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Under review as a conference paper at ICLR 2027

Shortcut to Nowhere: Demystifying Deep Spurious Regression

Abstract

Real-world regression often exhibits shortcuts: attributes that are spuriously correlated with continuous targets in training, yet unreliable under deployment shifts; regressing targets using such shortcuts may fail catastrophically at test time. Existing studies on spurious correlations focus primarily on classification, where labels are categorical and groups are naturally defined. However, many real-world tasks require continuous prediction, where hard label boundaries or discrete group-label pairs do not exist. We define Deep Spurious Regression (DSR) as learning from regression data with attribute-label confounding, addressing continuous spurious correlations, and generalizing to all attribute-label combinations at test time. Motivated by the intrinsic difference between classification and regression shortcuts, we propose to exploit the similarity among spurious attributes in both label and feature spaces, thereby accounting for nearby targets and related groups while calibrating both label and learned feature distributions across attributes. Extensive experiments on common real-world DSR datasets that span computer vision, environmental sensing, and large language model (LLM) regression verify the superior performance of our strategies. Our work fills the gap in benchmarks and techniques for studying spurious correlations in continuous prediction.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
domain generalization, subpopulation shift, spurious regression, robust learning

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
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Paper summary

This paper studies Deep Spurious Regression (DSR), a setting in which a continuous target is correlated with an observed attribute under the training distribution, while evaluation requires generalization across the full target range and across all target–attribute combinations. The paper argues that classification-oriented treatments of spurious correlation do not transfer directly, because continuous targets carry an ordering and meaningful local neighborhoods, and because certain target–attribute combinations may be sparse or entirely absent during training.

The proposed approach smooths the empirical training distribution along two axes. Along the target axis, attribute-conditional label distribution smoothing (LDS) shares information between nearby target values. Along the attribute axis, an affinity matrix transfers count information across related attributes. L-MDS constructs this affinity from Wasserstein-1 distances between per-attribute target distributions, whereas F-MDS uses distances between per-attribute feature centroids. In both cases, the pairwise distances are embedded into two dimensions via multidimensional scaling (MDS), followed by a row-normalized RBF kernel. The resulting smoothed counts define per-sample weights for weighted regression.

The methods are evaluated on UTKFace, SkyFinder, PovertyMap, and CodeNet, with race, camera ID, country, and programming language serving as the respective attributes. Results are reported in terms of overall MAE, per-attribute error, and error across many-, medium-, few-, and zero-shot target–attribute regions. The best proposed variant improves overall MAE over ERM on all four datasets, with the largest gains on CodeNet and in several sparse regimes. However, the improvements are not consistent across metrics or regions, and a number of claims in the experimental discussion are stronger than the tables support. The paper further includes additional baselines, kernel and loss ablations, reduced-data experiments, and a controlled interpolation/extrapolation study.

Critical strengths
  1. The paper identifies an underexplored problem in continuous prediction. Continuous targets introduce ordering, local neighborhoods, interpolation, and missing target–attribute combinations that are not naturally captured by the finite group–label formulation standard in classification. A well-designed benchmark for these phenomena would broaden the study of robustness to shortcut correlations.

  2. The proposed procedures are simple to integrate and are evaluated across several domains. L-MDS and F-MDS can be implemented as reweighting schemes without redesigning the underlying predictor. The evaluation spans visual, environmental, socioeconomic, and code-regression tasks, and the improvements on CodeNet are sizable—provided that the data construction and experimental protocol can be verified.

Critical weaknesses
  1. The benchmark does not convincingly distinguish spurious regression from conditional target imbalance. The proposed methods smooth and reweight discretized (y, a) counts toward the balanced or more-uniform evaluation distribution. This addresses joint target–attribute imbalance, but it does not demonstrate that the predictor has ceased to rely on a shortcut. Camera location, country, programming language, and demographic attributes may themselves carry legitimate target information. The paper offers no counterfactual intervention or direct measurement of shortcut use, and all evaluation is under a single balanced test construction, so spurious dependence is never separated from ordinary domain variation. This concern is particularly acute for CodeNet, where the training set is constructed with 1,500 samples per language and per-language target distributions described only as "Gaussian" (Appendix C.5); if these distributions are identical across languages, then the language–runtime correlation that motivates the benchmark does not exist by construction.

