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Withdrawn from ICLR 2027

Forecast Quality and Recourse in Semantic Facility Placement

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Forecasts guide the residency of service capabilities before demand is known, while compatible capacity may also be activated afterward at a recourse cost. We show that this distinction changes both the value of anticipation and the appropriate learning target. In the stated two-stage model, newly planned activations can be deferred without changing assignments, physical states, or total cost when emergency activation has no extra fee or delay. With paid recourse, a separable capability admits a Bayes one-step rule based on expected service savings clipped by capacity and activation cost. The conditional mean of demand generally does not determine that rule. A squared-loss calibration bound motivates learning the clipped value directly. On 12 matched generated conditions, selecting forecasts by local-search rollout cost reduces cost by 2.05% relative to EMA, but the improvement does not transfer to the same forecasts under MPC. A separate replay uses 104 structured API calls from 40 public annotated dialogues under 54 explicit cost mappings. The clipped target changes cost in only six mappings.

Primary area:
optimization
Keywords:
decision-focused learning, predict-then-optimize, optimization with recourse, facility location, stochastic optimization, online optimization, demand forecasting, model predictive control, resource allocation, agentic systems

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
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Paper summary

The paper studies semantic facility placement, where a controller forecasts demand for capabilities and decides whether to pre-provision them or activate them after demand arrives. It derives a deferral identity for the zero-surcharge case and, when emergency activation has extra cost, proposes forecasting expected recourse-clipped service value instead of raw demand counts.

Critical strengths
  • Interesting finding of distinction between prediction accuracy and decision quality.
Critical weaknesses
  1. Poor writing and problem-framing. The paper fails to establish a clear narrative connecting the motivating problem, the limitations of existing approaches, the proposed mathematical formulation, and the resulting practical benefit. The article starts with the problem and make the reader extra confused about what the application is, and the terms make readers extremely confused.
  2. The connection between the theoretical analysis and the empirical evaluation is unclear. The theory derives a decision-aligned forecasting target under a simplified single-capability model, but the main experiments evaluate forecasting methods combined with different placement controllers in a coupled setting. The paper does not establish that the theoretical result explains or predicts the observed end-to-end cost improvements. In particular, the experiments do not directly validate whether the proposed clipped-value target improves placement decisions under the assumptions of the theory, nor how its benefits extend beyond this simplified setting.
  3. I'm not certain if this article falls within ICLR's scope. This paper seems to focus on a narrowly specified operations-research model and controller evaluation, with limited contribution to "learning representatives".
Questions for authors
  1. What exact problem remains unsolved, and can the authors give a concrete example showing why advance placement is needed, emergency recourse is insufficient, and existing prediction/placement methods fail?
  2. Beyond decision-aware forecasting for a specific cost, what genuinely novel learning insight or method does the paper contribute versus SPO and learning-augmented facility location, and how is it reflected in the evaluation?
  3. Under realistic conditions, does the method deliver meaningful gains versus oracle placement, reactive no-prewarm activation, and decision-focused learning baselines when startup latency, shared resources, and real serving costs are measured rather than modeled?
2 comments

Thank you. The paper asks which quantity should be learned when a placement decision can be repaired after demand is observed. It does not establish that agent platforms generally need advance placement or claim improved deployed serving.

1. The problem and a separating example

A forecast chooses residency before demand arrives. Later activation can recover service, but may cost more. That option changes the prediction target. When emergency activation has no additional fee or delay, Theorem 1 shows that advance activation has no intrinsic advantage. This is a negative result about the model, not a claim that advance placement is always necessary.

With paid recourse, even a perfect conditional-mean forecast can recommend the wrong action. Consider one capability with local capacity U=12U=12, residency cost f=4f=4, toggle cost m=1m=1, emergency fee γ=1\gamma=1, and unit local-service saving b−c=1b-c=1. One context has demand 5.5 surely. Another has demand 0 or 11 with equal probability. Both means are 5.5 and capacity never binds. Yet E[min⁡(N,6)]E[\min(N,6)] equals 5.5 in the first context and 3 in the second. The activation threshold is 5, so the optimal one-step decisions differ. Early activation saves 0.5 in the first context, while waiting saves 2 in the second. A predictor retaining only the conditional mean cannot distinguish these actions. This example concerns modeled costs, not measured deployment gains.

