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Under review as a conference paper at ICLR 2027

Conformal Maps for LLM Evaluation: Learning Behavior-Aware Instruction Geometry

Abstract

Aggregate benchmark scores collapse heterogeneous patterns of model success and failure into a single number. A more informative evaluation should characterize this variation at the level of individual instructions, relating a held-out instruction to previously observed model behavior while quantifying uncertainty in that prediction. Conformal prediction provides a natural framework for the latter through finite-sample coverage guarantees, but the informativeness of its prediction sets depends on the score being calibrated. We introduce *conformal maps*, learned instruction embedding spaces whose local support is optimized for informative label-conditional conformal prediction while remaining anchored to a pretrained semantic representation. The same measure of local support organizes historical successes and failures, defines the conformity score, and exposes the evidence surrounding a new instruction. Across five QA and reasoning benchmarks and three target models, the learned maps induce measurable behavioral organization, retain a controllable amount of pretrained structure, and improve conformal singleton rate over the pretrained representation in most dataset–model pairs while maintaining label-conditional coverage. The learned geometry also exposes the amount, direction, and provenance of local behavioral evidence, providing an inspectable account of which prior instructions support a prediction.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Representation Learning, Uncertainty Quantification, LLM Evaluation

Reviews

Among:
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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.25 over 4 reviews, above 96% of the others.
Reviewer_GW9QOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper proposes conformal maps for anticipating whether a fixed target LLM will succeed or fail on a new instruction, using instruction text and historical instruction–outcome pairs. A pretrained instruction encoder is fine-tuned with a neighborhood-support objective and a distance-preservation regularizer. Class-specific kernel support supplies conformity scores for label-conditional split conformal prediction, with model selection separated from final calibration. Across five QA and reasoning benchmarks and three target models, the paper reports improved singleton rates over the pretrained kernel baseline in 14 of 15 settings. Additional experiments examine supervised alternatives, representation transfer, behavioral organization, retained pretrained geometry, and inspectable local evidence.

Critical strengths
  1. The paper provides useful empirical evidence for instruction-level behavioral assessment. The experiments cover five benchmarks and three target models, with improvements over the pretrained kernel baseline in most settings. Comparisons with frozen-embedding probes and end-to-end classifiers, together with the representation–score decomposition and candidate-budget analysis, investigate several plausible explanations for the gains.

  2. The statistical protocol and geometric characterization are thoughtfully organized. Training, validation, calibration, and testing are separated, preserving the applicability of label-conditional split conformal coverage under exchangeability. The regularization study characterizes the trade-off between behavioral separation and preservation of pretrained local ordering. Transfer, pooled-training, and stability analyses provide additional information about the learned representations.

Critical weaknesses
  1. The methodological advance beyond established assessor models, metric learning, and conformal training needs sharper delineation. Predicting LLM correctness from prompt representations is established in prior assessor research, including PredictaBoard by Pacchiardi et al., 2025. The neighborhood log-probability objective closely follows Equation 6 of NCA by Goldberger et al., 2004, while ConfTr by Stutz et al., 2022 already learns underlying models to improve conformal-set efficiency. The manuscript acknowledges these antecedents and includes useful supervised baselines and a regularization sweep. Nevertheless, its contribution currently appears primarily integrative and empirical, and the comparisons do not fully isolate the benefit of neighborhood training from geometry preservation. A classifier equipped with the same distance-preservation penalty and a matched selection budget would help establish this distinction. The geometry-based success prediction of Kashani et al., 2025 also merits discussion when positioning the contribution. These precedents limit the novelty of individual ingredients without establishing that the complete proposed system is redundant.

  2. The connection between the stated method, its theoretical interpretation, and the released implementation remains unresolved. Equation 2 defines py=gy/Sp_y=g_y/S, where S=g0+g1S=g_0+g_1. However, the released scoring code computes p~y=gyS+10−6\widetilde{p}_y=\frac{g_y}{S+10^{-6}}. This introduces a query-dependent scaling that can change class-conditional rankings when support is small, so the logistic-margin identities and Appendix A.7 do not directly describe that implementation. Additionally, the released training loss includes each anchor in its own correct-label support, potentially making the loss small at large bandwidths without useful support from other instructions. The practical effects of these choices have not been quantified, and the authors should confirm whether the released code matches the reported experiments. Independent calibration still supports coverage for a fixed implemented score; the concern is the interpretation and robustness of the reported efficiency gains.

Additional presentation and figure documentation feedback. Figure formatting needs more consistent editorial treatment throughout the manuscript. In Figure 4, the bar-chart labels are substantially smaller than the adjacent tabular text, while Figures 6 and 14 contain dense case descriptions that are difficult to read at normal page scale. Please standardize typography, readable font sizes, color conventions, line and marker styles, legends, panel labels, spacing, and caption formatting across the main paper and appendix. Figure 14 also claims to show the same four anchors as Figure 6, but their R4 examples differ. The examples or captions should be corrected. The AI Use Statement already acknowledges generative AI assistance in creating or modifying figures and tables. Please identify the affected items, the tools used, and whether AI assisted with layout, plotting code, or direct image generation. The authors should also explain how they checked the scientific content and numerical fidelity, and make empirical plots reproducible from the underlying experimental data and plotting scripts.

Questions for authors
  1. What methodological contribution should be attributed specifically to the proposed formulation beyond NCA-style representation learning followed by label-conditional calibration? Could a focused comparison give the end-to-end classifier the same geometry-preservation penalty and a matched selection budget, while reporting both singleton rate and retained geometry?

  2. Does the released scoring implementation match the reported experiments? Please quantify how often SS is comparable to or below 10−610^{-6}, and whether numerically stable exact normalization changes score rankings, prediction sets, or the main singleton-rate comparisons.

  3. Is including each training anchor in its own support intentional? Please quantify the self-support contribution across sampled bandwidths and provide a diagonal-masked ablation on representative settings under the same evaluation protocol.

  4. Appendix B.5 distinguishes the ESS-matched diagnostic bandwidth from the actual prediction bandwidth. Do the evidence regimes and supporting instructions remain similar under the prediction bandwidth, and what fraction of the conformity score is accounted for by the displayed neighbors?

  5. Which figures and tables were created or modified with generative AI, and what role did the tools play? Please clarify how numerical plots and illustrative diagrams were produced and verified, including the correspondence between plotted values and experimental outputs.

4 comments
AuthorsOpenReview ↗

Our response – part 1

We appreciate the reviewer’s careful and technically detailed assessment, as well as the positive comments on the empirical evaluation and statistical protocol. The review identified several concrete points that led us to add new controls and clarify both the contribution and the implementation:

  • W1/Q1 (Methodological contribution): We sharpen the distinction from assessor models, NCA, and conformal training; add the geometry-based predictor of Kashani et al. to the related work; and introduce a geometry-regularized end-to-end classifier control that directly separates the effects of neighborhood training, the conformity score, and geometry preservation.
  • W2/Q2/Q3 (Implementation details): We verify that the released scoring implementation matches the code. In addition we rerun our pipeline under exact log-space normalization and diagonal-masked training ablations. The headline singleton-rate results are unchanged and the reported gains do not rely on these two implementation details.
  • Q4 (Evidence at the prediction bandwidth): We repeat the evidence analysis using the bandwidth selected for prediction, quantifying agreement in evidence direction and support/margin rankings.
  • W3/Q5 (Figures, AI use, and reproducibility): We correct the Figure 6/14 example mismatch and clarify that AI tools were used only to construct scripts generating figures from experimental sources. All reported numbers match the experimental results.