  2. The methodological contribution is incremental and lacks theoretical support. The method is essentially attribute-conditional LDS combined with an MDS/RBF affinity over observed attributes. No analysis is provided for when cross-attribute smoothing is statistically justified, when it reduces shortcut reliance, or when it transfers information between incompatible attributes and induces negative transfer. The choice of a two-dimensional MDS embedding is heuristic, and F-MDS relies on a single global centroid per attribute, which may primarily capture differences in target means rather than attribute-level feature geometry.

  3. The approach assumes that the spurious attribute is known and fully observed. Both the training weights and the cross-attribute affinities require explicit attribute annotations. The paper does not address noisy, partially observed, or unknown shortcut attributes (acknowledged only as future work in the Limitations section), even though these are common in the deployment settings used to motivate DSR. This substantially narrows the scope of the formulation.

  4. The reported experimental configurations and dataset statistics are internally inconsistent. Appendix D states that the main experiments use Gaussian smoothing with k = 5, σ = 2, yet none of the main-table rows for the proposed methods is consistent with this configuration. For example, the UTKFace F-MDS row (overall MAE 7.22) coincides exactly with the k = 9, σ = 1 entry in Table 20 across all average-based columns; the UTKFace L-MDS row (7.30) matches the k = 9, σ = 1 entry rather than the stated k = 5, σ = 2 entry (7.28); the SkyFinder L-MDS row (3.54) does not match the stated configuration (3.57) but instead matches entries such as k = 9, σ = 3; and the PovertyMap L-MDS row (0.486) matches the k = 9, σ = 2 entry exactly. No validation-only model-selection protocol is described. In addition, the stated 10,222 White training samples out of 17,620 correspond to roughly 58%, not the reported 42.4% (which appears to be computed over the full dataset rather than the training split—the denominator should be clarified), and Table 29 reports a maximum per-attribute count of 1,159 for PovertyMap whereas Appendix C.4 reports 1,521 Tanzanian training examples. Because the proposed weights depend directly on these distributions, these inconsistencies prevent reliable reproduction of the headline results.

  5. The empirical advantage is inconsistent, and the contribution of MDS itself is not isolated. The paper does not compare MDS against applying the RBF kernel directly to the original distances, nor against alternative embedding dimensions. The raw results for the attribute-conditional LDS control underlying Table 5 are also omitted. Moreover, the "Ours (best)" rows select different variants for different columns. On SkyFinder, RnC attains lower overall MAE than every proposed variant, while all proposed variants degrade worst-case zero-shot MAE relative to ERM; the methods also frequently sacrifice many-shot performance. As a whole, the tables do not show a consistent benefit for any one fixed variant.

Questions for authors
  1. Main tables vs. Appendix D. The configuration stated in Appendix D (k = 5, σ = 2) does not appear to be the one that produced the main-table rows — UTKFace F-MDS (7.22) matches the k = 9, σ = 1 entry in Table 20 exactly, and similar mismatches show up for SkyFinder and PovertyMap. Could the authors clarify which setting was actually used for each dataset and method, together with the binning rule and K, the exponent α, weight clipping/normalization, MDS dimension, F-MDS update interval, seeds, and the validation criterion used for selection? Two smaller discrepancies: is the 42.4% figure for White in UTKFace computed over the full dataset or the training split (10,222/17,620 ≈ 58%), and which count is correct for PovertyMap — the 1,159 maximum in Table 29 or the 1,521 Tanzanian examples in Appendix C.4?

  2. The CodeNet construction is unclear to me. Appendix C.5 says every language has 1,500 training samples and that the target distribution "follows a Gaussian distribution," but it does not say whether these Gaussians differ across languages. What are the per-language means, variances, and supports? If the distribution is the same for all 13 languages, I do not see what induces the language–runtime correlation that the benchmark is built around.

  3. What evidence is there that models in these benchmarks actually take shortcuts, as opposed to suffering from joint (y, a) imbalance? Quantifying how predictive the attribute alone is, or probing whether predictors trained with and without the proposed weighting differ in their reliance on attribute information, would go a long way here. Evaluation under a shift other than the prescribed balanced test set would also help — right now, the claim of spuriousness rests mostly on the framing.

  4. Is MDS itself contributing anything? It seems the RBF kernel could be applied directly to the Wasserstein or centroid distances without the intermediate embedding. Was this simpler variant tried, and if so, how does it compare? Relatedly, for F-MDS, does a single global centroid per attribute work as well as per-bin or target-conditioned centroids, which might avoid collapsing attributes that differ mainly in target mean?