2. The learning contribution and related work

Decision-oriented training is established by Smart Predict-then-Optimize [1]. DF² [2] learns expected optimization objectives, and Diffusion-DFL [3] learns conditional distributions for stochastic decisions.

Our specific result derives the statistic induced by this execution model,

μ(H)=E[min⁡{(b−c)min⁡(N,U),f+m+γ}∣H],\mu(H)=E[\min\{(b-c)\min(N,U),f+m+\gamma\}\mid H],

with opening threshold f+mf+m and retention threshold f−mf-m. Proposition 3 converts squared prediction-risk excess for this target into a bound on excess one-step decision cost. Appendix A.5 identifies the additional continuation term required over a horizon. The claim is therefore a model-specific target and risk characterization, not a new general decision-focused framework, a competitive algorithm, or a representation architecture.

Under the same empirical smoothing, a conditional-distribution estimator exactly reproduces the value regressor. We will add this equivalent comparator. Our theorem identifies the required functional, not superiority over distributional learning.

3. What the experiments do and do not test

The coupled experiment and the separable replay answer different questions. Table 1 tests whether forecast selection transfers between controllers. It never trains the clipped target, and cannot validate that target under shared capacity. Table 2 tests the target in the separable model where the theorem applies. This distinction will appear beside both tables.

We checked the replay's 86 action disagreements against an intermediate capacity-only expected-value calculation. All 86 occur at the emergency-cost clipping step, not the capacity-clipping step. They correspond to 43 distinct dialogue/epoch/API coordinates across repeated mappings. The small 0.25% aggregate gain remains a mechanism check, not evidence of broad practical superiority.

We also added the missing optimal one-epoch placement control. Ridge's gain over EMA is +0.23%, with interval [−0.16,0.59][-0.16,0.59]%, compared with -1.66% under local search and +1.14% under three-epoch MPC. Thus the original comparison establishes controller dependence but does not isolate search from horizon effects. In full no-advance rollouts with matched retention-selection rules and optimal recourse, local-cost calibration improves over EMA by only 0.079%, interval [−0.017,0.190][-0.017,0.190]%. These controls narrow the interpretation.

4. Practical evidence, presentation, and venue fit

We have no measured startup-latency, shared-resource serving, or deployment-cost comparison demonstrating gains over contemporary decision-focused systems. The API calls are externally authored, but their resource prices are counterfactual. No realistic operating regime is established by those mappings.

The introduction will state three questions. When does recourse remove the value of advance activation? When it does not, which conditional target is sufficient? How do forecast selection and downstream control interact? Optimization and learning theory are listed ICLR topics. We ask that the contribution be assessed on its target characterization and evidence, not as a deployed serving system. Please identify which stated result underlies the soundness concern, distinguishing correctness from limited empirical breadth.

[1] Elmachtoub and Grigas. Smart Predict-then-Optimize, Management Science 2022.

[2] Kong et al. DF², UAI 2025.

[3] Zhao et al. Diffusion-DFL, ICLR 2026.

I appreciate the authors' response. However, the current presentation of the revision still does not fully address my concerns.

Reviewer_fK4mOpenReview ↗
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Paper summary

The paper examines forecasting for persistent capability placement with post-demand activation. It derives a pathwise deferral identity for activation when there is no emergency surcharge or delay, along with a one-step activation/retention rule for a separable local–remote capability. The rule applies a threshold to the conditional expectation of a service-value transform clipped by capacity and emergency-activation cost, with an associated squared-loss plug-in bound. The experiments cross forecast choices with local search and MPC on generated placement instances. They also compare count and clipped-value estimates in a separable replay of annotated API-Bank call sequences under fixed cost mappings.

Critical strengths
  1. The analysis explicitly states the execution assumptions and distinguishes advance activation from retention. This helps interpret forecasting results in systems that allow post-demand repair.

  2. The paper distinguishes among generated scenarios, annotated-call replay, and hardware-calibrated simulation, and reports actual solver status and gaps. These qualifications make the experiments easier to interpret.

Critical weaknesses
  1. The replay does not isolate the empirical role of emergency recourse from that of ordinary capacity clipping. The target is T(N) = min{(b−c)N, (b−c)U, f+m+γ}. Under the grid disclosed in Eq. (47), the emergency-cost bound is strictly below the capacity bound in only 24 of the 54 mappings; in the remaining 30, it adds no further clipping. Table 2 groups the results by surcharge, but neither the table nor the 86-decision diagnostic attributes the changes to these two mechanisms. This distinction matters because Eq. (48) exactly integrates T under the same smoothed empirical conditional demand distribution. With demand supported on {0,1,2}, this distribution is also straightforward to estimate and can be reused across mappings. The comparison therefore tests retaining distributional information versus transforming a mean. It does not yet establish which of the observed benefits specifically test the proposed emergency-recourse mechanism, even though the one-step target derivation itself is valid.

