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Under review as a conference paper at ICLR 2027

Not Every Step Matters: Learning Multi-Turn LLM Routers

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Abstract

LLM agents complete tasks through a sequence of model calls and environment interactions, causing inference costs to accumulate. Routing each call to an appropriate model offers a way to reduce these costs while maintaining task performance. However, the capabilities needed can change over the course of a task, and choosing a different model does not matter equally at every step. We find that the value of model selection is concentrated at a small subset of steps. We call these steps pivotal: differences in the capabilities of candidate models at the same agent history lead to substantially different final task outcomes. A step can be difficult or critical to the task without being pivotal if changing the model makes little difference. We identify pivotal steps through counterfactual rollout trees and use their model comparisons to guide data collection, router training, and inference. Our router matches or outperforms the strongest fixed-model baseline on five of six interactive benchmarks. It also reduces total inference cost by 47.8% across the 473-task evaluation suite.

Primary area:
foundation or frontier models, including LLMs
Keywords:
large language models, multi-turn agents, model routing, counterfactual learning, efficient inference

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_c517OpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
3
Soundness
3
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Paper summary

The paper proposes a framework for learning per-step model routers for multi-turn LLM agents. It uses counterfactual rollout trees to identify pivotal states, where candidate models differ substantially in their best recorded downstream returns. These comparisons guide data collection and training with ranking, performance, and cost objectives. At inference time, predicted model differences adjust the cost penalty. The framework is evaluated on six interactive benchmarks, including three OOD settings.

Critical strengths
  1. A useful contribution to the design of routing supervision.

The central insight is that a difficult or important step is not necessarily informative for learning model selection: if all candidate models preserve similar outcomes, there is little performance preference to learn. This shifts attention from imitating a selected model at every state to identifying where comparative supervision is useful. I find this a meaningful refinement of search-based routing, with a concrete consequence for how training data should be collected and selected.

  1. Evidence that selective supervision can improve routing rather than merely reduce training data.

The filtering results provide a useful empirical finding: training on 32.7% of the available examples improves mean online performance over the plain all-state recipe on all three source benchmarks. The fifteen additional all-state alternatives make this more informative than a single full-data comparison, although small differences should not be interpreted as statistically established superiority. Together with the online cost-quality results, this supports the practical value of concentrating supervision on model-discriminative states (Table 3 and Appendix D.4).

Critical weaknesses
  1. Comparison with the closest sequential routers could be more direct.

The paper cites DialRouter, MTRouter, and Hera, but does not evaluate against these closely related approaches. Since search-derived supervision and outcome-based multi-turn routing already appear in prior work, a more direct comparison would help establish the added value of pivotal-state selection. Appendix A.5 also identifies Router-R1 as an adaptation rather than a faithful reproduction. The internal ablations are useful, but leave the relative advantage over the closest existing frameworks less clear.

  1. The performance and cost targets do not necessarily describe the same continuation.

Equation 1 backs up the highest discovered return, whereas Equation 5 targets the cheapest continuation, which need not achieve that return. Combining these estimates in Equation 9 can therefore associate a favorable outcome with a cost that belongs to a different, potentially unsuccessful path. This limits the interpretation of the cost-aware score and merits discussion or validation. The concern primarily affects the cost-aware extension; it does not directly invalidate Table 2's performance-only results at lambda = 0.

Questions for authors
  1. Could the authors provide a matched comparison with an appropriate closest sequential router, particularly DialRouter, to clarify the additional benefit of pivotal-state selection over search-derived routing supervision?

  2. Does pivotal-only training retain its advantage over a random subset of the same size when optimizer-update counts and learning-rate schedules are matched? This would help distinguish informative selection from generic data reduction and optimization effects.

  3. How should the combined performance-cost score be interpreted when its two targets may correspond to different continuations? Is there evidence that the cost predictions track the costs incurred by the deployed router under different cost preferences?

3 comments
AuthorsOpenReview ↗

Rebuttal Part 1

We thank the reviewer for recognizing the value of selective routing supervision and for the careful assessment of the all-state comparisons. We address the closest-method comparisons, the random control, and the performance–cost interpretation below.

