 500 pairs per cell
Snapshot without shared shocksRFR^F and RAR^A, unbiasedAUROC 0.91 at 500 pairs and 0.94 at about 2,000 pairs
Query access to frozen policiesRFR^FAUROC 0.83, against 0.85 with full snapshots
Observed data onlynot identified in general (Prop. 1)natural deviations of SAC give a lag-1 RMSE of 0.015, against 0.004 for matched rollouts

Shared shocks cut the variance of each pair by a factor of 4.3, since the two rollouts have a median correlation of 0.77. Natural deviations are rare, since SAC prices about 0.25s0.25s below its policy mean in only 0.4% of periods, so intervention is the practical route (App. B.5 and B.11).

3. Query-Only Access

A tester who can query each frozen policy but cannot copy its state runs both rollouts in its own simulator with shared shocks. It rebuilds the execution state by replaying the last 50 observed periods through the policy. This covers the 5-period window of the neural policies exactly and recovers the scripted execution state in 93% of units. With the 15k budget, Frozen AUROC is 0.83, close to the 0.85 with full snapshots (Sec. 6, App. D and D.1).

AuthorsOpenReview ↗

Response to Reviewer Aekw (Part 2/3)

W2 & Q2: A Concrete Decision and Its Benefit

Thank you for this question. To turn the surface into a decision with consequences, we ran a remedy experiment with welfare outcomes on learned sellers, and targeting by the surface nearly doubles the consumer-surplus gain of targeting by PCI (Sec. 5.2 and App. B.10).

1. The Decision

A monitor or a vendor can apply a remedy to only KK of its seller pairs, since each remedy must be set up and checked. The remedy delays rival-price information, so that rivals' prices enter the observation with a 10-period lag. The data-age limits used in practice work in the same way. The RealPage settlement, for example, lets the models train on nonpublic competitor data only when the data are at least 12 months old [3]. The question is which KK pairs to treat.

2. How We Evaluate It

We apply the remedy to all 60 learned pairs (3 algorithms and 20 seeds) and continue Adaptive learning for 2×1052\times10^5 steps. We then score each ranking rule at a budget of b=0.2b=0.2, which means K=12K=12. Since every pair is treated, we can compute the best possible choice of 12 pairs.

The surface score is D1:5AD^A_{1:5} averaged over the 6 cells of the full grid, and it uses no labels. For each pair, ΔPCI is the mean PCI over the last 2×1042\times10^4 periods minus the same window of a matched run from the same snapshot with the same shocks but no remedy. The 95% intervals come from 2,000 bootstrap resamples of pairs, with the ranking recomputed in each resample.

3. Results

In this logit market, lower prices under the same demand raise consumer surplus, CS=μlog⁡(∑je(a+z−pj)/μ+ea0/μ)CS=\mu\log(\sum_j e^{(a+z-p_j)/\mu}+e^{a_0/\mu}). We report the change in CS for the treated pairs, measured against the matched runs.

Ranking ruleMean ΔPCI, treated pairsΔCS, treated pairs
Random−0.06 [−0.08, −0.04]+4.3% [+2.9, +5.7]
PCI−0.09 [−0.13, −0.05]+7.5% [+4.2, +10.9]
Static deviation test−0.11 [−0.15, −0.07]+8.7% [+5.5, +11.9]
Response surface (no labels)−0.17 [−0.21, −0.13]+13.8% [+10.6, +17.0]
Best possible 12 pairs−0.21+17.2%

The same 12 treatments bring almost twice the gain in consumer surplus when the pairs are chosen by the response surface. Over PCI, the paired gain is +6.3 percentage points [+2.4, +10.1] in ΔCS and −0.08 [−0.13, −0.03] in ΔPCI. Over the static deviation test, it is +5.1 [+1.0, +9.3] and −0.06 [−0.11, −0.01]. The surface reaches 81% of the best possible effect. Total surplus rises under every rule, most under the surface.

4. What the Decision Maker Learns

High prices are a poor guide to where a remedy works. PCI spends part of the budget on high-price pairs that do not react to their rivals, and these pairs hardly move under the remedy. Over all 60 pairs, the Spearman correlation between the score and ΔPCI is −0.64 for the surface, −0.42 for the static deviation test and −0.31 for PCI. The surface can tell apart markets that prices treat as equal. Among learned markets whose PCI differs by at most 0.02, 27% have clearly different responses, with non-overlapping 95% intervals (App. B.8).

W3: What the Full Surface Adds beyond Deviation Tests

Calvano et al. [1] trace price paths after a one-shot deviation with learning frozen, and Harrington [2] proposes testing pricing algorithms for reward-punishment properties. The surface builds on these tests in three ways, and the revision measures each one.

1. A Matched Control

A pre/post contrast mixes the response with shocks and drift. Replacing the matched control with a pre/post contrast lowers AUROC from 0.94 to 0.81, and an independent control from the same snapshot gives 0.91. So the matched control mainly removes bias (App. B.5).

2. The Whole Path as a Feature

Deviation paths are usually inspected by eye or reduced to a scalar such as PD-16. The surface uses the whole controlled path as input. This matters because myopic best response reacts at lag 1 about as strongly as reciprocal punishment (−0.10-0.10 vs. −0.126-0.126), and only the later lags tell them apart. Keeping lag 1 alone gives AUROC 0.74, one depth per regime gives 0.87, and the full surface gives 0.94.

AuthorsOpenReview ↗

Response to Reviewer Aekw (Part 3/3)

W3: What the Full Surface Adds beyond Deviation Tests (continued)

3. Frozen and Adaptive Evaluation

What a policy encodes differs from what continued learning adds. The CMA notes that one-off audits can quickly become outdated because deployed algorithms keep updating [4], and Adaptive evaluation measures this learning directly. For SAC, the response depth is 0.028 under Frozen and 0.041 under Adaptive evaluation, so a test with learning frozen misses about a third of the response. At the same budget of 15,000 transitions, the surface with both regimes reaches AUROC 0.91, against 0.83 for PD-16 with both regimes and a stabilized denominator. The paired gain is +0.08 [+0.05, +0.11] (App. B.4), and it holds on a pool that adds a rule which learns but never observes the rival (App. B.6).