  2. The forecast-transfer comparison changes both the optimizer and the decision horizon, while the replay does not resolve the role of persistent state. Local search optimizes a single predicted epoch, whereas MPC optimizes three recursively forecast epochs. The ranking reversal could therefore result from horizon-dependent forecast errors and future switching costs, even without a difference in optimization quality. An exact one-epoch optimizer would separate these explanations. Separately, the replay uses a one-step regressor that omits the continuation correction in Eq. (9). Although this limitation is acknowledged, the clairvoyant horizon reference also has access to future demand and cannot isolate its effect under the same information. Resetting the state at every dialogue and grouping calls in pairs further determine the available opportunities for persistence. These controls are important for understanding whether the reported conclusions concern optimization, the forecast horizon, or the short-state dynamics imposed by the evaluation.

Questions for authors
  1. Among the 86 action disagreements, which occur where recourse adds clipping beyond capacity alone, and what are their separate cost effects?

  2. Does the forecast-ranking reversal persist when comparing local search with an exact one-epoch optimizer, before introducing MPC’s three-epoch horizon?

  3. Given the same observed information, how much of the remaining decision error is due to target estimation, and how much is due to omitting the continuation term D_t?

  4. How sensitive are the 86 action disagreements to grouping calls in pairs and resetting placement after each dialogue?

  5. At γ=0, how much of the coupled-policy difference remains relative to a no-advance baseline with matched retention logic and optimal recourse?

1 comment

Thank you for identifying the two missing separations. We have now isolated capacity versus recourse clipping and added a one-epoch optimizer control. We also distinguish the conclusions these checks support from quantities the submitted experiments cannot identify.

1. Which of the 86 changes are due to recourse clipping

Write S(N)=(b−c)min⁡(N,U)S(N)=(b-c)\min(N,U) and h=f+m+γh=f+m+\gamma. Using the same training weights and previous state, we compare three targets

A=T(E^[N]),B=min⁡(E^[S(N)],h),C=E^[min⁡(S(N),h)].A=T(\widehat E[N]),\quad B=\min(\widehat E[S(N)],h),\quad C=\widehat E[\min(S(N),h)].

Here A−BA-B isolates the capacity-related Jensen gap and B−CB-C isolates the emergency-cost Jensen gap. The targets obey A≥B≥CA\ge B\ge C. In all 86 reported disagreements, thresholding BB gives the same action as AA, while thresholding CC changes it. Thus none of these action changes is explained by capacity clipping alone. All occur in the 24 mappings with an active emergency cap. The remaining 30 mappings have no disagreements. Twenty changes concern retention at γ=0\gamma=0, and 66 concern cold activation at γ=0.5\gamma=0.5. On the count policy's common state, the former save 3.60 modeled cost units and the latter save 4.20, including four adverse changes. These are immediate common-state effects, not complete-rollout savings.

The analytical example on p. 5 also separates the mechanisms. It has U=12U=12 and demand either 5.5 surely or 0/11 with equal probability. Capacity never binds. Both means are 5.5, but with f=4,m=1,γ=1,b−c=1f=4,m=1,\gamma=1,b-c=1, the clipped expectations are 5.5 and 3, on opposite sides of the cold threshold 5.

You are correct about the distributional baseline. With the same smoothed conditional probabilities, ∑n=02T(n)p^(n∣H)\sum_{n=0}^2 T(n)\hat p(n\mid H) is algebraically identical to the submitted value estimator. We checked this numerically, with maximum difference below 2×10−162\times10^{-16}. A conditional distribution can be reused across cost mappings. Our contribution is to identify the sufficient functional for a fixed decision, not to outperform that distributional estimator. We will state this equivalence explicitly and relate it to DF² [1] and sufficient decision proxies [2].