Weakness 1 / Question 1: Closest sequential routers and the scope of Router-R1

We compare simplified forms of the learning strategies underlying these routers within a common five-model, terminal-reward setting. Our MSE, CE/Anchored CE, and all-state controls serve this purpose: they compare outcome regression, return-derived model preferences, and the use of every collected decision state. The relationship to the closest methods is therefore more specific than a general comparison with unrelated routers:

Closest frameworkShared learning strategy represented in our controlsFramework-specific components not reproduced
DialRouterSearch-derived model-choice supervision, represented by our CE objectives; the all-state control additionally tests training without pivotal filtering.Its future-state retrieval architecture and dialogue simulator/reward model. Our targets use distributions of benchmark terminal returns rather than its selected search actions.
MTRouterPredicting downstream outcomes for state–model pairs, represented by our pointwise MSE objective and performance-based selection.Its joint history–model embeddings and error-adjusted trajectory targets. Our performance targets use tree-backed values rather than its adjusted observed returns.
HeraLearning model preferences from returns at shared states and using cost in routing, reflected in our within-state objectives and cost-aware inference.Its binary device–cloud setting, action-agreement initialization, and iterative rollout-based preference construction. Our five-model targets and cost objective differ from its binary preference labels.

We prioritized these common-protocol controls because importing the full frameworks would change several factors at once. For MTRouter, preserving its outcome estimator would also introduce its model representation, error adjustments, and trajectory-collection scheme. For Hera, moving from two device–cloud candidates to five models requires changing its binary labels and cloud-call cost definition, as well as reproducing its two-stage training. DialRouter additionally requires adapting dialogue feedback and future-state retrieval to environment-terminal rewards. The simplified controls retain the shared learning ideas while allowing us to test the training-state selection under a fixed encoder, feedback source, and collected dataset. They are strategy-level counterparts, not measurements of the full published systems.

The most direct comparison is Table 3: with the same encoder and Anchored CE objective, the all-state recipe scores 0.373/0.481/0.653, while pivotal-only training scores 0.422/0.573/0.710 on SQL/WebShop/SWE-bench using 32.7% of the examples. Appendix D.4 adds fifteen full-data variants. These results establish the incremental value of the selection rule in the common pipeline; a ranking against complete DialRouter, MTRouter, or Hera implementations would require their full evaluation.

Question 2: Pivotal selection versus a matched-size random training subset

The existing ablations establish the effectiveness and data efficiency of pivotal-only training. Table 3 compares the same encoder and Anchored CE objective with all decision states versus the pivotal subset. Retaining 32.7% of the examples improves the equal-benchmark mean from 0.502 to 0.568, with gains on all three source benchmarks.

The evidence extends beyond a single full-data baseline. Appendix D.4 evaluates fifteen alternatives that retain all states while incorporating pivotality through reweighting, gating, adaptive temperatures, or objective selection. Pivotal-only training remains competitive with their strongest configurations while using substantially fewer examples. These comparisons support filtering as an effective way to use comparative supervision in our pipeline.

A matched-size random subset would further distinguish informative selection from generic data reduction and optimization effects. Our existing training comparisons do not isolate these factors, since dataset sizes and optimizer-update counts differ. We therefore interpret the results as evidence for an effective, data-efficient training recipe, without attributing the entire improvement exclusively to the quality of the selected states. The Random baseline in Table 2 is an inference-time control and serves a separate purpose from this training-subset comparison.

AuthorsOpenReview ↗

Rebuttal Part 2

Weakness 2 / Question 3: Performance–cost scoring and its online evaluation

Equation 9 is a routing decision rule that combines separately learned performance and cost signals. The performance target favors the highest backed return, while Eq. 5 uses the cheapest expanded continuation. Although both heads train on the same state–model transitions, their future choices can differ. The combined score therefore expresses a preference over models using these two signals, rather than an exact expected net return under a single continuation policy. Appendix A.2 specifies the cost signal as a discounted, dimensionless proxy based on model-price ratios.

We evaluate the resulting decisions through online task outcomes and realized model-call costs. Both quantities are recorded on the same executed trajectory. The evaluation harness computes dollar cost from the actual input/output token usage of each selected model. Thus the reported end-to-end results assess the performance and expenditure of the policy that actually runs, rather than combining the success of one path with the cost of another.