In the subsequent parts, we address each point in detail.

AuthorsOpenReview ↗

Our response – part 2

W1. & Q1. Novelty and new comparisons

We agree with the reviewer's own conclusion: the precedents "limit the novelty of individual ingredients without establishing that the complete proposed system is redundant". We do not claim novelty for the ingredients (see also our response to W1 of Reviewer 1). The contribution is the formulation and study of a model-specific geometry of instruction space as an evaluation object: historical successes and failures become local structure that simultaneously determines conformal predictions and exposes the evidence supporting them.

  • Assessors (Pacchiardi et al., 2025). An assessor outputs a scalar estimate of correctness. Our system outputs a prediction set with finite-sample label-conditional coverage, computed from a geometry that also exposes how much historical evidence surrounds the instruction, which outcome it favors and which evaluated instructions contribute.
  • NCA (Goldberger et al., 2004). The training objective is the same, but what is new is its role: the local support score defines the conformity score, and Appendix A.7 shows when improving it reduces ambiguity after the conformal thresholds are recalibrated, which does not follow from better discrimination alone.
  • ConfTr (Stutz et al., 2022) trains a classifier through a differentiable calibration step and leaves no geometry to inspect. We now compare with it directly (new Appendix C.16): across the 15 benchmark–model pairs, our map has a higher singleton rate by +0.067 (95% CI [+0.057, +0.077]), and it is significantly higher in 11 of the 15 pairs and lower in 2.
  • Kashani et al. (2025). Thank you for the pointer. They keep the pretrained prompt embedding fixed and represent each LLM, in closed form, as one vector; success is predicted by a linear projection onto it, without coverage guarantees. We instead adapt the geometry to one target model, read evidence from neighborhoods and calibrate it into prediction sets. Our closest baseline in form is raw + logistic, a linear readout on the frozen embedding (0.365 against 0.451 for the map, Fig. 4). We will add this discussion to the related work.

Isolating neighborhood training from geometry preservation

We ran the control the reviewer proposes. Our method has three components: the neighborhood loss, the distance-preservation penalty and the kernel conformity score. The control gives the classifier the penalty, and the kernel score, matching the selection budget. These additions move the classifier toward our method one component at a time.

The classifier is trained with cross-entropy plus the same penalty, applied to its embedding, over the same grid λ∈{0,0.1,1,10}\lambda \in \{0, 0.1, 1, 10\} and checkpoints as the map, with the same cross-validated selection. For the matched comparison, both encoders are scored with the kernel score and selected over the same candidates, so the two rows differ only in the loss. Cells give the singleton rate at α=0.1\alpha = 0.1 for Qwen3, averaged over five benchmarks.

no penalty (99 candidates)with penalty, (λ\lambda selected, 396 candidates)
Classifier encoder (cross-entropy)0.3830.437
Conformal map (neighborhood loss, ours)0.4390.451
Map minus classifier, singleton rate+0.056 [+0.041, +0.071]+0.014 [+0.0002, +0.028]

With its own probability score, the end-to-end classifier goes from 0.374 to 0.419 with the penalty;the map is +0.032 [+0.017, +0.046] above it.

  • Our components transfer to the classifier. The penalty and the kernel score raise the classifier from 0.374 to 0.437 and its retained geometry from CLRP50\mathrm{CLRP}_{50} 0.13 to 0.43. We agree with the reviewer that a large part of the gap in Fig. 4 is due to these two components. A classifier that adopts them is no longer an independent baseline: it is our pipeline with a different loss.
  • The neighborhood loss improves on cross-entropy in both settings, by +0.056 without the penalty and by +0.014 with it. The loss and the penalty act in the same direction, so whichever is added second adds less: this is also why the penalty gives the map a smaller gain than it gives the classifier. With the penalty in place the advantage of the loss is small, and we do not claim otherwise.
  • The bandwidth is part of the method, not extra budget. Against the classifier's probability score the map also selects the bandwidth η\eta of its kernel score. This is one scalar of the conformity score, selected on validation data without retraining, and a probability score has no counterpart to tune. The matched comparison removes the difference altogether.

What we attribute to the proposed formulation is therefore the combination: a conformity score read from neighbourhoods, a loss that trains the quantity this score uses, and a penalty that keeps the pretrained geometry. No single ingredient accounts for the gain on its own.

AuthorsOpenReview ↗

Our response – part 3

W2. & Q2. & Q3. Method, theory and released implementation

The released code is the code that produced the reported experiments. We thank the reviewer for the careful reading of the code. Removing the constant from the scoring code leaves the results of the learned map unchanged, and masking the anchor's own term in training does not change them significantly; we quantify both below.

The constant in the scoring code (Q2)

All reported results use py=gy/(S+10−6)p_y = g_y/(S + 10^{-6}), where the constant was meant as a division-by-zero safeguard. Removing the constant does not change the results of the learned map (singleton rate 0.408 with and without it, over the 15 benchmark–model pairs and three seeds of Table 1). We established this by re-running selection, calibration and evaluation with the exact normalization of Equation 2, computed in log space.

How often is SS comparable to or below 10−610^{-6}? Never for η≤10\eta \leq 10 (smallest SS observed: 0.22). At the two largest bandwidths of the grid it is more frequent: over all candidate configurations, S≤10−6S \leq 10^{-6} for 21% of queries at η=50\eta = 50 and 31% at η=100\eta = 100 (S≤10−4S \leq 10^{-4} for 28% and 33%). Among the selected kernel configurations, 39 of 135 use η≥50\eta \geq 50.

Does exact normalization change rankings and prediction sets? For the 96 selected configurations with η≤10\eta \leq 10, nothing changes: scores differ by at most 2×10−62 \times 10^{-6}, rankings are identical and no prediction set changes. For the 39 with η≥50\eta \geq 50, prediction sets change for less than 8% of test queries on average. Over all selected configurations, the singleton rate of the learned map is unchanged (Table 1 results stay at 0.408). The map remains the method with the highest singleton rate in 14 of 15 pairs and the overall gain remains significant. Coverage is unchanged (0.90 on average for both classes).

The anchor in its own support (Q3)

The inclusion of the self-term was not a deliberate choice. The loss sums exp⁡(−ηdij)\exp(-\eta d_{ij}) over the whole minibatch without masking j=ij = i, so each anchor adds exp⁡(0)=1\exp(0) = 1 to the support of its own class. Inclusion of the anchor affects the training loss only. At selection, calibration and inference, the queries are held-out questions and are not in the reference bank, so no self-term enters any reported score.