2. One-epoch optimization control

We froze all original forecasts and added a one-epoch mixed-integer planner with the same costs, reserve, movement weight, and realized assignment rule. All 1,440 test calls returned optimal status, with maximum reported gap below 1.7×10−141.7\times10^{-14}. Ridge versus EMA changes from -1.66% under local search to +0.23% under one-epoch optimization, with within-family interval [−0.16,0.59][-0.16,0.59]%, versus +1.14% under three-epoch MPC. The point estimate changes sign, but the one-epoch interval includes zero. Therefore the submitted reversal cannot be attributed solely to search quality. Horizon and state effects matter, and we will narrow that interpretation.

3. Target error versus omitted continuation

The future-informed reference cannot identify this split under the predictor's information, and we will not use its gap for that purpose. Let μ0=E[min⁡(S,h)∣H]\mu_0=E[\min(S,h)\mid H] and μD=E[min⁡(S−Dt,h)∣H]\mu_D=E[\min(S-D_t,h)\mid H]. Since clipping is 1-Lipschitz,

∣μ^0−μD∣≤∣μ^0−μ0∣+E[∣Dt∣∣H].|\hat\mu_0-\mu_D|\le|\hat\mu_0-\mu_0|+E[|D_t|\mid H].

This separates target-estimation error from omitted continuation analytically. Applying it to a complete controller also requires accounting for nonoptimal post-observation decisions. The experiment does not estimate the true conditional continuation value, so we cannot assign a defensible numerical fraction of its remaining error to either source.

4. Grouping and state resets

After rebuilding and refitting the replay with blocks of one, two, and three calls, the disagreement counts are 58, 86, and 220, and mean mapping-wise gains are 0.17%, 0.25%, and 0.40%. With two-call blocks and physical state carried between held-out dialogues, 20 fixed random dialogue orders give gains of 0.20–0.36%. This is an artificial carry-over sensitivity check, not observed cross-dialogue persistence or timing. We will report the dependence rather than treat the original grouping as operationally validated.

5. No-advance control at zero surcharge

We also ran full coupled rollouts that retain each local planner's retention-selection rule, suppress new planned openings, and optimize realized recourse. Each policy uses its own evolving state. Local-cost calibration's gain over EMA is then 0.079%, interval [−0.017,0.190][-0.017,0.190]%, rather than the original 2.05%. This rules out interpreting Table 1 as evidence of intrinsic early-activation value. The positive result is the recourse-dependent target characterization and the diagnosed controller interaction, not a universal anticipatory-placement advantage.

[1] Kong et al. DF², UAI 2025.

[2] Schutte et al. Sufficient Decision Proxies for Decision-Focused Learning, IJCAI 2026.

Reviewer_bhGCOpenReview ↗
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Paper summary

The paper studies how demand forecasts should influence the advance placement of service capabilities when additional compatible capacity can be activated after demand is observed. It formalizes a two-stage, capacitated facility-placement model with residency, switching, connection, rejection, and optional emergency-activation costs. Compatibility is specified by a fixed mask rather than inferred from semantic similarity.

Its first theoretical result is a pathwise deferral identity: if emergency activation has neither a surcharge nor a delay, every feasible execution can defer newly planned activations while preserving its assignments, final physical state, and total cost (Theorem 1). The second result concerns a separable local-versus-remote capability. The Bayes-optimal one-step decision depends on the conditional expectation of a capacity- and recourse-clipped service saving, rather than only the conditional mean demand (Theorem 2). A threshold-regression excess-risk bound motivates predicting this clipped value directly (Proposition 3). The paper also distinguishes this one-step target from the continuation value required for finite-horizon decisions.

The experiments cross count-MSE and solver-cost forecast selection with local search and three-step MPC on 12 held-out generated conditions. Local-cost calibration reduces modeled cost by 2.05% relative to EMA under local search, but by only 0.05% under MPC; conversely, MPC-selected forecasts worsen local-search cost by 2.04% (Table 1). A separate, separable replay uses 104 annotated API calls from 40 public dialogues across 54 hypothetical cost mappings. Direct clipped-value regression changes aggregate cost in six mappings, giving a mean mapping-wise reduction of 0.25% (Table 2). Additional synthetic and hardware-parameterized simulations are reported, but the study does not evaluate a deployed serving system.

Critical strengths
  1. The paper gives a precise and useful account of when anticipation has economic value. Theorem 1 and Appendix A.1 establish the deferral result at the level of feasible executions, including both transition charges and persistent physical states; they do not incorrectly infer that a greedy repair heuristic will reproduce the same solution. Theorem 2 then identifies the recourse-clipped conditional value and distinct opening/retention thresholds, while Proposition 3 supplies a simple decision-calibration bound. The finite-horizon qualification in Appendix A.5 is particularly important since it prevents the one-step result from being presented as an optimal dynamic policy. Together, these results isolate a meaningful modeling assumption that can otherwise confound claims about forecast-driven pre-provisioning.