The λ/r analyses examine how this decision rule responds to cost preferences: Figure 3 varies λ, Figure 4 compares state-dependent and fixed cost penalties, and Appendix E.4, Figure 11 jointly varies λ and r. Together, these analyses examine the operating points obtained by changing the strength and state dependence of the cost penalty. Tables 10–11 separately provide the full benchmark and aggregate quality–cost results at λ = 0. The inference sweeps evaluate the practical use of the cost signal in model selection.

At λ = 0, Table 2's action selection uses only the performance score. Cost supervision still contributes to learning the shared representation: Appendix D.3 shows that retaining the cost loss under Anchored CE raises SQL performance from 0.348 to 0.422 and WebShop performance from 0.499 to 0.573, with λ = 0 throughout. This provides additional evidence for the usefulness of cost supervision alongside the evaluation of cost-aware inference.

Comment on statistical significance: Small differences from the best all-state variants

The main finding is the substantial improvement over the plain all-state recipe with much less supervision. The complete set of comparisons is:

Training recipeData shareSQLWebShopSWE-benchEqual-benchmark mean
Plain all-state100%0.3730.4810.6530.5023
Benchmark-wise best of 15 all-state alternatives100%0.4020.5660.7030.5570
Pivotal-only32.7%0.4220.5730.7100.5683

The improvement over the plain recipe is 6.60 percentage points in the equal-benchmark mean. Against the benchmark-wise best full-data alternatives, the mean difference is 1.13 points. The latter comparator selects a different best setting for each benchmark from the fifteen tested mechanisms; pivotal-only uses the common reported recipe. This makes it a useful comparison with a broad set of full-data approaches, but not a statistical demonstration of superiority over every alternative.

All learned rows report three independent training seeds, and Appendix D.4 presents their variation. We therefore interpret the small gaps as showing that the compact supervision set remains competitive with the tested full-data alternatives.

Thanks for the response. I accept the clarification that Eq. 9 is a preference rule and that the reported costs come from the same executed trajectories, which addresses my second concern. However, my concern about comparison with more relevant baselines remains, and the matched-size random-subset control was not run, so the advantage of pivotal selection over generic data reduction is still unestablished. I am keeping my score at 3.

Reviewer_n5rVOpenReview ↗
Rating
3
Confidence
4
Informativeness
3
Presentation
3
Soundness
2
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Paper summary

The paper defines pivotal states as states where different model choices lead to materially different downstream task outcomes. It uses MCTS-based counterfactual tree collection to identify such states, trains a router only on pivotal-state comparisons, and evaluates online on six interactive benchmarks. Pivotal-only training uses 32.7% of state-model examples and reportedly reduces cost by 47.8% while matching or exceeding strong fixed-model baselines on five benchmarks.

Critical strengths

The pivotality definition is conceptually clean: it separates task difficulty from routing value by asking whether model choice changes the reachable outcome. This is a useful distinction for adaptive model routing.

The online evaluation is stronger than many offline routing papers. The pivotal-only training result, using 32.7% of examples and outperforming all-state alternatives, provides direct evidence for the data-selection hypothesis.

Critical weaknesses

Pivotality is defined relative to the candidate model pool and the collected counterfactual tree. If the model pool or exploration budget changes, the pivotal labels may change, which limits deployability.

The OOD average is slightly below ALL-STRONG, and the pivotal threshold D(s) ≥ 0.5 is natural for binary rewards but somewhat arbitrary for graded rewards. The paper acknowledges this, but the robustness evidence is not yet decisive.

Questions for authors

How stable are pivotal labels under changes to the candidate model pool or exploration budget?

How do you explain the OOD average being slightly below ALL-STRONG despite the claimed five-of-six match-or-exceed result?

How sensitive are the online results to the pivotal threshold and to the MCTS collection budget?

Are training and test task splits fully disjoint for all source and OOD benchmarks?

3 comments
AuthorsOpenReview ↗

Rebuttal Part 1

We thank the reviewer for recognizing the distinction between task difficulty and routing value, and the strength of the online evaluation. We address label stability, online sensitivity, cross-domain performance, and data separation below.

Weakness 1 / Question 1: Label stability under changes in the model pool or exploration budget

Our method requires useful comparisons for the available models, rather than labels that remain unchanged after the models change. If a new candidate introduces a return difference exceeding the pivotal threshold among branches previously tied in the collected tree, the label should change. Such a change reflects the intended meaning of the label. For deployment, modular model-specific heads offer an adaptation route, while observations for the new model and any affected continuations must be added or refreshed. Our OOD results establish transfer across task domains with a fixed panel; they do not establish invariance to panel replacement.