Self-support contribution across bandwidths. For minibatches of the training size (70) drawn from the MMLU training set (Qwen3), we measured the share of an anchor's own-class support that is the anchor itself, 1/g(xi,yi)1/g(x_i, y_i):

η\eta0.10.3131030100sampled η∼log⁡U[0.1,100)\eta \sim \log U[0.1, 100)
Pretrained encoder (initialization)0.030.040.060.260.991.001.000.49
Trained map, λ=1\lambda = 10.030.040.050.170.931.001.000.45
Trained map, λ=0\lambda = 00.030.030.030.030.030.040.060.03

At small bandwidths the anchor is one of about 35 same-outcome items and contributes about 3%. At η≥10\eta \geq 10 under the pretrained geometry, the anchor is essentially its whole own-class support, so its loss term is close to zero and those bandwidths contribute little gradient.

Diagonal-masked ablation. We retrained the map with the diagonal masked, changing nothing else, and evaluated it under the same protocol (same splits, 99 candidates, cross-validated selection, calibration and test; MMLU, Qwen3):

With self-term (paper)Diagonal maskedDifference (95% paired bootstrap interval)
λ=0\lambda = 00.4560.488+0.032 [−0.003, +0.068]
λ=1\lambda = 10.4100.453+0.043 [0.000, +0.085]

Neither difference is significant, and if anything, it slightly improves our own method. Both variants are well above the pretrained encoder (0.337).

AuthorsOpenReview ↗

Our response – part 4

W3. and Q5. Presentation and figure documentation

Figure 14. We thank the reviewer for the careful reading. The two figures are rendered separately, and their R4 examples went out of sync while the paper was being revised. We have regenerated Figure 14 so that it shows the same four anchors as Figure 6.

Consistency. All figures are produced by plotting scripts from the stored experimental results, and they share one visual system: a single typeface (DejaVu Sans) in every figure of the main paper and appendix, and one palette (two hues, blue and orange, with neutral grays) used throughout. We agree that the text in some figures is too small at page scale, in particular the bar-chart labels of Figure 4 and the case descriptions of Figures 6 and 14. We will enlarged these to a common minimum size in the camera-ready version providing us with more space for figures.

AI assistance and reproducibility (Q5). AI coding assistance was used for the plotting and table-generation code behind all figures and tables, and in every case its role was limited to writing and editing that code. No figure or table contains generated imagery, and no reported value was produced or edited by an AI tool.

  • Numerical plots and tables. Each is produced by a script in the released repository that reads the stored experimental outputs and writes the figure, or the LaTeX table, directly. Plotted and tabulated values are therefore the experimental outputs themselves, with no manual transcription, and the numbers quoted in the text are read from the same files.
  • Illustrative diagrams. Figure 1 is a schematic, also drawn by a script; it illustrates the construction and reports no measurements. The example cards of Figures 6 and 14 show actual test instructions and their nearest training instructions, retrieved from the stored embeddings.
  • Verification. We reviewed every figure and table against the result files it is generated from, and the evaluation scripts check the data splits of every run against a reference before scoring it.

We have expanded the AI Use Statement accordingly.

Q4. Evidence under the prediction bandwidth

We computed both quantities on all 15 benchmark–model pairs and three seeds (45 cases), comparing the diagnostic bandwidth with the prediction bandwidth selected as in the main results.

Do the supporting instructions remain similar? Yes, they are identical. Neighbors are ordered by distance in the learned map, and this order does not depend on the bandwidth, so the same instructions are displayed under both. At the diagnostic bandwidth, the 3 displayed neighbors account for 19% of the score. The prediction bandwidth, is selected for conformal efficiency and typically aggregates evidence over a much broader portion of the reference bank. At this bandwidth, the three displayed neighbors account for only about 1% of the support. A prediction that pools evidence from many historical instructions cannot be summarized faithfully by only three examples. This broader aggregation also makes the prediction less dependent on any single retrieved example. The displayed neighbors should be interpreted as the nearest concrete exemplars of the learned geometry, rather than as a sparse decomposition of the prediction score. We will adjust our provenance claims accordingly.

Do the evidence regimes remain similar? The regimes are descriptive labels for regions of the evidence plane at the diagnostic bandwidth; they are not used by the prediction, and no reported result depends on them. The quantities they summarize do carry over to the prediction bandwidth: the direction of the evidence (which side of the base rate it favors) agrees between the two bandwidths for 93% of queries, and query rankings by margin and by total support have Spearman correlations of 0.85 and 0.75 (medians over the 45 cases).

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

This manuscript introduces Conformal Maps, a framework for predicting a target LLM's behavior on unseen instructions based on its historical successes and failures, with statistical coverage guarantees. The method fine-tunes a pre-trained instruction encoder using a kernel-weighted neighborhood objective and distance-preserving regularization to learn behavior-aware representations while preserving semantic structure. These representations are then used for label-conditional conformal prediction and the retrieval of supporting historical evidence. Experiments across multiple benchmarks and LLMs demonstrate improvements over the baseline, alongside additional analyses. Overall, the manuscript addresses a practically relevant problem and presents a well-developed framework. However, the novelty of the approach relative to existing metric learning and conformal prediction methods remains unclear, and the experimental evidence does not fully substantiate its central claims.

Critical strengths

This manuscript explores a problem of practical significance: predicting whether a target large language model will succeed or fail on unseen instructions, based on historical behavioral records and without requiring additional model queries. Furthermore, by incorporating "label-conditional conformal prediction," the proposed method provides formal statistical coverage guarantees.

Critical weaknesses
  1. Insufficient comparisons with established metric-learning methods. The proposed objective closely resembles Neighborhood Components Analysis (NCA), while distance-preserving regularization and conformal calibration are established techniques. Although Appendix A.7 provides theoretical insights into calibrated ambiguity, it does not establish that optimizing the proposed objective necessarily improves singleton rates. Despite comparisons with supervised classifiers, the lack of direct comparisons with supervised contrastive or triplet-based metric learning makes it difficult to assess the objective's advantages over existing representation learning methods.

  2. Insufficient evidence for the interpretability of learned behavioral geometry. The analyses in Section 5.3 and Table 2 demonstrate improved neighborhood coherence but do not establish whether the retrieved examples offer more meaningful explanations of model behavior than alternative supervised representations. Moreover, random within-benchmark splits may contain semantically similar or near-duplicate instructions, making it difficult to determine whether the observed neighborhood structure reflects generalizable behavioral patterns rather than semantic similarity.

Questions for authors
  1. Comparison with existing metric learning methods Given the close connection between the proposed training objective and Neighborhood Components Analysis (NCA), direct comparisons with supervised contrastive learning or triplet-based metric learning are necessary to establish its advantages over existing methods.

  2. Interpretability of the learned behavioral geometry The paper emphasizes retrieving historical instructions as supporting evidence for model behavior predictions. However, nearest-neighbor retrieval can also be performed using supervised classifier representations. The authors should provide direct empirical comparisons to demonstrate that the retrieved examples offer more meaningful behavioral insights than those obtained from supervised baselines.

  3. Data efficiency and dependence on historical behavioral records The proposed method relies on substantial historical success/failure data, with reference banks containing approximately 8,000–27,000 instructions. How does performance change as the training set or reference bank size decreases? In particular, does the method maintain its advantage in singleton rate over supervised baselines under limited-data settings?