The surface also predicts responses at intervention settings not used for fitting, with path RMSE 0.031 against 0.061 for PD-16 with history (App. C.9).

W3: Is the Added Value Worth the Effort?

A single reference cell costs 0.75% of the training transitions and keeps most of the value of the full grid. Costs are per policy pair and relative to the 2×1062\times10^6 steps used to train one learned pair. We measure quality by AUROC on the scripted pool, and for learned sellers by the remedy effect and the Kendall τ\tau of the pair ranking against the full grid.

SettingTransitionsvs. trainingScripted AUROCLearned ΔPCI / τ\tau
Reference cell, F+A1.5×1041.5\times10^40.75%0.91−0.15 / 0.86
Grid, 100 pairs per cell4.8×1054.8\times10^524%0.91−0.16 / 0.93
Grid, 500 pairs per cell2.4×1062.4\times10^6120%0.94−0.17 / 1

The reference cell uses 250 pairs × 2 rollouts × 15 lags × 2 regimes, the same budget as the equal-budget comparison. It already reaches AUROC 0.91 and 88% of the full-grid remedy effect. The full grid serves prediction at new intervention settings and a complete description across (α,d)(\alpha,d). Frozen rollouts need no gradient updates, so its compute is about 0.7 times that of training (App. D.1).

W3: The Role of the Theory

Thank you for this view. The theory is deliberately simple. It states what observed data cannot identify and what a valid evaluation must copy. These requirements matter in practice. A checkpoint with network weights only, a common shortcut, silently turns Adaptive evaluation into Frozen evaluation and changes the Adaptive response depth by about 30% for SAC and TD3 (App. B.12).

Presentation

We have worked on the parts that took effort to read. Sec. 3.1 now defines the execution state and the learner state, and Sec. 5.1 defines the labels. App. C.7 to C.10 give the market, every scripted rule, the prediction model and the classifier.

References

[1] Calvano, Emilio, et al. "Artificial intelligence, algorithmic pricing, and collusion." American Economic Review 110.10 (2020): 3267-3297.

[2] Harrington, Joseph E. "Developing competition law for collusion by autonomous artificial agents." Journal of Competition Law & Economics 14.3 (2018): 331-363.

[3] U.S. Department of Justice. "United States of America et al. v. RealPage, Inc. et al.; Proposed Final Judgment and Competitive Impact Statement." Federal Register 90.232 (2025): 56286-56335.

[4] Competition and Markets Authority. "Algorithms: How they can reduce competition and harm consumers." Research paper, UK Competition and Markets Authority, 2021.

[5] Xu, Xiangzhe, et al. "Checkpointing and deterministic training for deep learning." Proceedings of the 1st International Conference on AI Engineering (CAIN), 2022: 65-76.

[6] Johnson, Justin P., Andrew Rhodes, and Matthijs Wildenbeest. "Platform design when sellers use pricing algorithms." Econometrica 91.5 (2023): 1841-1879.

Final Thanks

Thank you again for your time and for questions that made the paper more useful. We hope the concrete users, the remedy experiment with welfare outcomes and the cost account answer your concerns about practical value. If they do, we would be grateful if you would consider raising your rating. We are happy to provide more details and look forward to further discussion.

Reviewer_38qROpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper argues that, based on observed price trajectories in markets with repeated price formation, it is generally not possible to identify counterfactual reactions, as policy systems that are observationally equivalent may react differently to the same intervention. Counterfactual response surfaces are proposedto measure these reactions. The price of a focal seller is reduced unilaterally, and an intervention rollout is compared with a matched control rollout. Both start from the same complete snapshot (market history and all learner states) and are subject to the same future exogenous shocks. Their normalised difference is measured across different intervention magnitudes and durations, response lags, and two regimes. In the ‘frozen’ regime, the learner states are fixed; in the ‘adaptive’ regime, the learning process continues.

There are three theoretical results:

  • An outcome-only impossibility result (Proposition 1).
  • Unbiasedness and consistency of the matched estimator (Theorem 1).
  • A uniform error bound for finite grids (Theorem 2).

The experiments utilise a differentiated logit market with two sellers, equipped with scripted policy systems and SAC/TD3/PPO sellers. Four findings are reported:

  • Pre-programmed systems with virtually identical PCI and price correlation differ sharply in their response.
  • Given the same budget, the response surface outperforms a scalar baseline with forced deviation (PD-16), with the AUROC value rising from 0.80 to 0.91.
  • An ablation analysis attributes the gain primarily to dynamic information and the matched control.
  • The response surface predicts held-out intervention settings for learned sellers and improves budget-constrained targeting on 1,000 scripted units.
Critical strengths
  1. A well-motivated problem with a simple, reusable design. High prices alone do not indicate whether sellers are reacting to competitors, and the study demonstrates this convincingly (Fig. 1, Fig. 3). ‘Matched rollouts’ extend common random numbers to learning agents by replicating both the learner’s complete state and the shocks. The result is a clear causal contrast and - when matched outcomes are positively correlated - estimates with lower variance. The design requires control over the capture and reproduction of learner states, but not access to interpretable internal processes. This makes it a plausible audit tool in simulation studies, which, for me, is the main reason why I see added value in this work.

  2. The experiments ask the right questions. The study includes a comparison, under the same budget, with a literature-grounded baseline (PD-16, inspired by Calvano et al., 2020), an ablation of design components, and a ‘held-out’ evaluation, split by training seed, policy instance and intervention cell. If specified appropriately, this design would effectively test the method’s key claims. My concerns relate to the way in which the experiments are reported, not to what they intend to test (see weakness 1).