  5. The "Ours (best)" envelope obscures which algorithm one should actually use: F-MDS wins overall on UTKFace, L-MDS wins on PovertyMap and CodeNet, and on SkyFinder no proposed variant beats RnC. Could the authors report, for a single variant chosen on validation data alone, raw means/stds and paired comparisons against the strongest baseline in each regime? I suspect the sparse- and zero-shot claims would need some revision under this fixed-method analysis, but it would make the empirical case much more convincing either way.

10 comments
AuthorsOpenReview ↗

Response to Reviewer CcXZ (1/8)

We sincerely thank the reviewer for the thoughtful and detailed feedback! We appreciate your recognition of the value of studying spurious correlations in continuous regression and the practical simplicity of our proposed methods. Below, we provide additional explanations and experimental results to address your concerns. We hope these clarifications strengthen our submission.

 

W4&Q1: The configuration stated in Appendix D…could the authors clarify…?

Thank you for pointing out these issues. We clarify our hyperparameter selection protocol and the dataset statistics below.

Hyperparameter selection. All hyperparameters were selected using the validation split only, with the test set reserved for final evaluation, following the protocol in [6]. For L-MDS, we search kernel size k∈{5,9,15}k \in \lbrace 5, 9, 15\rbrace and σ∈{1,2,3}\sigma \in \lbrace 1, 2, 3\rbrace. For F-MDS, we search k∈{3,5,9}k \in \lbrace 3, 5, 9\rbrace and σ∈{1,2}\sigma \in \lbrace1, 2\rbrace, together with inverse and square-root-inverse reweighting. Each configuration is trained with five random seeds. For each dataset and method, we select the configuration with the lowest mean validation MAE across the five runs and report its test performance over the same five seeds.

The original Appendix D reported the implementation defaults (k=5k=5, σ=2\sigma=2), rather than the dataset-specific settings used for the main results. We have clarified this distinction in Appendix D (Table 46) and provided the exact configurations:

DatasetL-MDSF-MDSReweighting
UTKFacek=9, σ=1k=9, σ=1sqrt-inverse
PovertyMapk=9, σ=2k=9, σ=2sqrt-inverse
SkyFinderk=9, σ=3k=9, σ=2sqrt-inverse
CodeNetk=5, σ=2k=5, σ=2sqrt-inverse

For reproducibility, we also provide the remaining implementation details in Appendix D (Table 47):

ItemSetting
Binning ruleUTKFace: 1-year bins over ages 1–116; SkyFinder: 1 °C bins over −30 to 50 °C; PovertyMap: width 0.1 over wealth index −1.1 to 2.5; CodeNet: 10 ms bins over 0–1,000 ms
Affinity constructionPairwise Wasserstein-1 distances between per-attribute target distributions (L-MDS), or Euclidean distances between per-attribute centroids of L2-normalized penultimate features (F-MDS)
Exponent0.5
ClippingNo clipping for square-root-inverse weighting; counts clipped to [5, 1000] for inverse weighting
NormalizationWithin-attribute LDS weights are normalized to mean 1, multiplied by the cross-attribute factor, and then normalized to mean 1 over the training set
MDS dimension2 for both variants
F-MDS update intervalCentroids are recomputed every epoch starting from epoch 5 (epoch 3 for CodeNet), with an exponential moving average of momentum 0.8 applied to the factors
Random seeds1–5
Validation criterionBest checkpoint by validation MAE within each run; best configuration by mean validation MAE across five seeds, selected separately for each dataset and method

Dataset statistics. The reviewer also pointed out two discrepancies in our dataset descriptions, which we clarify below.

UTKFace. The reviewer is correct that 10,222 / 17,620 is 58%. The counts of 10,222 (42.4%) and 1,711 (7.1%) in the original Appendix C.2 refer to the full dataset of 24,103 images before splitting. In the training split of 17,620 images, the White and Others groups contain 8,392 (47.6%) and 830 (4.7%) images, respectively, consistent with Table 43.

PovertyMap. Our benchmark contains 20 attribute groups across 18 countries, with Tanzania and Zimbabwe each divided into rural and urban groups. The 1,159 images in Table 43 correspond to rural Tanzania, while the 1,521 images reported in Appendix C.4 include both rural (1,159) and urban (362) Tanzania. The smallest group is Togo, with 97 images. All weights, affinities, and shot regimes were computed using these 20 attribute groups.