8 comments
AuthorsOpenReview ↗

Our response – part 1

We appreciate the reviewer’s recognition of the practical importance of predicting LLM behavior from historical evaluations and of the value of label-conditional coverage guarantees. In response to the concerns raised, we have added several new analyses:

  • W1/Q1 (Metric learning): We add direct comparisons with supervised contrastive and triplet-based metric learning, and clarify the scope and interpretation of Appendix A.7.
  • W2/Q2 (Inspectability): We directly compare the behavioral information exposed by our neighborhoods with those of the supervised classifier representation, including an identical kernel readout, and clarify that our claim concerns inspectability of prediction evidence, not human interpretability.
  • W2 (Near-duplicates): We add a near-duplicate/paraphrase audit, de-duplicated evaluation, and semantic-distance-stratified analysis (new Appendix C.17).
  • Q3 (Data efficiency): We add ablations over reference-bank size, representation-training data, and calibration-set size across all 15 benchmark–model pairs (new Appendix C.15).

In the remaining parts, we address each point in detail.

AuthorsOpenReview ↗

Our response – part 2

W1. & Q1. Comparison with metric-learning

We agree with the reviewer on the first point: the objective is closely related to NCA, and distance-preserving regularization and conformal calibration are established techniques. We do not claim novelty for these components in isolation (see also our response to W1 of Reviewer 1). Your comment raises two further points, which we address in turn: the additional comparison with supervised contrastive and triplet-based metric learning, and the interpretation of Appendix A.7.

Our method vs. other metric-learning methods. We ran the requested comparison. Starting from the same pretrained encoder, we fine-tuned it with the supervised contrastive loss (SupCon; Khosla et al., 2020) and with a batch-all triplet loss on cosine distance (Schroff et al., 2015; Hermans et al., 2017), and evaluated the resulting representations exactly as ours. To match selection budgets, each objective is run at a fixed temperature or margin and compared with our objective without the distance-preservation penalty (=0), so that only the training objective differs. Results are for Qwen3 over the five benchmarks at =0.1.

Training objectiveSingleton rateOurs (=0) minus objective [95% bootstrap interval]
Pretrained encoder (no training)0.386
SupCon, =0.10.426+0.013 [−0.004, +0.029]
SupCon, =0.050.425+0.014 [−0.002, +0.030]
Triplet, margin 0.20.442−0.003 [−0.018, +0.012]
Triplet, margin 0.50.445−0.007 [−0.022, +0.008]
Ours, =00.439

All three objective families substantially improve over the pretrained representation, and we find no statistically significant difference between either SupCon or triplet training and our objective without distance preservation. This absence of a significant gap is consistent with the close relationship between the three objectives, a systematic difference in downstream conformal efficiency is not something we would expect. The three losses are different smooth surrogates for closely related positive-vs.-negative neighborhood orderings.

For an anchor xx with outcome yy, define its soft-minimum distance to the same-outcome examples (++) and to the different-outcome examples (−-) as

dη±(x)=−1ηlog⁡∑i∈I±exp⁡[−η d(x,xi)],d_{\eta}^{\pm}(x) = -\frac{1}{\eta} \log \sum_{i \in \mathcal{I}^{\pm}} \exp\left[-\eta\, d(x,x_i)\right],

where

I+=i:yi=y,I−=i:yi≠y.\mathcal{I}^{+} = \\{i : y_i = y\\}, \mathcal{I}^{-} = \\{i : y_i \neq y\\}.

Our neighborhood loss can then be written as

\left( \eta \left[ d_{\eta}^{+}(x)-d_{\eta}^{-}(x) \right] \right).$$ Thus, the objective applies a smooth positive-vs.-negative ranking loss to aggregate soft-minimum distances. Triplet loss imposes the closely related pairwise condition $$\left[ s_{in}-s_{ip}+m \right]_{+},$$ penalizing cases where a negative example is not sufficiently farther from the anchor than a positive example. Under a common temperature, the relationship with SupCon is similarly direct. For a common temperature and candidate set, let (q_{ij}) denote the softmax probability assigned by anchor (i) to example (j). The NCA-style form underlying our loss is $$-\log \sum_{p\in P(i)} q_{ip},$$ whereas standard SupCon uses $$-\frac{1}{|P(i)|} \sum_{p\in P(i)} \log q_{ip}.$$ By Jensen's inequality, \$ L_i^{\mathrm{SupCon}} \ge L_i^{\mathrm{NCA}} + \log |P(i)|\$. Both objectives therefore move softmax probability mass from different-outcome to same-outcome examples, while SupCon additionally encourages that mass to be distributed across individual positives. The objectives are not identical, but they impose closely related behavioral ordering pressures. We therefore do not claim that our objective is a better metric-learning loss than SupCon or triplet loss. Instead, this comparison shows that the gain from adapting instruction geometry to target-model behavior is not specific to one particular neighborhood surrogate: all three objectives produce statistically indistinguishable conformal efficiency in this experiment. **The analysis of Appendix A.7 further explains why similar performance is plausible.** After label-conditional recalibration, ambiguity is determined by the class-conditional ranking induced by the learned margin: at a given , it depends on two operating points of its ROC curve. Consequently, differences that change the scale of a score while preserving its ranking do not affect calibrated ambiguity. SupCon, triplet loss, and our objective are different surrogates that impose closely related positive-vs.-negative ordering pressures, and empirically they produce similar held-out rankings: test AUC is 0.723 for our objective, 0.712 and 0.706 for triplet loss, and 0.701 and 0.699 for SupCon. These ranking differences are modest, consistent with the absence of a significant difference in singleton rate after recalibration.
AuthorsOpenReview ↗

Our response – part 3

W1. Interpretation of Appendix A.7

The reviewer is right, and we will state this more carefully. Appendix A.7 does not show that optimizing the objective necessarily improves singleton rate. What it establishes is the following.

  • A characterization. After label-conditional recalibration, the probability of an ambiguous (two-label) prediction set is determined by the class-conditional ranking induced by the learned margin, even though the calibration thresholds themselves change with the representation.
  • A sufficient condition. If one representation dominates another in ROC terms, it yields lower ambiguity for every

, including in expectation under finite-sample calibration.

  • A link to the objective. The population minimizer of the logistic objective ranks by the likelihood ratio, which is the ranking that is optimal for this ambiguity criterion.

The analysis therefore explains why the objective is an appropriate surrogate; it does not guarantee that minimizing it on finite data produces a representation that dominates the pretrained one. Whether it does is an empirical question, which we answer experimentally.

W2. & Q2. Inspectability of the learned behavioural geometry

We interpret W2 and Q2 as raising the same central question: how should one determine whether retrieved historical examples provide more meaningful behavioral evidence than nearest neighbors from another supervised representation?

There is no standard representation-independent scalar metric of explanatory meaningfulness: if the intended claim is that inspecting examples improves human understanding or downstream decisions, this would require a specified user task and a human evaluation, which we do not provide. We will therefore narrow our terminology from general interpretability to inspectability of the evidence used by the prediction.

For this claim, we evaluate three measurable properties and compare directly against the supervised classifier representation.

  1. Faithfulness to the prediction. In the conformal map, reference-bank examples are not a post-hoc visualization: their kernel contributions constitute the class-specific supports from which the conformity score is computed. The amount of evidence, its direction, and the highest-contributing historical instructions are therefore properties of the actual prediction mechanism. In the supervised classifier, prediction is produced by the classification head; nearest neighbors in its hidden representation can be inspected, but the prediction itself does not depend on which examples are retrieved.