Critical weaknesses
  1. The empirical methods are insufficiently specified, meaning that the key findings cannot be evaluated. The theory establishes basic properties of a simulation estimator: the existence of observation-equivalent systems, unbiasedness and a Hoeffding-type bound. Whilst these are correct and clarifying, they are elementary, meaning that the contribution of the paper relies largely on its experiments. These experiments omit essential details:
  • Held-out prediction (Section 5.2). A response surface is a set of measured responses; on its own, it does not predict any previously unknown intervention. The prediction model, its inputs, its fitting procedure and the representation of the test policy instances are not described. The reported extrapolation results (RMSE 0.031, R2R^2 0.82) cannot therefore be evaluated.
  • Identification. The paper does not specify how surfaces are converted into classification values, which classifier or scoring rule is used, or how the baselines (temporal outcome model, static deviation test) are fitted.
  • Ablations. What is removed in each ablation is not specified. Examples include ‘remove dynamic response’, ‘remove matched control’, ‘merge Frozen & Adaptive’ and ‘remove role swap’.
  • Environment and policies. The scripted policy rules, the logit demand parameters, the costs and the composition of seller pairs are not specified.

The announced release of the code does not currently fill these gaps in the reporting. The omissions appear to be remediable, but in their current form they prevent an evaluation of the key empirical findings.

  1. The criterion for binary classification is unclear, and the learnt behaviour is not characterised.
  • Labels. The response surface itself is clearly defined (Equation 11), but the binary label used for identification and targeting is not. In Appendix C.6, reciprocal punishment, ‘noisy reciprocity’ and ‘opponent shaping’ are described as response-dependent, whilst the myopic best-response strategy is regarded as a non-response-dependent control. If the myopic best-response strategy depends on the rival’s previous price, it responds causally to a price reduction; therefore, the criterion must be more narrowly defined, for example, a sustained reaction or a specific punishment mechanism. This should be outlined in the paper. Furthermore, a causal reaction alone does not prove either coordination or harmful behaviour. The targeting experiment demonstrates the recovery of the assigned, predefined labels, and its broader regulatory significance remains unproven.
  • Learned sellers. Fig. 5 shows learned responses, broken down by algorithm, but only as prediction targets. The paper does not systematically characterise what the surfaces reveal about SAC, TD3 and PPO sellers in terms of algorithm, regime and PCI. This is the key question that the method is designed to answer.
  • Practical scope of application. The method relies throughout on the recording of complete learner states and the replay of exogenous shocks. The ‘Limitations’ section does not discuss what this requires in practice: control over execution, the learner state and the shocks - something that an auditor of deployed systems does not usually have.
Questions for authors

The following clarifications are required in order to assess the key findings:

  1. Prediction model. Which model produces the ‘held-out’ predictions presented in Section 5.2? What are its input data, how is it fitted, and how is the extrapolation from α∈{0.10,0.25},d=1\alpha \in \{0.10, 0.25\}, d = 1 to α=0.50,d=5\alpha = 0.50, d = 5 carried out?
  2. Scores and labels. How are response surfaces and baselines converted into scores for the AUROC? What is the exact criterion for ‘response-dependent’? If the myopic best-response strategy depends on the opponent’s previous price, why is it then classified as non-response-dependent?
  3. ‘Frozen’/adaptive ablation. Section 4.3 states that the two regimes coincide for script-driven strategies, yet combining them reduces the AUROC from 0.94 to 0.84 (Fig. 4b). Are learned systems included in the identification experiments? If so, how are they labelled, and what is the composition of the sample?
  4. Pair composition. Are the seller pairs of the same type or mixed, for scripted and for learned sellers? What does the ‘role swap’ feature encode?
  5. Accounting for the same budget. Do the 15,000 transitions per policy-pair seed also include control rollouts? Does the response surface in Fig. 4a use information from both regimes, whilst PD-16 uses only ‘Frozen’?
  6. Ablation operations. What replaces the control when ‘remove matched control’ is selected? A comparison of a ‘matched control’ with an independently simulated control would isolate the variance benefit of shared shocks. What information remains after ‘remove dynamic response’?
  7. Learning sellers. What do the response surfaces reveal beyond the prediction plots in Fig. 5 for SAC, TD3 and PPO, broken down by algorithm and regime, and how do they relate to the observed PCI? Fig. 5a shows positive mean reactions, i.e. price increases following a price cut. What drives these?

Suggestions (which do not affect my assessment):

  • Report results for the intermediate regimes RFA,RAFR^{FA}, R^{AF} from Remark 1.
  • Investigate mixed pairs with explicit role asymmetry.
  • For stochastic strategies, discuss whether an observation-based approach that utilises naturally occurring deviations could identify reactions, and under which assumptions regarding conditioning, support and observability.
  • A variance-sensitive bound (e.g. an empirical Bernstein bound) would better reflect the paired design. This is optional and does not constitute a shortcoming.

Minor notes Notation and definitions

  • Sign of δ\delta. In Section 5.1, δ=−αs\delta = -\alpha s (negative) is used, whilst in Appendix A.1 the off-path action a⋆−δa^\star - \delta is used with δ>0\delta > 0. Please adhere to one of these two conventions.
  • Remark 1. The order of the indices in RFAR^{FA}, RAFR^{AF} (focal or opponent first) is not specified.
  • Table 3. The policy system reported is not stated, and D1:5AD^A_{1:5}, R1AR^A_1, TrecAT^A_{rec} are used before they are defined in Appendix C.4.
  • Caption for Fig. 3. Reference is made to ‘training seed’ confidence intervals for pre-programmed strategies, which, however, have not been trained. Please define clusters for pre-programmed systems.
  • Table 1. ‘Hard tie-breaking’ is not defined for a logit market. In the case of ‘three sellers’, it is unclear how the responses are defined or aggregated across two opponents.
  • Eq. (16). The recovery time may occur even before a delayed reaction begins. A definition after the peak or as the last exit would be more robust. Furthermore, η=0.05\eta = 0.05 is comparable in magnitude to the reactions of the trained sellers in Fig. 5.
  • PD-16 (Equation 17). The denominator pj0−pNp^0_j - p^N is unstable if prices are close to the Nash equilibrium prior to the intervention.
  • Appendix C.2. Maintaining the final state for remaining lags may lead to a distortion of reactions with late lags. Please specify how often this occurs.