We have corrected and clarified the dataset statistics in Appendices C.2 and C.4, clarified the PovertyMap attribute definition in Section 4, and included the selected hyperparameters and implementation details in Appendix D (Tables 46–47). To support the community and enable future research, we remain committed to fully open-sourcing our research.

 

AuthorsOpenReview ↗

Response to Reviewer CcXZ (2/8)

Q2: The CodeNet construction is unclear to me…

Thank you for pointing out that Appendix C.5 can have more detailed language-specific parameters. We are happy to address uncertainties in the CodeNet experiment construction. The training set distribution does differ by language. We use Gaussian-shaped sampling weights with language-specific centers over the target range (0, 1000] ms. The different distributions per language induce the language–runtime correlation that our CodeNet benchmark is built on. The empirical runtime statistics for each language are listed below:

LanguageMeanStandard deviationObserved range
C318.4175.71–900
C#510.6200.120–1,000
C++173.9132.51–703
D87.3118.41–910
Go389.5244.31–1,000
Haskell243.2259.11–1,000
Java227.0147.730–835
JavaScript203.2153.520–920
Kotlin491.2208.679–999
PHP64.696.79–650
Python199.7140.110–777
Ruby406.9188.17–994
Rust307.9181.92–1,000

We have clarified the language-dependent sampling procedure and included the empirical means, standard deviations, and observed runtime ranges for all 13 programming languages in Appendix C.5 (Table 45).

 

W1&Q3: What evidence is there…as opposed to suffering from joint (y, a) imbalance?

We thank the reviewer for raising this important distinction. We agree that attributes such as camera location, country, and programming language may carry legitimate target information, and we do not assume that all attribute-related information is spurious. Our concern is whether models rely on attribute–target associations that are predictive during training but become unreliable under distribution shift. To distinguish this reliance from the effects of joint (y,a)(y,a) imbalance, we examine the predictive power of the attribute alone, evaluate robustness beyond the balanced test set, and directly probe shortcut reliance through attribute interventions on both synthetic and real-world datasets.

Predictive power of the attribute alone. We evaluate how predictive the attribute alone is using two measures. First, we fit an attribute-only regression model separately on the training and test splits, using the mean target value of each attribute group to measure how much target variance the attribute explains within each distribution (R2R^2). Second, we use the attribute-group means estimated from training to predict the test targets without refitting, measuring whether the learned attribute–target associations transfer to the test distribution. We also compare the transferred predictor against the global training-set mean.

DatasetTrain R2R^2Test R2R^2 (within split)Test R2R^2 (transferred)Test MAE (attribute vs. global mean)
UTKFace0.1310.056−0.09123.13 vs. 22.25
SkyFinder0.3820.2300.1868.63 vs. 9.55
PovertyMap0.6260.0680.0390.756 vs. 0.778
CodeNet0.3660.005−0.117314 vs. 297

Across all four datasets, attributes explain substantially more target variance during training than at test time. Notably, attribute-only predictors trained on UTKFace and CodeNet perform worse than the global-mean baseline at test time, while the predictive power of attributes also declines substantially on PovertyMap and SkyFinder. These findings highlight spurious attribute–target correlations that are predictive during training but become unreliable at test time, providing potential shortcuts for models to exploit.

AuthorsOpenReview ↗

Response to Reviewer CcXZ (3/8)

W1&Q3: What evidence is there…as opposed to suffering from joint (y, a) imbalance? (Continued)

We next examine how model performance changes when these correlations shift.

Robustness beyond the balanced test set. We agree that evaluating additional test distributions can provide a more comprehensive assessment of robustness to spurious correlations. Nevertheless, evaluating on a balanced test distribution is a common practice in prior work on spurious correlations. For example, Group DRO [1] uses a 95% bird–background correlation during training on Waterbirds and a balanced test distribution. Similarly, IRM [12] evaluates ColoredMNIST under a shifted color–label correlation (10% at test time versus 80–90% during training). While these evaluation protocols are widely adopted, we further extend our evaluation to address the reviewer's concern. Specifically, we importance-reweight the saved test predictions [11], without retraining, to evaluate three attribute–target dependencies: training-aligned, balanced, and reversed. The reversed setting emphasizes attribute–target combinations that were underrepresented during training, allowing us to assess model robustness when the spurious correlations are reversed.