  2. Behavioral informativeness of the retrieved neighborhood. We quantify whether the retrieved examples contain information about held-out model behavior. The success fraction of a query's neighborhood ranks held-out outcomes with AUC 0.686 for the learned map, compared with 0.665 for the classifier representation and 0.645 for the pretrained encoder (Table 2; five benchmarks, three seeds). Behavioral coherence is also higher for the map: the share of queries in homogeneous neighborhoods is 53%53\%, compared with 35%35\% for the classifier representation and 4%4\% for the pretrained encoder.

  3. Usefulness under an identical readout. To isolate representation quality from the prediction head, Appendix C.8 applies the same kernel conformity score to both learned representations. The classifier representation obtains a singleton rate of 0.376, compared with 0.421 for the map. Thus the difference is present even when both representations are queried through exactly the same neighborhood-based mechanism.

The higher-level evidence is also reproducible across retraining: cross-seed Spearman correlations are 0.84 for margin and 0.75 for total support, remaining 0.61 and 0.51 after removing agreement attributable to the pretrained geometry (Appendix C.14).

These measurements are the criteria we currently use for “behaviorally informative” retrieval: the evidence directly enters the prediction computation, its composition is more predictive of held-out behavior, and the representation supports a stronger identical neighborhood readout than the supervised classifier representation. We do not claim that these results establish that humans will necessarily find the retrieved examples more useful or understandable.

If the reviewer has a different quantitative notion of “meaningful behavioral insight” in mind we would be happy to evaluate it. Our concern is to avoid substituting an arbitrary proxy for a human-interpretability claim that has not been operationally defined.

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

This paper explores an algorithm that fine-tunes an encoder model to predict whether a target LLM will succeed or fail on a new instruction, based on a bank of previously evaluated instructions. On top of the training, authors use the same kernel-weighted neighbor support (how much success vs. failure evidence surrounds the query) as the conformity score for label-conditional conformal prediction, which gives per-class coverage guarantees, and they use singleton rate as the measure of efficiency. A regularizer keeps the learned geometry close to the pretrained embedding, trading off behavioral separation against semantic structure. The authors further argue that the learned neighborhoods make the prediction inspectable: how much evidence there is, which outcome it favors, and which past instructions contribute. Across five QA benchmarks and three target models, the learned map improves singleton rate over the pretrained encoder in most settings while maintaining coverage, and is competitive with or better than supervised probes and an end-to-end classifier.

Critical strengths
  • The conformal protocol is careful and clean. Selection, calibration and test are kept separate, and label-conditional coverage is verified per class.
  • Using the same local support as training loss, conformity score and explanation is a simple and coherent design.
Critical weaknesses
  • The novelty over prior work is unclear. Pekala et al. (2012) and Stutz et al. (2022) also learn representations or scores for more efficient conformal prediction, but are only cited as motivation. A learned metric on the frozen encoder and a comparison with conformal training are missing.
  • The gains over simple baselines are marginal. At a matched search budget the map is only slightly ahead of raw + MLP (0.415 vs. 0.408), and Table 1 and Fig. 9 disagree on some settings (e.g. Gemma/MMLU).
  • The map may be learning benchmark-specific shortcuts (spurious correlations). Splits are random, Fig. 14 shows near-duplicate questions in train and test, and the transfer results in Appendix C.4 are mixed. The discussion and experiment over this concern is limited.
  • There is no truly out-of-distribution evaluation. Even the transfer experiments use a bank and calibration data from the target benchmark, and all benchmarks are short-answer QA.
  • The interpretability claim is not validated. Neighbors change a lot across seeds, and the usefulness of the exposed evidence is not well tested.
Questions for authors

See the weaknesses

4 comments
AuthorsOpenReview ↗

Our response – part 1

We appreciate the reviewer’s careful assessment and the positive comments on the conformal protocol and the coherence of using the same local support for training, prediction, and evidence. In response, we have added several new analyses and clarifications:

  • W1 (Novelty and prior work): We add direct comparisons with a learned LMNN metric using the distance-ratio score of Pekala et al. and with conformal training following Stutz et al. (new Appendix C.16), and clarify the level at which we claim methodological novelty.
  • W2 (Baseline comparisons): We clarify the search-budget comparison in Appendix C.6. We also explain the seed differences between Table 1 and Figure 9.
  • W3 (Spurious correlations and near-duplicates): We add a near-duplicate/paraphrase audit, repeat evaluation after de-duplication, and stratify gains by pretrained distance to the reference bank (new Appendix C.17).
  • W4 (OOD evaluation): We clarify the exchangeability assumption and the need for target-distribution calibration. We also discuss the cross-benchmark results (Appendix C.4) and add labeled-data ablations (new Appendix C.15) to quantify adaptation requirements.
  • W5 (Interpretability): We clarify that our claim concerns the inspectability of prediction evidence, not demonstrated improvements in human decision-making. We also highlight the behavioral informativeness of the neighborhoods (Section 5.3) and the stability of evidence amount and direction across seeds (Appendix C.14).

Below, we address each concern in detail.

W1. Comparison with a learned metric and conformal training

The reviewer is right that Pekala et al. (2012) and Stutz et al. (2022) were cited only as motivation. We have now run both requested comparisons (see new Appendix C.16 for details):

  • A learned metric on the frozen encoder (Pekala et al.). We train their LMNN linear metric on the pretrained encoder's embeddings and evaluate it with their distance-ratio score. Its strongest variant reaches a singleton rate of 0.365, against 0.405 for our map: a difference of +0.040 (95% bootstrap interval [+0.031, +0.049]).
  • Conformal training (Stutz et al.). Following their experiments on pretrained features, we train a head on the pretrained encoder with their size and coverage losses. It reaches 0.338, against 0.405 for our map: a difference of +0.067 (95% bootstrap interval [+0.057, +0.077]). In our setting ConfTr does not improve on the same head trained with cross-entropy (0.363). This is consistent with their own findings: on their binary datasets they report that ConfTr "is not able to improve inefficiency significantly", and they observe smaller gains when training on pretrained features.

W2. Gains vs. serch budget

Clarification. The singleton rate of 0.415 is the performance of our map restricted to only 8 candidates. However, raw + MLP uses 30 candidates. The comparison made by the reviewer therefore give the map roughly a quarter of the MLP's budget, and the map is still ahead. The same appendix actually reports singleton rates of 0.423 at 24 candidates and 0.431 at 48 candidates for the map, both sitting well above the performance of raw + MLP (0.408). Under each pipeline's full protocol, which is the comparison in Fig. 4 and the main text, the map reaches 0.451 against 0.408 for raw + MLP: a paired difference of +0.043 with a 95% bootstrap interval of [+0.027, +0.059], which is significant.

Table 1 and Fig. 9 do not disagree; they differ in the number of training seeds. Table 1 reports the average over three training seeds and Fig. 9 reports a single seed, like Fig. 4 whose comparison it repeats for the other target models, we will clarify this in the captions. For Gemma/MMLU, Table 1 gives 0.37 for the map against 0.36 for the pretrained encoder, a difference of +0.002. Fig. 9 gives 0.29 against 0.30 for the first seed, which is one of the three runs entering that average (0.29, 0.37 and 0.43 for the map).