Presentation

  • The contribution bullets in the introduction do not include the ‘held-out’ prediction result highlighted in the abstract.
  • Figure 6 appears in Section 6/7, far removed from the relevant discussion in Section 5.2.

Language and References

  • Section 5.2: ‘Static deviation test reaches …’ should read: ‘The static deviation test reaches ...’.
  • The citations in the text “Meylahn & V. den Boer, 2022” and “den Boer et al., 2026” suggest that the BibTeX author field requires braces, i.e. {den Boer}.
  • Incomplete references: For Hettich (2021), Lambin (2024) and Zhou (2026), the venue or URL is missing.
8 comments
AuthorsOpenReview ↗

Response to Reviewer 38qR (Part 1/5)

We thank the reviewer for the detailed and constructive comments. Below we address each point in turn.

W1 & Q1: The Prediction Model

The predictor uses only the test instance's own surface on the training cells, and it stays ahead of both baselines even when they receive the same structure (path RMSE 0.031 against 0.052 and 0.079).

1. Inputs and Split

The target cell (α=0.5\alpha=0.5, d=5d=5, H=100H=100) is never used as model input or for fitting, for any instance. It is measured only to score the predictions. For each test instance, the model input is that instance's own surface on the training cells (α∈{0.10,0.25}\alpha\in\lbrace0.10,0.25\rbrace, d=1d=1, H∈{20,50}H\in\lbrace20,50\rbrace). The few shared quantities are fitted on training seeds and policy instances that do not overlap with the test ones. For our model these are the pooled exponent γˉ\bar\gamma and the tail-rate prior. For the baselines they are the ridge and GRU weights.

2. Three Steps

  1. Magnitude. The model scales the reference path by a power law, R^(k;α,1)≈(α/0.25)γuR^(k;0.25,1)\hat R(k;\alpha,1)\approx(\alpha/0.25)^{\gamma_u}\hat R(k;0.25,1). It estimates γu\gamma_u from α∈{0.10,0.25}\alpha\in\lbrace0.10,0.25\rbrace and shrinks it toward the pooled value γˉ=0.75\bar\gamma=0.75 by empirical Bayes.
  2. Duration. It builds the d=5d=5 response by adding five lag-shifted single-period responses, R^(k;α,5)=∑m=04R^(k−m;α,1)\hat R(k;\alpha,5)=\sum_{m=0}^{4}\hat R(k-m;\alpha,1).
  3. Horizon. It fills lags 51 to 100 with an exponential tail fitted on lags 30 to 50.

3. Where the Gain Comes From

"PD-16 + history" is a ridge regression from training-cell PD-16 values, PCI, price correlation, the last 10 prices and (α,d)(\alpha,d) onto an 8-function exponential basis for the path. The temporal model encodes the 200-period history with a GRU and maps its final state and (α,d)(\alpha,d) to the 100-lag path. To separate the measured surface from the structural steps, we give the same superposition to both baselines and also remove it from our model.

ModelPath RMSE
Temporal outcome model0.088
Temporal outcome model + same superposition0.079
PD-16 + history0.061
PD-16 + history + same superposition0.052
Surface without superposition0.047
Surface without shrinkage0.038
Surface, full0.031

With the same structure, both baselines stay behind the surface, and the surface without superposition still beats them. So the gain comes from measuring the response. Fig. 5 uses Adaptive evaluation, and its caption now says so (Sec. 5.2 and App. C.9).

W1 & Q2: Scores, Classifier and Labels

Scores come from an L2-regularized logistic regression with grouped cross-validation, and a unit is RD when its noise-free response persists beyond the one-period reaction of the static game.

1. Scores

For each intervention cell and regime, the features are R^(k)\hat R(k) for k=1,…,15k=1,\dots,15, the response depth D1:5D_{1:5}, the late depth D16:HD_{16:H} (full grid only) and the recovery time TrecT_{rec}, together with the role-swapped direction. A logistic regression with an L2 penalty turns these features into an out-of-fold probability. We use 5-fold cross-validation grouped by instance seed, choose the penalty by inner cross-validation, and use the same folds for every method. PD-16 and the static deviation test serve directly as scores, since AUROC does not change under a monotone calibration. The static test is the opponent's one-period Frozen price change against its own pre-intervention price. The outcome-only baseline is a logistic regression on PCI, price correlation, mean profit, price std and lag-1 autocorrelation (App. C.10).

2. Labels

A scripted unit is response-dependent (RD) if its noise-free Adaptive response to the reference intervention (α=0.25\alpha=0.25, d=1d=1) exceeds 0.05 in magnitude at two or more lags k≥2k\ge2. All other units are non-response controls (NR). The noise-free path switches off execution noise, sets future shock innovations to zero and averages over 200 snapshots per instance. Labels follow from the rule definitions and agree with this check for every instance (Sec. 5.1 and App. C.6).

3. Myopic Best Response

You are right that myopic best response reacts causally to a price cut. Its lag-1 response is −0.10-0.10, close to the −0.126-0.126 of reciprocal punishment, because the best-response slope at pNp^N is 0.42. The reaction fades at once. The echo is −0.018-0.018 at k=3k=3 and below 0.005 after that. This one-period reaction already exists in the static game, so the condition k≥2k\ge2 places myopic best response among the NR units. It is our hardest negative for one-step tests, and it explains why removing dynamics costs the most AUROC (from 0.94 to 0.74).