DatasetMethodTrain-alignedBalancedReversedReversed − Train
UTKFaceERM6.75 ± 0.037.39 ± 0.077.69 ± 0.120.95
L-MDS6.74 ± 0.197.30 ± 0.097.64 ± 0.100.90
F-MDS6.73 ± 0.097.22 ± 0.157.52 ± 0.230.79
SkyFinderERM2.84 ± 0.043.68 ± 0.035.27 ± 0.042.43
L-MDS2.84 ± 0.023.54 ± 0.024.76 ± 0.071.92
F-MDS2.86 ± 0.033.56 ± 0.024.74 ± 0.081.88
PovertyMapERM0.416 ± 0.0260.504 ± 0.0090.586 ± 0.0130.170
L-MDS0.407 ± 0.0020.486 ± 0.0090.562 ± 0.0120.155
F-MDS0.417 ± 0.0180.488 ± 0.0030.551 ± 0.0100.134

Under training-aligned dependence, ERM performs comparably to L-MDS and F-MDS across all three datasets. However, when the attribute–target correlations are reversed, ERM experiences a larger increase in MAE, particularly on SkyFinder and PovertyMap, where both L-MDS and F-MDS achieve lower errors and smaller performance gaps. These results suggest that our methods reduce reliance on unstable spurious correlations and improve robustness beyond the original balanced test distribution.

We further evaluate ColoredRotatedMNIST under varying strengths of spurious color–angle correlations (ρ=0.75,0.90,0.95\rho=0.75, 0.90, 0.95).

ρ\rhoMethodTrain-alignedBalancedReversedReversed − Train
0.75ERM7.29 ± 0.268.90 ± 0.109.68 ± 0.102.39
L-MDS8.10 ± 0.178.65 ± 0.068.99 ± 0.090.89
F-MDS8.08 ± 0.158.55 ± 0.049.08 ± 0.151.01
0.90ERM7.27 ± 0.1813.15 ± 1.1616.01 ± 1.438.74
L-MDS8.86 ± 0.6010.68 ± 0.8611.22 ± 0.372.36
F-MDS8.95 ± 0.4510.48 ± 0.3411.97 ± 0.363.02
0.95ERM6.75 ± 0.0722.28 ± 2.3622.72 ± 2.2615.97
L-MDS9.35 ± 1.2614.22 ± 1.3115.30 ± 2.245.95
F-MDS9.17 ± 0.3313.23 ± 1.0115.25 ± 1.156.08

As the spurious correlation strengthens, ERM becomes increasingly sensitive to changes in attribute–target dependence, with its reversed-minus-training MAE gap increasing from 2.39° to 15.97°. In contrast, L-MDS and F-MDS consistently exhibit substantially smaller gaps across all three settings, demonstrating improved robustness under stronger spurious correlations.

Reviewer_7ucsOpenReview ↗
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2
Confidence
3
Informativeness
2
Presentation
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Soundness
2
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Paper summary

This paper studies spurious correlations in regression, focusing on uneven target coverage within and across annotated attributes. The authors propose L-MDS and F-MDS, which combine conditional label density smoothing with another weighting term across attributes. L-MDS measures attribute similarity using Wasserstein distances between target distributions, while F-MDS uses distances between centroids of normalized features. These distances are mapped to two dimensions through multidimensional scaling and used to smooth the counts that determine the weights. The experiments cover age, temperature, poverty, and code runtime prediction, with errors reported by attribute and target-density region. Both methods improve overall error over ERM. Their advantage over other reweighting methods, and their performance in sparse regions, vary across the datasets.

Critical strengths
  1. A target value can be common overall but rare within one attribute. Looking at the conditional target distribution therefore addresses a problem that marginal label balancing can miss. The paper studies this in four different regression applications.

  2. L-MDS is easy to use since its weights can be computed before training and it adds nothing at inference. On CodeNet, it lowers overall MAE from 248.2 with square-root reweighting to 243.4. The combined variant also improves the zero-shot results, and Table 5 shows gains over conditional LDS.