AuthorsOpenReview ↗

Our response – part 2

W3. Spurious correlations and the impact of near-duplicates

Dataset-specific structure is the object of study, and it is evaluated out of sample. Our setting is the evaluation of a fixed LLM on new instructions drawn from the same distribution as previously evaluated ones. Regularities in where that model succeeds or fails within a benchmark are therefore part of the signal we aim to learn, not automatically shortcuts. The relevant concern is whether the gains are driven by brittle benchmark artifacts rather than stable behavioral structure. All reported results are measured on held-out test instructions, with representation learning, model selection, calibration, and testing performed on disjoint splits. Thus, any benchmark-specific structure that improves our test results must at least persist to unseen questions from that distribution. Conformal calibration does not prevent shortcut learning, but it does separate validity from informativeness: a poor representation can reduce singleton efficiency, while label-conditional coverage is still controlled after calibration.

Part of the learned structure also carries across benchmarks. Appendix C.4 tests a stronger form of generalization by applying a map trained on one benchmark to another. Across the 20 ordered transfer pairs, 18 show no significant decrease relative to the pretrained encoder and 9 show a significant improvement. The only two significant losses occur on CQA, where the map trained on CQA itself also provides no significant gain. Transfer is uneven, but the results argue against the gains being explained purely by benchmark-specific training artifacts. A complementary pooled-training experiment shows that a single map trained on all five benchmarks raises singleton rate on their union from 0.408 to 0.480 (Appendix C.4). We do not claim transfers to arbitrary distributions. Our primary claims concern same-distribution evaluation, where benchmark-specific behavioral structure is precisely what the method is intended to characterize; the cross-benchmark results show that part of this structure is nevertheless shared across datasets.

Near-duplicate questions. Near-identical questions come from the benchmarks themselves. In MMLU, many items share a template and differ only in a value, an entity or the answer options; a random split places such siblings on both sides, and a nearest-neighbour display such as Figure 14 elicit them, although only 9.1% of held-out MMLU questions have a near-duplicate in the reference bank. We audited every held-out question against the reference bank for all five benchmarks (see new Appendix C.17). Below we summarise the key findings.

  • Near-duplicates are the most favourable case for the baseline, not for our method. A near-copy sits at almost zero distance in the pretrained embedding, so the baseline can retrieve it without any learning. On test questions with a near-duplicate in the bank, the pretrained embedding reaches a singleton rate of 0.676 and the learned map cannot improve much on it (0.681, difference +0.005, 95% bootstrap interval [−0.003, +0.014]). Near-duplicates are therefore where our method is hardest to distinguish from the baseline.
  • The gains hold after removing near-duplicates. We removed every near-duplicate from the validation, calibration and test sets and repeated selection, calibration and evaluation. Across the five benchmarks the map improves on the pretrained embedding by 12.8% relative, against 13.9% originally, and coverage remains at the nominal level. On MMLU, the benchmark shown in Figure 14, the gain rises from +0.069 to +0.085.
  • The advantage grows as semantic neighbours become less informative. Splitting the remaining test questions into thirds by pretrained distance to the bank, the gain of the map vs. raw embedding is absent for the nearest third (−0.004), +0.026 for the middle third, and +0.078 for the furthest third. These are the questions for which semantic similarity offers the least, and they are where the learned geometry helps most. A map relying on near-copies would show the opposite pattern.
AuthorsOpenReview ↗

Our response – part 3

W4. OOD Evaluation

We agree, and the paper's claims are limited to the exchangeable setting. The coverage guarantee of split conformal prediction requires calibration data exchangeable with the test data. This holds for any conformity score, including the pretrained embedding, logistic regression and the MLP baselines; it is a property of the conformal framework and not of our map specifically. We therefore do not claim finite-sample coverage under arbitrary distribution shift without target-distribution recalibration; we state this openly as a limitation.

Within this setting, two practical questions remain: how much of the method must be adapted to a new distribution, and how much labeled target data is required.

  • The representation does not need to come from the target benchmark. In Appendix C.4, a map trained on a different benchmark significantly improves on the pretrained encoder in 9 of 20 source–target pairs and shows no significant decrease in 18. Coverage on the target is at the nominal level in all 20 (worst-class coverage 0.874–0.913 at a 0.90 target).
  • One map serves a heterogeneous mixture. A single map trained on all five benchmarks raises the singleton rate on their union from 0.408 to 0.480, without knowing which benchmark a test instruction comes from.
  • Little target data is needed. In the new Appendix C.15, with only 50 calibration examples the map already improves on the pretrained encoder by 0.041 (95% interval [0.036, 0.047]), and restricting the reference bank to 30% of its size gives a singleton rate of 0.396 against 0.410 with the full bank.

W5. Interpretability

For each prediction the map exposes three things: the amount of local evidence (total support), its direction (which outcome the neighbourhood favours), and its provenance (which previously evaluated instructions contribute). This is not a post-hoc explanation: the conformity score is computed directly from kernel contributions over the reference bank, so these quantities are components of the prediction itself. We do not claim that inspecting them necessarily improves human decision-making.

What is validated?

  • Direction is predictive of held-out outcomes. The success fraction of a query's neighborhood ranks held-out outcomes with AUC 0.686 under the learned map, compared with 0.645 for the pretrained encoder and 0.665 for the classifier representation (Table 2; five benchmarks, three seeds). The share of queries in behaviorally homogeneous neighborhoods also rises from 4%4\% to 53%53\%.
  • Amount and direction are reproducible across retraining. Across independently trained maps, query rankings by margin and total support have Spearman correlations 0.84 and 0.75. After removing agreement explained by the pretrained geometry, the corresponding correlations remain 0.61 and 0.51 (Appendix C.14).
  • The exposed evidence is functionally tied to the prediction. The conformity score is obtained from the same class-specific local supports g(x,0) and g(x,1) used to define evidence amount and direction. Thus these quantities describe the actual score being calibrated, not an auxiliary explanation fitted after prediction.

The reviewer is right that the identity of individual neighbours is the least stable property: the K=50 neighborhoods have a mean cross-seed Jaccard overlap of 0.48. We report this in Appendix C.14 and for that reason base our interpretation on support, direction and regime, treating individual neighbours as a lower-level diagnostic. This clarifies what provenance means. For the map that is deployed and calibrated, the listed neighbours are direct contributors to the score behind that prediction. They are not the unique set of instructions that explains the LLM's behaviour: a retrained map can support the same conclusion with different instructions.

Figure 6 illustrates what this information can reveal: neighborhoods dominated by successes, neighborhoods dominated by failures, conflicting evidence, and exceptions where the actual outcome contradicts the local evidence. The practical usefulness of inspecting these examples depends on the application and the practitioner's objectives, making it difficult to define a single quantitative measure of usefulness. We therefore do not claim that exposing this information necessarily improves human decision-making. Rather, our contribution is to make the evidence behind each prediction directly accessible and inspectable. We will revise the paper to consistently describe this property as inspectability of the prediction evidence, rather than a broader claim of human interpretability.