AuthorsOpenReview ↗

Response to Reviewer 38qR (Part 2/5)

W1: Environment and Scripted Rules

The market follows Calvano et al. [1], and every scripted rule is specified below (App. C.7 and C.8).

Market. We use the logit demand of Calvano et al. [1] with a=2a=2, a0=0a_0=0, μ=0.25\mu=0.25 and c=1c=1. At z=0z=0 this gives pN=1.473p^N=1.473, pM=1.925p^M=1.925 and s=0.452s=0.452. A common AR(1) quality shock zt=0.9zt−1+ϵtz_t=0.9z_{t-1}+\epsilon_t with ϵt∼N(0,0.052)\epsilon_t\sim N(0,0.05^2) moves demand, and sellers do not observe it. Episodes last 1,000 periods. Snapshot times come from [200,T−Hmax⁡−dmax⁡][200, T-H_{\max}-d_{\max}], so the terminal-state fallback of App. C.2 never occurs. Price correlation is the Pearson correlation of the two unintervened price series.

Learned sellers. Each seller observes the last 5 periods of both prices and of its own demand, so ot∈R15o_t\in\mathbb R^{15}. Actions in [−1,1][-1,1] map linearly to [pN−0.5s,pM+0.5s][p^N-0.5s, p^M+0.5s]. An intervention sets the executed price to pi,τ−αsp_{i,\tau}-\alpha s.

Scripted rules. Every scripted price carries a small execution noise ξi,t∼N(0,(0.01s)2)\xi_{i,t}\sim N(0,(0.01s)^2). Each instance seed fixes the shock stream and the snapshots and holds five draws of the rule parameters.

  • Independent high-price targets pN+κsp^N+\kappa s and adjusts toward a target level of its own demand. It never observes the rival. Common shocks move both sellers' demand, which gives a price correlation of 0.91 to 0.95.
  • Common-shock response prices on a constant-gain filter of the shock. It infers the shock from its own demand as if the rival charged its own price, so it reads part of a rival cut as a negative shock.
  • Myopic best response plays BR(pj,t−1)\mathrm{BR}(p_{j,t-1}) under the filtered shock.
  • Reciprocal punishment is a graded trigger. A rival cut larger than θs\theta s starts a counter of TPT_P periods, and the punishment depth grows with the size of the cut. A seller that has just cut its own price does not start a punishment for 8 periods, so it does not retaliate against a punishment that it caused.
  • Noisy reciprocity starts the same punishment only with a probability ρ\rho, which Bush-Mosteller reinforcement [3] updates against a learned profit aspiration.
  • Opponent shaping keeps a recursive least squares (RLS) model of the rival's reaction and a shaping gain ψ\psi that rises with the rival's prediction error. It sets its price to the reference price plus ψ\psi times a decaying memory of rival undercuts.
  • Demand-learning independent pricing (DLI, new) fits its own residual-demand curve by RLS and never observes the rival. It sets a markup from the estimated demand slope. Under this misspecified demand model it sustains PCI 0.78, in the spirit of Hansen et al. [2].

Q3: The Frozen and Adaptive Ablation

Thank you for catching this. The sentence in Sec. 4.3 was too broad, and we have corrected it. Learned sellers are not part of the identification or targeting pools. The merge effect comes from two scripted rules that update online statistics.

1. Learner State and Execution State

Frozen evaluation holds each policy fixed as a map from observation history to actions. The execution state is the memory that this fixed map uses, such as punishment counters, filters and observation windows, and it always evolves. The learner state is whatever changes the map, such as network weights, optimizer moments, buffers, and online estimates like RLS coefficients or a Bush-Mosteller probability. Frozen evaluation fixes it, and Adaptive evaluation updates it.

Noisy reciprocity and opponent shaping have learner state. For opponent shaping, the lag-1 response is −0.041-0.041 under Frozen evaluation and −0.094-0.094 under Adaptive evaluation. Merging the two regimes removes this contrast, which explains the drop from 0.94 to 0.84. Both states are now defined in Sec. 3.1, 4.3 and App. C.3.

AuthorsOpenReview ↗

Response to Reviewer 38qR (Part 3/5)

Q3: The Frozen and Adaptive Ablation (continued)

2. The Contrast Reflects Responses to the Rival

To show that the F−A features capture responses to the rival and not the mere presence of an update rule, we add DLI as a hard negative. DLI has learner state but never observes the rival. Its Adaptive learning creates a small gap that fades quickly, with a lag-1 response of −0.012-0.012 under Frozen and −0.031-0.031 under Adaptive evaluation. The augmented pool has 700 pairs (400 NR and 300 RD).

Augmented poolAUROC (all)AUROC (RD vs. DLI)DLI flagged at TPR 90%
Surface, F+A, full grid0.930.929%
Surface, F+A, 15k0.900.8912%
Surface, Frozen only, 15k0.850.8615%
PD-16, F+A, stabilized, 15k0.810.7641%
PD-16, Frozen, stabilized, 15k0.810.7837%

The surface keeps its gain from Adaptive data (+0.05 over Frozen only) and flags fewer DLI units with both regimes than with Frozen data alone. It reads the shape and persistence of the learning-induced change. PD-16 with both regimes flags 41% of DLI units. The Frozen-only comparison involves no learner state, and the surface leads stabilized PD-16 there by 0.04 on this pool (App. B.6).

Q4: Pair Composition and Role Swap

On mixed pairs with role asymmetry, the surface reaches AUROC 0.92, and role swap matters most there. Scripted pairs in the main pool are same-family pairs with independently drawn parameters. Learned pairs are same-algorithm self-play pairs, with 3 algorithms and 20 seeds, which gives 60 pairs. Role swap measures both Rj←iR_{j\leftarrow i} and Ri←jR_{i\leftarrow j} and appends the reverse-direction response surface.

Following your suggestion, the mixed pool has 30 ordered cross-family combinations and 20 seeds. This gives 600 units, each labeled by the opponent's family.