Critical weaknesses
  1. Much of the evaluation concerns uneven attribute-target coverage and more balanced test distributions. The improvement could come from correcting these frequencies, without showing that the model relies less on a spurious attribute. This is close to the imbalance problem studied in [1]. The paper already has ColoredRotatedMNIST to study attribute-target dependence, but only uses it to analyze ERM. I would expect the proposed methods to be tested there, with the dependence changed and marginal target frequencies kept fixed.
  2. Table 5 does not isolate the MDS geometry. The full method adds another inverse-count factor on top of conditional LDS, so even an identity affinity would change the weights. The improvement could partly come from this additional reweighting. I am also not sure why similarity between marginal target distributions or feature centroids should determine which attributes help each other in a particular sparse region. Both comparisons use information across the full target range. A comparison with simple affinities at the same reweighting strength is missing.
  3. F-MDS is effectively tied with LDS in overall UTKFace error, and RnC performs better overall on SkyFinder. CodeNet and PovertyMap have better results. I do not think the paper explains these differences well enough to tell when the proposed weighting should be used, or how to choose between label and feature affinities.
  4. The text claims lower worst-case zero-shot error on SkyFinder, but Table 2 does not show this relative to ERM. On CodeNet, L-MDS lowers overall MAE relative to square-root reweighting while increasing average zero-shot MAE from 498.1 to 523.6. F-MDS and the combined variant do better in that region. The limitations discuss a tradeoff with dense regions, but this does not explain why L-MDS can lose on the sparse regions it is intended to help.

[1] Delving into Deep Imbalanced Regression, ICML 2021.

Questions for authors
  1. Do L-MDS and F-MDS help on ColoredRotatedMNIST when attribute-target dependence changes but marginal target frequencies stay fixed?

  2. How do identity or uniform affinities compare at the same reweighting strength? Do similar attributes actually benefit from sharing counts?

  3. What explains the different zero-shot results of L-MDS and F-MDS, and how should the variant be selected?

4 comments
AuthorsOpenReview ↗

Response to Reviewer 7ucs (1/3)

We sincerely thank the reviewer for the detailed and constructive feedback! We appreciate your recognition of the value of attribute-conditional target distributions, the simplicity of our proposed methods, and our experimental evaluation across four regression applications. Below, we provide additional explanations and experimental results to address your concerns. We hope these clarifications strengthen our submission.

 

W1&Q1: Much of the evaluation concerns uneven attribute-target coverage and more balanced test distributions…Do L-MDS and F-MDS help on ColoredRotatedMNIST…?

Thank you for suggesting this experiment. We conducted an additional analysis on ColoredRotatedMNIST to examine whether L-MDS and F-MDS remain effective when marginal target frequencies are fixed but attribute–target dependence changes. We vary the color–target correlation ρ∈{0.50,0.75,0.90,0.95}\rho \in \lbrace 0.50, 0.75, 0.90, 0.95\rbrace, where ρ\rho is the probability that an image has the background color associated with its rotation angle. Each setting contains 2,400 training images, with 600 images per color and per 45° angle bin. Thus, both marginal distributions remain uniform while the color–target dependence changes. The training sample counts are shown below. Bold entries indicate the angle bin associated with each background color.

ρ\rhoRotation angleRedBlueGreenYellow
0.500°–45°300100100100
45°–90°100300100100
90°–135°100100300100
135°–180°100100100300
0.750°–45°450505050
45°–90°504505050
90°–135°505045050
135°–180°505050450
0.900°–45°540202020
45°–90°205402020
90°–135°202054020
135°–180°202020540
0.950°–45°570101010
45°–90°105701010
90°–135°101057010
135°–180°101010570

We report overall MAE, off-diagonal MAE (where the background color is associated with a different angle bin), and color sensitivity. To measure color sensitivity, we change each test image's background to each of the other three colors while keeping the digit and rotation fixed, and compute the average absolute change in predicted angle. Lower values indicate less sensitivity to background color.