Reviewer_ABQnOpenReview ↗

Thank you for the response

Thank you for the comprehensive response over my comment. As I indicated in my review, I have relatively low confidence in my assessment of this work. Authors response makes sense to me as fair defense of their work, and the contribution is discussed and compared against the baselines. I therefore change my review to weak accept

Reviewer_ySXdOpenReview ↗
Rating
4(+1)
Confidence
2
Informativeness
3(+1)
Presentation
2
Soundness
2
Read review
Paper summary

This paper introduces conformal maps, which reshape the instruction embedding space by fine-tuning a pretrained encoder. This method aims to retain the original semantic structure while making local support more informative about whether a target LLM will answer a given instruction correctly. Hence It can use a finite reference bank of previously evaluated instructions and their outcomes to predict the LLM’s performance on new instructions. Label-conditional conformal calibration determines separate thresholds for success and failure, converting local-support scores into prediction sets with finite-sample coverage guarantees under exchangeability. The paper presents extensive experiments to evaluate the method’s effectiveness and empirical coverage, and analyzes the effects of key hyperparameters and the trade-off between behavioral separation and semantic preservation.

Critical strengths
  1. The paper presents an extensive experimental evaluation, accompanied by clear and informative analyses. The appendix provides detailed methodological explanations and substantial additional results.
  2. Predicting a target LLM’s performance on unseen instructions from historical evaluation data is an interesting problem with potential practical value, particularly when the assessment does not require querying the target model on the new instructions.
  3. The loss function balances behavioral separation with preservation of the pretrained geometry. The accompanying theoretical analysis and empirical results provide support for this design and clarify the trade-off between these two objectives.
Critical weaknesses
  1. The methodological novelty appears relatively incremental, this approach primarily combines neighborhood-based representation learning, geometry preservation, and standard label-conditional conformal calibration.

  2. Generalization beyond established public benchmarks needs further validation. The evaluation relies on longstanding public benchmarks, with the main experiments using random within-benchmark splits. The paper does not report an analysis of the target models’ prior exposure to these benchmarks or dedicated checks for duplicate and paraphrased questions across the reference bank and held-out evaluation sets. These factors could affect how well the findings extend to independently constructed instructions, particularly because predictions rely on local support from previously evaluated examples.

  3. Although the paper includes cross-benchmark transfer and pooled-training experiments, the evaluated transfer protocol still uses labeled target-benchmark examples for the reference bank, model selection, and calibration. The practical burden of adapting the method to new benchmarks therefore remains insufficiently quantified.

Questions for authors

I find the fine-tuning approach well motivated, and I have a small question about its applicability across benchmarks. Beyond the frozen-encoder baseline already included in the paper, have the authors considered other training-free alternatives? I would be interested in understanding how such approaches might compare with the proposed method in terms of transferability to new benchmarks and the effort required for adaptation. ^ ^

4 comments
AuthorsOpenReview ↗

Our response – part 1

We are glad that the reviewer found the problem interesting and the empirical and theoretical analysis informative. We also appreciate the concrete concerns raised, which led us to clarify the scope of the paper and add several new analyses:

  • W1 (Novelty): We clarify that the contribution is the formulation and study of an inspectable, model-specific geometry of LLM behavior, rather than a new metric-learning or conformal-prediction primitive, and sharpen the theoretical contribution of Appendix A.7.
  • W2 (Generalization): We added a near-duplicate and paraphrase audit, including de-duplicated and semantic-distance-stratified evaluations (new Appendix C.17). We are also evaluating on benchmarks released after the target models’ documented training-data cutoffs and will report those results in a follow-up rebuttal comment.
  • W3 (Adaptation cost): We added a data-efficiency analysis varying calibration-set size, reference-bank size, and representation-training data, and quantify the computational cost of target-benchmark fine-tuning (new Appendix C.15).
  • Q1 (Training-free alternatives): We add the distance-ratio conformal score of Pekala et al. to the frozen-encoder alternatives already evaluated in the paper, and clarify the trade-off between using a frozen encoder, transferring an existing map, and retraining on the target benchmark.

Below, we address each point in detail.

W1. Novelty

We agree that the individual ingredients of our method are established, which we explicitly acknowledge in the paper. We do not intend to claim novelty for any of the components in isolation.

Our contribution is the formulation and study of a different object for LLM evaluation: a model-specific geometry of instruction space in which local neighborhoods encode previously observed successes and failures, enabling more efficient conformal prediction of model success while preserving substantial pretrained semantic organization. Unlike scalar assessor-style evaluations, this geometry exposes structure behind the prediction: for a new instruction, the evaluator can quantify uncertainty while also identifying how much relevant behavioral evidence exists, which outcome it supports, and which prior instructions contribute to that evidence. This is the central contribution of the framework.

Our theoretical contribution is specific to this formulation. Because conformal recalibration changes the decision thresholds along with the learned representation, better discrimination does not automatically imply lower ambiguity. Appendix A.7 characterizes post-calibration ambiguity through the class-conditional ranking of the learned margin, shows that ROC dominance is sufficient to reduce ambiguity for every , including in expectation under finite-sample calibration, and links the logistic neighborhood objective to the likelihood-ratio ranking that optimizes this criterion. The analysis therefore specifies when representation learning yields more informative conformal sets after recalibration.

Finally, the empirical contribution is the finding that such geometries can in fact be learned for LLM behavior: across five benchmarks and three target models, they introduce model-specific behavioral structure while retaining pretrained organization, improve conformal efficiency, and expose reproducible local evidence about previously unseen instructions. We view this as an important contribution in its own right: all reviewers rated the paper highly on informativeness (consensus score 2), consistent with the view that the resulting framework provides useful new insight into instruction-level model behavior even if its individual algorithmic components are familiar.

AuthorsOpenReview ↗

Our response – part 2

W2. Near-duplicates and benchmark exposure

Thank you for your careful comment. We agree that using random splits leaves the possibility of the held-out instructions being near identical to the ones in the training bank. However, this does not immediately make the task easier. We audited every held-out question against the reference bank across all five benchmarks for near-duplicate and paraphrased examples and report these analyses in the new Appendix C.17. In summary,

  • Near-duplicates are the most favourable case for the baseline, not for our method. A near-copy sits at almost zero distance in the pretrained embedding, so the baseline can retrieve it without any learning. On test questions with a near-duplicate in the bank, the pretrained embedding reaches a singleton rate of 0.676 and the learned map cannot improve much on it (0.681, difference +0.005, 95% bootstrap interval [−0.003, +0.014]). Near-duplicates are therefore where our method is hardest to distinguish from the baseline.
  • The gains hold after removing near-duplicates. We removed every near-duplicate from the validation, calibration and test sets and repeated selection, calibration and evaluation. Across the five benchmarks the map improves on the pretrained embedding by 12.8% relative, against 13.9% originally, and coverage remains at the nominal level. On MMLU, the benchmark shown in Figure 14, the gain rises from +0.069 to +0.085.
  • The advantage grows as semantic neighbours become less informative. Splitting the remaining test questions into thirds by pretrained distance to the bank, the gain of the map vs. raw embedding is absent for the nearest third (−0.004), +0.026 for the middle third, and +0.078 for the furthest third. These are the questions for which semantic similarity offers the least, and they are where the learned geometry helps most. A map relying on near-copies would show the opposite pattern.