Mixed pairsAUROC
Surface (full)0.92
Surface without role swap0.84
PD-160.74
Static deviation test0.70

In pairs of one RD seller and one NR seller, comparing the Adaptive depths D1:5AD^A_{1:5} of the two directions finds the responsive seller in 95% of units. Role swap adds 0.08 AUROC here and 0.05 in the same-family pool, so it matters most when the two sellers differ (App. B.7).

Q5: Equal-Budget Accounting

Yes, the 15,000 transitions include the control rollouts, and the surface leads PD-16 in each regime. The F+A surface uses 250 pairs × 2 rollouts × 15 lags × 2 regimes in one direction. The Frozen-only surface uses the full 500 pairs, and PD-16 uses 1,000 Frozen rollouts × 15 lags.

Method (15k transitions)AUROCFPR at TPR 90%
PD-16, Frozen (paper)0.800.37
PD-16, Frozen, stabilized0.820.32
PD-16, F+A, stabilized0.830.30
Surface, Frozen only (500 pairs)0.850.26
Surface, F+A (paper)0.910.15

The surface leads in each regime. With Frozen data, its paired gain is +0.03 [+0.01, +0.06] over stabilized PD-16 and +0.05 [+0.02, +0.08] over the original PD-16. With both regimes the gain is +0.08 [+0.05, +0.11]. PD-16 gains just 0.01 from Adaptive data, because a pre/post contrast cannot separate the response from drift. The stabilized denominator max⁡(pj0−pN,0.1s)\max(p_j^0-p^N, 0.1s) answers your note on Eq. (17). Most of the 17% of units below this floor are myopic best responders near pNp^N (App. B.4 and C.5).

Q6: Ablation Operations

Each ablation changes one part of the full-grid surface (AUROC 0.94), and an independent control shows that the matched control mainly removes bias.

  • Remove dynamic response keeps only R^(1)\hat R(1) for each cell and regime (0.74).
  • Remove matched control uses the opponent's pre-intervention price as the reference, which gives a pre/post contrast (0.81).
  • Merge F & A pools the Frozen and Adaptive pairs into one surface (0.84).
  • Remove recovery features drops TrecT_{rec} and D16:HD_{16:H} (0.86).
  • Convert to scalar keeps one depth per regime, DˉF\bar D^F and DˉA\bar D^A, averaged over cells and lags (0.87).
  • Remove role swap drops the reverse direction (0.89).

The scalar version keeps the regime contrast, which is why it scores above the merged surface (0.87 vs. 0.84).

Your suggestion to test an independently simulated control was very helpful. Shared shocks cut the variance of each pair by a factor of 4.3, since the median correlation between the two rollouts is 0.77. At 500 pairs, AUROC is 0.94 with the matched control, 0.91 with an independent control from the same snapshot, and 0.81 with no control. So most of the loss without a control comes from bias. An independent control reaches 0.94 with about 2,000 pairs (App. B.5 and C.10).

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

The paper studies the problem of distinguishing strategic responses among learning sellers whose observed price paths look similar. The paper proposes counterfactual response surfaces, constructed by comparing intervention and control rollouts from matched market states under shared shocks. It distinguishes evaluation with frozen policies from evaluation with continued learning and reports improvements in behavioral identification, response prediction, and intervention targeting

Critical strengths
  1. The paper clearly motivates why observed prices alone cannot reveal how sellers respond to deviations. Measuring responses across intervention sizes and time horizons provides a more informative description of behavior

  2. The distinction between frozen and adaptive evaluation is useful. It makes explicit whether the measured response includes learning after the intervention

3..The experiments include equal-budget comparisons, component ablations, and held-out intervention settings. Treating training seeds as the statistical replication unit also avoids overstating confidence from many correlated rollouts

Critical weaknesses
  1. Important experimental components remain underspecified, including the classifier, response-prediction model, and precise scripted policy rules. These omissions make the reported identification and extrapolation results difficult to reproduce or assess

2.The identification and targeting evaluations primarily distinguish predefined scripted policy families. The learned-agent experiments demonstrate response prediction, but do not establish that the method identifies the underlying mechanisms of learned behavior

  1. The theoretical results largely formalize consequences of correct simulator replay, linearity of expectation, and concentration bounds. I think the main contribution therefore lies in the experimental methodology, which needs more complete specification and stronger validation
Questions for authors

NA

6 comments
AuthorsOpenReview ↗

Response to Reviewer Rmpi (Part 1/4)

We thank the reviewer for the detailed and constructive comments. Below we address each point in turn.

W1: Specification of the Classifier and the Prediction Model

Every component you listed is specified below, together with the results that each part supports.

1. Classifier and Baselines

For each intervention cell and regime, the features are the response path R^(k)\hat R(k) for k=1,…,15k=1,\dots,15, the response depth D1:5D_{1:5}, the late depth D16:HD_{16:H} (full grid only) and the recovery time TrecT_{rec}, together with the role-swapped direction. An L2-regularized logistic regression on standardized features turns them into an out-of-fold probability. The outer split is 5-fold cross-validation grouped by instance seed, the penalty is chosen by inner cross-validation, and every method uses the same folds. PD-16 and the static deviation test serve directly as scores, since AUROC does not change under a monotone calibration. The static test is the opponent's one-period Frozen price change against its own pre-intervention price. The outcome-only baseline is a logistic regression on PCI, price correlation, mean profit, price standard deviation and lag-1 autocorrelation (App. C.10).

2. Response-Prediction Model

The model is fitted on α∈{0.10,0.25}\alpha\in\lbrace0.10,0.25\rbrace, d=1d=1 and H∈{20,50}H\in\lbrace20,50\rbrace and tested on α=0.50\alpha=0.50, d=5d=5 and H=100H=100. Training and test sets are separated by training seed, policy instance and intervention cell. For a test instance, the input is that instance's own surface on the training cells. The target cell is never used as model input or for fitting, and it is measured only to score the predictions. The model has three steps.