  2. The experiments separate prediction, optimization, and execution effects comparatively carefully. The primary experiment freezes forecast choices after disjoint fitting and calibration periods, evaluates the same forecasts under both downstream solvers, and uses common offered demand, initialization, and recourse accounting (Section 3, Table 1, Appendix D.1). The contrast between ridge's 15.06% improvement in count error and its opposite cost effects under local search (-1.66%) and MPC (+1.14%) is informative. Solver termination statistics and the clock-cap sensitivity experiment (Appendix D.2) also distinguish requested optimization budgets from achieved solution quality. The authors report negative and null findings and explicitly restrict the interpretation of their synthetic and API-call results, which increases confidence in the narrower conclusions.

Critical weaknesses
  1. The main theoretical learning target lacks convincing validation in the more relevant coupled setting. The clipped-value regressor is tested only in a separable replay with one optional capability per API, while the main coupled experiment selects among nine EMA/ridge mixtures by solver rollout cost and never regresses on the proposed target (Sections 3–5). These results are also obtained without an emergency surcharge (Section 2), the regime in which Theorem 1 shows that advance activation has no intrinsic cost advantage. Table 1 therefore supports solver-dependent forecast selection, but does not show that learning the clipped target improves capacitated placement. The replay adds limited evidence: six of 54 hypothetical mappings improve, 48 tie, and the mean gain is 0.25% (Table 2).

  2. The empirical evidence for broader usefulness is narrow. The crossed comparison uses 12 generated conditions (four families, three seeds each) and 24 test epochs, and its bootstrap intervals resample seeds within the same families, so they cannot establish generalization to other workloads (Section 5). Cost selection is not consistently better even for its own solver: under MPC, the count-fitted ridge forecast improves cost by 1.14%, versus 0.71% for MPC-cost selection (Table 1). All costs are modeled quantities: connection costs are dimensionless (Appendix F), and the replay uses 40 dialogues with hand-specified capacities and prices (Appendix D.4). A 2.05% reduction therefore cannot be translated into latency or monetary savings.

Questions for authors
  1. In the coupled model, is there a per-bundle analogue of the clipped-value target (for example, a heuristic that clips each bundle's predicted saving by its capacity and recourse cost) that could be compared with count prediction and solver-cost calibration on the same coupled instances with positive recourse surcharges? Section 4 already limits the target to separable decisions; this comparison would show whether the mechanism behind Theorem 2 still matters once capacities are shared, which Table 1 does not currently address.

  2. For the zero-surcharge coupled experiment, can you quantify how much of the forecast-dependent improvement is attributable to retaining existing capabilities rather than opening new ones or changing assignment/search outcomes? Theorem 1 rules out an intrinsic advantage from early opening, but does not by itself identify which remaining mechanism explains Table 1.

  3. How stable are the Table 1 cross-solver rankings across additional independent seeds or a held-out workload generator? Please report the distribution of paired effects by family and clarify whether the favorable local-search cost-selection result persists beyond the four fixed generated families. The current within-family bootstrap is informative but has a limited scope.

  4. For the API-call replay, how sensitive are the six positive mappings and the 0.25% mean gain to the selection of dialogues and the coarse last-API context? A dialogue-level uncertainty or leave-family-out analysis, alongside the number of distinct changed decisions per mapping, would help distinguish a robust target effect from a small number of repeated threshold crossings.

Suggestions for future work, not conditions for acceptance:

  • Test resource-sharing, startup-delay, and measured activation-cost regimes. The paper correctly states that these mechanisms are outside its current model, but they are central to interpreting whether the derived target is useful for an operational scheduler.

  • Consider richer probabilistic or decision-focused forecasting baselines. The current nine-point EMA/ridge grid is appropriate for a controlled mechanism study, but does not establish how the proposed approach compares with stronger prediction-and-optimization methods.

2 comments

Thank you for recognizing the deferral result, the distinction between activation and retention, and the matched experimental design. Your central concern is correct. Table 1 does not validate clipped-value learning under shared capacity. We separate that open question from the results the paper establishes and add the following targeted controls.