The benefit of pivotal filtering in Table 3 cannot be attributed to using a different model panel or collecting a different set of trees for that comparison. The pivotal-only and all-state recipes share the panel and the underlying collected trees. They score 0.422/0.573/0.710 versus 0.373/0.481/0.653 on SQL/WebShop/SWE-bench. Thus the comparisons obtained under the reported collection protocol are useful for learning, even though those labels are conditional on the available search evidence.

Weakness 2 / Question 2: OOD averages and the five-of-six statement

The OOD result is a 0.5-point macro performance gap to ALL-STRONG with 26.4% lower macro cost, while outperforming every reported prior router in OOD macro performance. Our score is 0.618, versus 0.623 for ALL-STRONG and 0.570 for RouteLLM, the strongest reported prior router on this measure. This is the quality–cost result supported by Tables 2 and 11.

The five-of-six statement is consistent with these averages: our reported means exceed ALL-STRONG on all three source benchmarks and CTF, tie on ALFWorld, and are lower on τ-bench. Within the OOD suite, the τ-bench loss is larger than the CTF gain. Counting benchmark wins therefore gives a different summary from averaging their scores.

The same trade-off appears with task weighting: our OOD micro score is 0.570 versus 0.577 for ALL-STRONG, with 28.1% lower cost. It exceeds the best reported prior-router micro score, 0.508, by 6.2 points. We claim benchmark-level matches or improvements in the reported means and strong OOD routing performance at lower cost than ALL-STRONG, and we perform much better than other existing routers.

AuthorsOpenReview ↗

Rebuttal Part 2

Weakness 2 / Question 3: Online sensitivity to the threshold and collection budget

For the threshold, the existing data show that the choice of 0.5 is not selecting a narrowly specific training set. Appendix B.4, Table 16 reports 99.61% overlap at D ≥ 0.4, 98.61% at D ≥ 0.6, and 99.81% under an approximately size-matched standard-deviation criterion. For graded-reward WebShop, the corresponding overlaps are 99.34%, 93.99%, and 99.72%. These results directly address the concern that the cutoff is arbitrary for nonbinary outcomes: nearby definitions retain most of the same supervision.

For collection budget, Figure 7 measures how much successful continuation coverage the search provides. At 100 recorded edges per task, the oracle returns are 0.662/0.800/0.380 on SQL/WebShop/SWE-bench; the complete trees yield 0.956/0.960/0.730. The ceiling therefore depends on search coverage. Table 3 evaluates the training-selection benefit using a common collection, so its pivotal-versus-all-state difference does not arise from different collection budgets between those two recipes.

Question 4: Separation of training and evaluation tasks

The available archived runs have zero overlap between source training and evaluation task IDs across all three seeds. The separation is enforced at the root-task level: all descendant states remain in the same partition, preventing a trajectory prefix from entering training while another branch of that task enters evaluation. Appendix A.1, Table 5 gives train/dev/test counts of 202/68/68 for SQL, 120/40/40 for WebShop, and 300/100/100 for SWE-bench. The primary training launcher uses only these source training partitions; ALFWorld, CTF, and τ-bench are excluded from its training input.

Reviewer_n5rVOpenReview ↗

Reply to the author

The authors have satisfactorily clarified the OOD macro/micro discrepancy and the data separation protocol. The threshold-overlap evidence is useful but measures training-set selection rather than online performance sensitivity. The collection-budget analysis reports oracle coverage ceilings but does not quantify online routing sensitivity to budget. The model-pool stability response appropriately scopes the claim but provides no quantitative stability analysis. These remain acknowledged limitations rather than fatal flaws. I maintain my rating of 3.

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

This paper addresses the high inference cost of LLM agents by proposing a multi-turn routing strategy that selects among different models at each step of an agent's trajectory. The core insight is that not all steps are equally critical for model selection; the authors define "pivotal steps" as those states where differences among candidate models lead to significantly different final task outcomes. They use counterfactual rollout trees to identify these steps and thereby guide data collection, router training, and inference. The proposed router is trained only on pivotal states using an "Anchored CE" objective, matching or surpassing strong fixed-model baselines on five of six interactive benchmarks (including InterCode-SQL, WebShop, and SWE-bench) while reducing total inference cost.