  1. Magnitude. It scales the reference path by a power law, R^(k;α,1)≈(α/0.25)γuR^(k;0.25,1)\hat R(k;\alpha,1)\approx(\alpha/0.25)^{\gamma_u}\hat R(k;0.25,1), with γu\gamma_u estimated from the two training sizes and shrunk toward the pooled value γˉ=0.75\bar\gamma=0.75 by empirical Bayes.
  2. Duration. It adds five lag-shifted single-period responses, R^(k;α,5)=∑m=04R^(k−m;α,1)\hat R(k;\alpha,5)=\sum_{m=0}^{4}\hat R(k-m;\alpha,1).
  3. Horizon. It fills lags 51 to 100 with an exponential tail fitted on lags 30 to 50.

To separate the measured surface from these structural steps, we give the same superposition to both baselines and also remove it from our model.

ModelPath RMSE
Temporal outcome model0.088
Temporal outcome model + same superposition0.079
PD-16 + history0.061
PD-16 + history + same superposition0.052
Surface without superposition0.047
Surface without shrinkage0.038
Surface, full0.031

With the same structure, both baselines stay behind the surface, and the surface without superposition still beats them. So the gain comes from measuring the response. The full model also reaches a test R2R^2 of 0.82 and 92% response-sign accuracy (Sec. 5.2 and App. C.9).

W1: Scripted Rules, Labels and Ablation Operations

1. Scripted Rules

Every scripted price carries an execution noise ξi,t∼N(0,(0.01s)2)\xi_{i,t}\sim N(0,(0.01s)^2), and each instance seed holds five draws of the rule parameters.

  • Independent high-price targets pN+κsp^N+\kappa s and adjusts toward a target level of its own demand. It never observes the rival. Common shocks move both sellers' demand, which gives a price correlation of 0.91 to 0.95.
  • Common-shock response prices on a constant-gain filter of the shock. It infers the shock from its own demand as if the rival charged its own price, so it reads part of a rival cut as a negative shock.
  • Myopic best response plays BR(pj,t−1)\mathrm{BR}(p_{j,t-1}) under the filtered shock.
  • Reciprocal punishment is a graded trigger. A rival cut larger than θs\theta s starts a counter of TPT_P periods, and the punishment depth grows with the size of the cut. A seller that has just cut its own price does not start a punishment for 8 periods, so it does not retaliate against a punishment that it caused.
  • Noisy reciprocity starts the same punishment only with a probability ρ\rho, which Bush-Mosteller reinforcement (Bush and Mosteller, 1955) updates against a learned profit aspiration.
  • Opponent shaping keeps a recursive least squares (RLS) model of the rival's reaction and a shaping gain ψ\psi that rises with the rival's prediction error. It sets its price to the reference price plus ψ\psi times a decaying memory of rival undercuts.
  • Demand-learning independent pricing (DLI) fits its own residual-demand curve by RLS and never observes the rival. It sets a markup from the estimated demand slope. Under this misspecified demand model it sustains PCI 0.78, in the spirit of Hansen et al. (2021).

The parameter ranges and update equations of all seven rules are in App. C.8.

AuthorsOpenReview ↗

Response to Reviewer Rmpi (Part 2/4)

W1: Scripted Rules, Labels and Ablation Operations (continued)

2. Labels

A scripted unit is response-dependent (RD) if its noise-free Adaptive response to the reference intervention (α=0.25\alpha=0.25, d=1d=1) exceeds 0.05 in magnitude at two or more lags k≥2k\ge2. All other units are non-response controls (NR). The condition k≥2k\ge2 excludes the one-period reaction of the static game. Myopic best response reacts at lag 1 about as strongly as reciprocal punishment (−0.10-0.10 vs. −0.126-0.126), but its echo is only −0.018-0.018 at k=3k=3, so it is NR. Reciprocal punishment, noisy reciprocity and opponent shaping are RD (Sec. 5.1 and App. C.6).

3. Ablation Operations

Each ablation changes one part of the full-grid surface.

AblationOperationAUROC
Full surfaceall features0.94
Remove dynamic responsekeep only R^(1)\hat R(1) for each cell and regime0.74
Remove matched controluse the opponent's pre-intervention price as the reference0.81
Merge Frozen & Adaptivepool both regimes into one surface0.84
Remove recovery featuresdrop TrecT_{rec} and D16:HD_{16:H}0.86
Convert to scalarkeep one depth per regime and direction0.87
Remove role swapdrop the reverse direction0.89

The dynamic response and the matched control are the two largest sources of identification performance (App. C.10).

W2: What the Method Shows about Learned Behavior

Thank you for this point. For learned sellers, the surface measures and predicts the response structure and shows whether a seller depends on its rival's actions. We add three analyses of learned sellers that need no labels, and one test on neural policies whose mechanisms are known.

1. Characterization of Learned Sellers

At the reference cell (α=0.25\alpha=0.25, d=1d=1), the surfaces of the 60 learned pairs (3 algorithms and 20 seeds) are summarized below. A response is persistent when its per-seed confidence interval excludes zero for three or more consecutive lags with k≥2k\ge2. Overshoot means a significant positive phase after the initial cut.

Alg.PCIRegimeR1R_1D1:5D_{1:5}Trec(ηrel)T_{rec}(\eta_{rel})PersistentOvershoot
SAC0.46F−0.0140.02846/201/20
A−0.0160.041910/208/20
TD30.39F−0.0100.02134/201/20
A−0.0110.03077/206/20
PPO0.27F−0.0040.00721/200/20
A−0.0040.00932/202/20

The surface resolves responses whose depth is 8 (SAC), 11 (TD3) and 38 (PPO) times smaller than that of reciprocal punishment (D1:5=0.34D_{1:5}=0.34). These responses build up over lags 2 to 5 and grow under Adaptive evaluation. Similar prices hide different responses here too. Among the 146 learned market pairs whose PCI differs by at most 0.02, 39 (27%) have non-overlapping 95% intervals for D1:5AD^A_{1:5}, and the largest such gap is 0.061 vs. 0.011 (App. B.8).