1. Coupled learning target

A bundle-wise clip cannot generally be added across bundles because shared resources make their service values interdependent. A precise analogue is the conditional marginal recourse value. Let Rγ(p,n∣s)R_\gamma(p,n\mid s) be the minimum one-epoch cost, including optimal repair, for planned placement pp, realized demand nn, and previous state ss. Comparing pp with the placement p+ip^{+i} that additionally activates bundle ii requires predicting E[Rγ(p,N∣s)−Rγ(p+i,N∣s)∣H]E[R_\gamma(p,N\mid s)-R_\gamma(p^{+i},N\mid s)\mid H]. Its sign determines the better of those two plans. In the separable model this reduces to the clipped-value threshold. With coupling, it depends on the other resident bundles and cannot be replaced by independent clipping without an additional approximation argument. We have not established the performance of a learned coupled marginal model. We will make that boundary explicit beside Table 1 rather than imply that solver-cost calibration tests Theorem 2.

2. What explains the zero-surcharge gains

We ran complete no-advance controls on the same 12 held-out conditions, keeping the frozen forecasts and local retention-selection rule, replacing each plan by p∧sp\wedge s, and optimizing realized recourse. Each policy evolves from its own resulting state. Local-cost calibration improves over EMA by only 0.079%, with within-family bootstrap interval [−0.017,0.190][-0.017,0.190]%, compared with 2.05% under the original execution rule. Keeping planned activations but replacing greedy repair by optimal recourse changes that comparison to -0.265%. All 2,880 recourse solves returned optimal status. These are controlled policy comparisons, not an additive causal decomposition. They show that the original gain is execution-rule dependent and does not establish an intrinsic benefit from early activation or a reliable retention-only advantage.

This agrees with Theorem 1. At γ=0\gamma=0, each early-activation execution has a deferred counterpart with the same assignments, final state, and cost. Prediction may change retention or heuristic decisions, but those changes must not be attributed automatically to advance provisioning.

3. Robustness and solver dependence

The local-cost-selected forecast has positive family-mean improvements of 2.62%, 2.59%, 0.62%, and 2.37% for the API-Bank-inspired, ToolBench-inspired, MCP-inspired, and AppWorld-inspired generators, respectively. These remain four generated families, not four production datasets.

We also added an optimal one-epoch placement control with the original forecasts and execution rule. Ridge's mean gain over EMA is 0.23% with interval [−0.16,0.59][-0.16,0.59]%, between the original local-search result of -1.66% and three-epoch MPC result of +1.14%. Thus the original comparison does not isolate search quality from horizon effects. No additional independent workload family has been evaluated, and the bootstrap remains conditional on the four supplied families.

4. Replay sensitivity and distinct decisions

The 86 common-state disagreements correspond to 43 distinct dialogue/epoch/API coordinates in 30 dialogues involving four APIs. Across the six affected mappings the counts are 33, 9, 1, 33, 9, and 1. They are repeated counterfactual evaluations, not 86 independent observations.

We separated capacity clipping from emergency-cost clipping. Every disagreement occurs at the emergency-cost clipping step. There are no disagreements in the 30 mappings where that cap is inactive. The same-state changes lower immediate cost in 82 cases and increase it in four.

Leaving out each of the 38 distinct sequence groups and refitting both estimators gives an aggregate mean gain ranging from 0.145% to 0.512%. Individual mapping effects can reverse. Rebuilding epochs from one, two, or three consecutive calls gives mean gains of 0.17%, 0.25%, and 0.40%. The effect is small and depends on the mapping and grouping.

The distributional comparison is also important. Under the same smoothed empirical conditional law, summing T(n)T(n) against the predicted count probabilities reproduces clipped-value regression to numerical precision. We do not claim superiority over a correctly estimated distribution. Recent DF² [1] and Diffusion-DFL [2] study expected-objective and distributional learning. Our contribution is the explicit recourse-induced target and its limits, not the general idea of decision-focused learning. Startup delays and measured deployment costs remain untested.

[1] Kong et al. DF², UAI 2025.

[2] Zhao et al. Diffusion-DFL, ICLR 2026.

Thank you for the additional analyses. They help clarify the original results, and I appreciate your openness about their limitations. I still find the theoretical result useful, but the proposed learning target itself has only been tested in the small separable replay. This leaves my main concern about its usefulness with shared capacity unresolved, so I will keep my rating. I have no further questions at this stage.

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