Critical strengths

Novel concept of pivotality: This paper moves beyond traditional single-query routing to step-wise routing, introducing a principled method for identifying which steps genuinely benefit from model selection. This sparsity argument—that only a small number of steps are critical—is compelling and empirically validated. Better training strategy: Demonstrating that training on only 32.7% of the data (pivotal states) outperforms training on 100% of the data is a finding that informs the learning paradigm for agent routers.

Critical weaknesses

High data collection cost: In the data collection phase, relying on MCTS rollout trees to identify pivotal steps is computationally expensive. Although the paper argues that this is a one-time offline cost, scaling it to new domains, where agent tasks with long interaction horizons, may be very costly compared with simpler heuristic-based data collection methods. Dependence on the model panel: The definition of pivotality is relative to a specific set of candidate models. If the model pool changes (e.g., a new SOTA model is released), the pivotal labels may become outdated, requiring the tree data to be recollected or re-evaluated. The paper does not adequately address how to adapt to a dynamic model pool without rerunning the expensive MCTS.

Questions for authors

How sensitive is the performance of the router to the threshold used for defining pivotality (D(s)≥0.5)? Would a dynamic threshold based on task difficulty improve generalization? Given the high cost of generating counterfactual trees for training data, how feasible is it to apply this method to entirely new domains where no prior trajectory data exists? In the inference-time modulation (Eq. 9), how was the constant r=0.05 chosen? Is there a principled way to set this hyperparameter across different benchmarks without extensive tuning?

2 comments
AuthorsOpenReview ↗

Rebuttal Part 1

We thank the reviewer for highlighting the usefulness of pivotality and the finding that selective supervision can improve routing while reducing the training set. We address the concerns about collection cost, model-panel adaptation, and generalization below.

Weakness 1: Offline MCTS cost and scalability

MCTS-based supervision is already used in several routing frameworks. DialRouter distills MCTS-generated dialogue decisions into a router; RoVer uses MCTS-based backward sampling for agent routing and verification; and Dr.LLM uses offline MCTS to supervise layer routing. This approach is useful when a model choice must be judged by its downstream consequences. Our use of MCTS follows this established approach, while asking how to obtain and use more informative model comparisons from the search.

We improve the supervision obtained under a specified search budget. In the matched phase-two comparison in Appendix B.3, Table 13, task eligibility and allocated iteration budgets are fixed. Pivotal-aware exploration increases the pivotal-state share from 34.5% to 39.7% on SQL, 20.4% to 24.6% on WebShop, and 23.7% to 24.2% on SWE-bench. Table 3 then shows that retaining 32.7% of the resulting training examples improves online performance over the all-state recipe. These are complementary gains in collection yield and supervision selection; matched iteration budgets do not imply identical API bills.

The collection expense is paid offline and amortized over deployment. Inference uses a 0.6B encoder and lightweight heads, without MCTS. Appendix A.8 reports model-call costs of USD 151.75 versus USD 290.95 for the 473-task suite, saving USD 139.20, or 47.8%. At the same workload mix, this is approximately USD 29,429 in gross savings per 100,000 tasks, before collection, training, and router-serving expenses. For a token-level illustration using Table 6's frozen prices, 2 million input and 0.2 million output tokens cost USD 9.00 on Sonnet versus USD 0.634 on Qwen3-235B. This comparison fixes token volume; the online results establish the achieved task-quality trade-off.

The encoder's reference cost is much smaller in this illustrative workload. The Qwen3-Embedding-0.6B API listing, checked on November 12, 2026, gives USD 0.010 per million tokens: 100,000 tasks with 10 routing decisions and 2,048 encoded tokens per decision would cost USD 20.48 at that rate. This is a base-model API reference, not our fine-tuned router's measured serving bill. The deployment argument is therefore amortization of offline supervision against repeated model-call savings; the precise break-even point depends on collection and serving costs.