The reviewer is also right that prior exposure to longstanding public benchmarks is difficult to rule out from the current experiments. To address this concern directly, we are currently running an additional evaluation on benchmarks released after the documented training-data cutoffs of the target models. We will report these results in a follow-up rebuttal comment once the evaluation is complete.

AuthorsOpenReview ↗

Our response – part 3

W3 and Q1. Adapting to a new benchmark, and training-free alternatives

W3 observes that our transfer experiments still use labeled examples from the target benchmark, and that the cost of adapting to a new benchmark is therefore not fully quantified. Q1 asks whether training-free alternatives would transfer more easily or require less adaptation. Both questions reduce to the same practical issue: what is required to apply the method to a new benchmark, and what can be avoided by not retraining the representation? We answer in four steps. We first separate the adaptation cost shared by all methods from the cost specific to ours. We then compare against training-free alternatives, describe the options available on a new benchmark, and finally quantify how much labeled target data is actually required.

Which part of the cost is specific to our method?

The reviewer is right that our transfer protocol uses labeled target examples for the reference bank, model selection, and calibration. Under the standard split-conformal setting used in the paper, target-benchmark calibration labels are required regardless of how the conformity score is obtained, because coverage on the new benchmark is established by calibrating there. Our neighborhood-based training-free baselines also use labeled target examples as the reference bank, and may use a validation split to tune their score. The additional cost of fitting a benchmark-specific conformal map is therefore representation training on the target benchmark.

Do training-free alternatives do better? (Q1)

Since training-free alternatives avoid representation training, the remaining question is how much conformal efficiency they sacrifice. Beyond the frozen encoder with the kernel score already reported in the main paper, the submission evaluates nearest-neighbor voting and a class-centroid score on the frozen representation (Appendix C.8); in the rebuttal, we additionally evaluate the distance-ratio score of Pekala et al. None improves on the strongest training-free baseline. Across the 15 benchmark--model pairs, the best training-free option attains a macro singleton rate of 0.351, compared with 0.405 for the learned map. Thus training-free alternatives remove the representation-training step, but not the need for target calibration, and incur a measurable loss in efficiency.

What are the options on a new benchmark?

A practitioner can choose among three levels of adaptation, all of which retain target-benchmark calibration.

  • Use the frozen encoder. This requires no representation training and gives a singleton rate of 0.351.
  • Reuse a map trained on another benchmark. This likewise requires no representation training on the target benchmark. Across the 20 ordered transfer pairs, 18 show no significant decrease relative to the frozen encoder and 9 show a significant improvement. Separately, a map trained jointly on all five benchmarks raises singleton rate on their union from 0.408 to 0.480, showing that one learned representation can support heterogeneous task distributions, although this pooled experiment is not an unseen-benchmark transfer test.
  • Retrain the map on the new benchmark. Fine-tuning the 0.6B encoder takes under two hours on a single GPU and gives the highest efficiency, with a macro singleton rate of 0.405.

How much labeled data is needed? (W3)

We also added an analysis varying the amount of target-benchmark data used at each stage (new Appendix C.15).

  • Calibration. With only 50 calibration examples, the map already improves on the frozen encoder by 0.041 (95% CI [0.036, 0.047]), and the advantage remains stable as the calibration set grows.
  • Reference bank. Restricting the bank to 30% of the training data gives a singleton rate of 0.396, compared with 0.410 using the full bank.
  • Representation training. Training the map on 60% of the available training data gives 0.376 versus 0.328 for the frozen encoder; at 30%, the corresponding rates are 0.355 and 0.333.
Reviewer_ySXdOpenReview ↗

Response from reviewer ySXd

I appreciate the authors’ clear and thoughtful response, which has addressed several of my concerns and also provided useful insights for my own research. I agree that combining existing methods can make a valuable contribution when the approach is well motivated and technically sound. I find the approach simple yet elegant, and I appreciate its clear motivation and solid execution. I will raise my score accordingly~ ^.^

Comments on the paper

2 comments
AuthorsOpenReview ↗

Global response

We thank the reviewers for their careful and constructive reviews. Below we summarize what the reviews agree on and the new experiments we ran in response. Details are in the individual responses; new material in the revised paper is set in blue.

What the reviewers found valuable

  • A practical problem. "An interesting problem with potential practical value" (ySXd); "addresses a practically relevant problem and presents a well-developed framework" (NuGs).
  • A careful protocol. "The conformal protocol is careful and clean" (ABQn); "The statistical protocol and geometric characterization are thoughtfully organized" (GW9Q).
  • A coherent design. "Using the same local support as training loss, conformity score and explanation is a simple and coherent design" (ABQn).
  • A thorough study. "An extensive experimental evaluation, accompanied by clear and informative analyses" (ySXd); "useful empirical evidence for instruction-level behavioral assessment" (GW9Q).

New experiments

  1. Additional comparisons (ABQn, NuGs, GW9Q). On all 15 benchmark–model pairs, our map exceeds the learned metric of Pekala et al. by +0.040 and conformal training by +0.067 in singleton rate (new Appendix C.16). Against a classifier trained with the same distance-preservation penalty, at a matched budget, the neighborhood loss remains ahead.
  2. Near-duplicates (ySXd, ABQn, NuGs). After removing every near-duplicate from the held-out sets, the relative gain remains and it is largest for the questions furthest from the reference bank (new Appendix C.17).
  3. Data requirements (ySXd, ABQn, NuGs). With only 50 calibration examples the map already improves on the pretrained encoder by 15% in singleton rate, and with only 30% of the reference bank it retains 97% of its full-bank singleton rate (new Appendix C.15).

The remaining questions are answered in the individual responses.

We believe that together, these results complete the comparison with prior work and show that our gains are robust to near-duplicates and to reduced data. They also support the contributions of the paper that go beyond the training method itself:

  • A new object for LLM evaluation: a model-specific geometry of instruction space, in which the past successes and failures of a model form local structure that can be queried for a new instruction.
  • A theoretical account of when learning such a geometry improves conformal efficiency after recalibration, which does not follow from better discrimination alone (Appendix A.7).
  • An empirical finding: across five benchmarks and three target models, these geometries can be learned, improve conformal efficiency at valid label-conditional coverage, and retain pretrained semantic structure.
  • Inspectable predictions: each prediction set comes with the amount and direction of the evidence behind it and the evaluated instructions that contribute to it.

We would be glad to answer any further questions.

Dear Area Chair,

We wanted to briefly follow up on the discussion, as only two of the four reviewers have engaged with our rebuttal so far. In response to the reviews, we have added several experiments and analyses to address the concerns raised, including:

  • New comparisons with metric-learning methods, conformal training, and supervised baselines, including under limited-data settings.
  • A near-duplicate analysis showing that our improvements persist after removing near-duplicates.
  • Additional ablations on data efficiency, implementation choices, and the robustness of the learned geometry.

Of the two reviewers who replied, one acknowledged that their concerns had been addressed and raised their score. The other also acknowledged that most concerns were resolved and requested one final experiment, indicating they would consider raising their score if it was adequately addressed. We have since completed this experiment with positive results, but have not received a further response.

We would be grateful if you could encourage the remaining reviewers to engage with our responses, particularly given the additional experiments conducted to address their specific questions.

Thank you for your time and consideration.

The authors

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

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