2. Attribution of Responses to Learning

The intermediate regimes RFAR^{FA} and RAFR^{AF}, written with the focal seller first, freeze one learner at a time. For the negative part of the response, D1:5A−D1:5FD^A_{1:5}-D^F_{1:5} splits into opponent updates (61%), focal updates (24%) and their interaction (15%), pooled over SAC and TD3. The positive responses in Fig. 5a are Adaptive overshoot. RAFR^{AF} keeps 78% of it and RFAR^{FA} keeps 14%, so the overshoot comes mainly from the focal seller's own learning (App. B.9).

AuthorsOpenReview ↗

Response to Reviewer Rmpi (Part 3/4)

W2: Validation on Implemented Remedies and Known Mechanisms

1. Validation by an Implemented Remedy

The remedy delays rival-price information, so that rivals' prices enter the observation with a 10-period lag. We apply it to all 60 learned pairs, continue Adaptive learning for 2×1052\times10^5 steps, and compare each pair with a matched run from the same snapshot and shocks without the remedy. ΔPCI is measured over the last 2×1042\times10^4 periods, and ΔCS is the change in logit consumer surplus. Each ranking rule treats its 12 top-ranked pairs. The surface score is D1:5AD^A_{1:5} averaged over the full grid and uses no labels. The 95% intervals come from 2,000 bootstrap resamples of pairs, with the ranking recomputed in each resample.

Ranking ruleMean ΔPCI, treated pairsΔCS, treated pairs
Random−0.06 [−0.08, −0.04]+4.3% [+2.9, +5.7]
PCI−0.09 [−0.13, −0.05]+7.5% [+4.2, +10.9]
Static deviation test−0.11 [−0.15, −0.07]+8.7% [+5.5, +11.9]
Response surface (no labels)−0.17 [−0.21, −0.13]+13.8% [+10.6, +17.0]
Best possible 12 pairs−0.21+17.2%

Ranking by the surface nearly doubles the consumer-surplus gain of ranking by PCI. The paired gain in ΔCS is +6.3 percentage points [+2.4, +10.1] over PCI and +5.1 [+1.0, +9.3] over the static deviation test, and the surface reaches 81% of the best possible effect. Over all 60 pairs, the Spearman correlation between the score and ΔPCI is −0.64-0.64 for the surface, −0.42-0.42 for the static deviation test and −0.31-0.31 for PCI (Sec. 5.2 and App. B.10).

2. Neural Policies with Known Mechanisms

To test identification on learned policies with a ground truth, we distill each scripted family into a neural policy. The student has the same hidden layers and the same 15-dimensional input as the SAC actor, and it is trained by DAgger-style behavior cloning with off-path price cuts in 30% of training episodes. On 600 pairs, the imitation error is 0.6% of ss on path and 1.8% off path. The classifier trained on the scripted pool, applied without refitting, reaches AUROC 0.90 [0.86, 0.93] against the family labels and 0.92 against the networks' own oracle labels. PD-16 reaches 0.77.

As a control, we clone on-path data only. These networks match their teachers on path within 0.5% of ss, but they differ off path by 21%, and 83% of the networks from RD families no longer respond by their own oracle labels. AUROC against the original family labels falls to 0.57, while against the networks' own oracle labels it stays at 0.91. So the surface tracks what a network actually does, not the family it was trained on. This is Proposition 1 inside a learned policy (App. B.13).

These analyses answer the mechanism question at the level the method supports. They show whose learning drives a response, they separate a seller that reacts to its rival from one that only re-learns its own demand (the hard negative below), and they recover known mechanisms inside neural policies. Outcome statistics cannot make any of these distinctions.

Comments on the paper

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Summary of Rebuttal

We thank the reviewers and the Area Chair for their time and helpful feedback. Reviewers 38qR and Rmpi found the problem well motivated, and Reviewer Rmpi found the Frozen and Adaptive evaluation useful. After reading the rebuttal, Reviewers 38qR and Aekw raised their ratings. Below we summarize the main changes.

1. Full specification (38qR W1, Rmpi W1). The revised paper now gives the prediction model, the classifier, the labels, the market, all seven scripted rules and every ablation step (Sec. 3.1, 5.1 and App. C.6 to C.10). When the baselines get the same structure, the response surface reaches a path RMSE of 0.031, against 0.052 and 0.079.

2. Learned sellers (38qR W2, Rmpi W2). The response surface measures learned responses that are 8 to 38 times smaller than those of reciprocal punishment. In 27% of learned markets with almost the same PCI, the responses are clearly different. The response surface shows which seller's learning drives each response. On neural policies with known mechanisms, it reaches AUROC 0.90 without refitting (App. B.8, B.9 and B.13).

3. Practical value (Aekw W1 and W2, 38qR W2). Developers, pricing-software vendors and platforms already hold the access the method needs, and monitors can test pricing software under recent remedies. On 60 learned seller pairs, choosing remedy targets by the response surface raises consumer surplus by 13.8%. Choosing the same number of pairs by PCI raises it by 7.5% (Sec. 5.2, App. B.10 and D).

4. Added value over deviation tests (Aekw W3, Rmpi W3). With the same budget of 15,000 transitions, the response surface reaches AUROC 0.91, and PD-16 with both regimes reaches 0.83. Most of this gain comes from the full response path and the matched control. One reference cell costs 0.75% of the training transitions. The theory tells a tester what to copy, and missing parts of the learner state change the Adaptive response by about 30% (App. B.4, B.5, B.12 and D.1).

All changes are marked in blue in the revised PDF, and the core code is in the supplementary material. We thank the reviewers again for comments that made the paper clearer and stronger.

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

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