Weakness 2: Adapting to a changing model panel

A panel update calls for additional model evidence, but need not require rebuilding every part of the router. A straightforward extension is a shared history encoder with a separate prediction head or lightweight adapter for each candidate. When a model is added, its component can be trained on new evaluations while reusing existing histories and model observations where applicable. IPR, Appendix D provides a precedent for this modular approach with frozen existing components and new adapters and a quality head. New-model outcomes and affected downstream comparisons would still need updating; this is an adaptation path for our fixed-panel method, rather than an experiment already reported.

Our OOD results show that recollection is not required for every change in the deployment distribution. The router trained on SQL, WebShop, and SWE-bench transfers to ALFWorld, CTF, and τ-bench without target-domain router training, reaching 0.618 OOD macro performance versus 0.570 for the best reported prior-router macro score, at 26.4% lower macro cost than ALL-STRONG. This demonstrates reuse across task domains with the same panel. It complements the modular extension for new candidates; it does not test replacement of the candidate models themselves.

The distinction matters because pivotality describes relative model capability at a state, rather than a permanent difficulty label. Updating those comparisons when capabilities change is appropriate. The selection principle can therefore be retained across architectures and panel updates, while the model-specific evidence is refreshed as needed.

AuthorsOpenReview ↗

Rebuttal Part 2

Question 1: Sensitivity to the pivotal threshold

The paper already reports a direct audit of the selected supervision. Section 3.1 refers to Appendix B.4, Table 16. Relative to the reference definition D(s) ≥ 0.5, the row-level Jaccard overlaps are:

Alternative definitionOverallSQLWebShopSWE-bench
D(s) ≥ 0.499.61%99.48%99.34%100.00%
D(s) ≥ 0.698.61%99.46%93.99%100.00%
σQ(s) ≥ 0.2099.81%99.73%99.72%100.00%

The selected examples are therefore largely unchanged around the reported threshold, including under an approximately size-matched standard-deviation criterion. WebShop has the largest change, consistent with its graded terminal rewards. These results measure training-set sensitivity; they do not represent online retraining under every alternative threshold.

Question 2: Difficulty-dependent thresholds

A difficulty-adaptive threshold is a possible extension, but absolute difficulty does not determine the value of model selection. Section 5.3 and Table 4 make this distinction concrete.

In SQL 126, Qwen initially queries the wrong field, but a later action repairs the error, and all five branches preserve a recorded successful continuation. The step is necessary and contains a local mistake, yet it provides no preference over the models under the recorded downstream outcomes. Conversely, in WebShop 157, the product and options have already been selected and the remaining action is a purchase click. Four models complete the purchase; Sonnet checks the features again and has no successful recorded continuation. Thus even the globally stronger model can be worse at a particular state, and a simple action can be pivotal.

These cases support an adaptive criterion based on state-conditioned differences between models, rather than difficulty alone. Their outcomes are explicitly scoped to the collected continuations; they are not claims that an unsuccessful branch could never recover under further exploration.

Question 3: Deployment in domains without collected training trajectories

The three OOD benchmarks directly test this setting. The router is trained on SQL, WebShop, and SWE-bench and deployed on ALFWorld, InterCode CTF, and τ-bench without target-domain router retraining.

Its OOD macro score is 0.618, compared with 0.570 for the highest macro score among the reported prior-router baselines and 0.623 for ALL-STRONG. OOD macro model-call cost is 26.4% lower than ALL-STRONG (Tables 2 and 11). Therefore, collecting new trees is not a prerequisite for the cross-domain deployment demonstrated in the paper. The results support transferring comparative routing behavior across these domains; additional collection remains an option for adaptation to more distant settings.

Question 4: Interpretation and selection of r

The parameter r has a direct interpretation through the effective penalty:

=\frac{r}{r+d(s)}.$$ **When the predicted top-two gap d(s) equals r, the cost penalty is halved.** Larger gaps reduce cost pressure, protecting choices with a clearer predicted performance advantage. The global coefficient λ determines the overall cost preference, while r determines the gap scale at which that preference is relaxed. Figure 3 varies λ at the reference setting r = 0.05. Appendix E.4 and Figure 11 additionally vary r over {0.1, 0.3, 0.5} jointly with λ over {0.2, 0.4, 0.8}. The paper recommends selecting the pair on a validation frontier because their effects interact; it does not identify 0.05 as a universally optimal constant. At λ = 0, r does not affect the routing decision, so the main performance-only comparison is independent of this inference parameter.

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

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