ρ\rhoMethodTest MAE ↓Off-diagonal MAE ↓Color sensitivity (°) ↓
0.50ERM7.97 ± 0.048.30 ± 0.063.09 ± 0.33
L-MDS7.76 ± 0.107.87 ± 0.081.59 ± 0.27
F-MDS7.77 ± 0.117.89 ± 0.061.73 ± 0.14
0.75ERM8.90 ± 0.109.68 ± 0.225.86 ± 0.22
L-MDS8.65 ± 0.068.92 ± 0.063.12 ± 0.32
F-MDS8.55 ± 0.048.87 ± 0.102.97 ± 0.30
0.90ERM13.15 ± 1.1615.50 ± 1.5213.55 ± 1.66
L-MDS10.68 ± 0.8611.34 ± 0.955.27 ± 0.70
F-MDS10.48 ± 0.3411.27 ± 0.345.58 ± 0.36
0.95ERM22.28 ± 2.3627.72 ± 3.0926.81 ± 3.01
L-MDS14.22 ± 1.3115.80 ± 1.5110.28 ± 0.89
F-MDS13.23 ± 1.0114.74 ± 1.139.44 ± 1.28

As attribute–target dependence increases, both L-MDS and F-MDS achieve larger improvements over ERM despite the unchanged marginal target distribution. At ρ=0.95\rho=0.95, L-MDS and F-MDS reduce overall MAE from 22.28 to 14.22 and 13.23, respectively, and off-diagonal MAE from 27.72 to 15.80 and 14.74. Color sensitivity also decreases from 26.81° for ERM to 10.28° and 9.44°, respectively, a reduction of over 60%. These results show that L-MDS and F-MDS improve generalization even when marginal target frequencies are held fixed. The recoloring analysis further shows that these improvements are accompanied by substantially reduced reliance on the spurious color attribute, rather than merely improved prediction accuracy. We have included these results and the detailed training distributions in Appendix B.11 (Tables 34–35).

 

AuthorsOpenReview ↗

Response to Reviewer 7ucs (2/3)

W2&Q2: How do identity or uniform affinities compare…?

Thank you for suggesting this ablation. We agree that isolating the contribution of attribute similarity from additional reweighting is important. We therefore compare our method against identity and uniform affinities under the same reweighting framework, keeping all other settings unchanged. Following [1, 2], we use paired bootstrap resampling (B=2,000B=2{,}000) to compute 95% CIs on Δ\Delta (Improvement), and assess significance with a Wilcoxon signed-rank test [3]:

DatasetComparison95% CIp-val
UTKFaceL-MDS vs. Identity[0.007, 0.308]0.029
L-MDS vs. Uniform[0.015, 0.301]0.041
PovertyMapL-MDS vs. Identity[0.001, 0.040]0.039
L-MDS vs. Uniform[0.005, 0.034]0.003
SkyFinderL-MDS vs. Identity[0.001, 0.091]0.038
L-MDS vs. Uniform[−0.033, 0.058]0.605
CodeNetL-MDS vs. Identity[8.5, 18.3]<0.001
L-MDS vs. Uniform[1.0, 11.2]0.009

Our method achieves statistically significant improvements over identity affinity across all four datasets and over uniform affinity on three of the four datasets. The improvements over identity affinity show that the gains extend beyond additional inverse-count weighting, while the comparisons with uniform affinity demonstrate the benefits of sharing counts according to attribute similarity. Together, these results provide evidence that MDS-derived attribute similarities contribute to the performance improvements beyond additional reweighting. We have included these ablation results and statistical tests in Appendix B.14 (Table 40).

 

W3 & Q3b: … how to choose between label and feature affinities?

We thank the reviewer for raising this point. While our methods do not outperform every baseline on every dataset, they achieve strong average performance across datasets and metrics. As shown in Table 19 (Appendix), L-MDS and F-MDS rank first and second on overall MAE (2.00 and 2.75), attribute-average error (2.00 and 2.75), and few-shot error (2.75 and 3.25). F-MDS also achieves the best average rank on zero-shot error (2.33). In contrast, ERM performs best on many-shot error (1.75), reflecting the trade-off between densely represented and underrepresented regions discussed in Section 5. Comparing the two variants, L-MDS performs better on overall MAE, attribute-average error, while F-MDS achieves better average rank on zero-shot error (2.33 vs. 4.00).

Beyond predictive performance, training efficiency is another important consideration when selecting between the two methods. L-MDS builds its attribute kernel from the training label distributions alone, so the kernel is computed once before training and adds no per-epoch cost. F-MDS re-extracts features and recomputes attribute centroids at every epoch, which is the source of its overhead. We report per-epoch wall-clock time, taken as the median gap between consecutive validation evaluations and averaged over five random seeds:

DatasetL-MDS (s/epoch)F-MDS (s/epoch)F-MDS slowdown
PovertyMap9.2 ± 2.213.3 ± 0.01.44x
UTKFace23.4 ± 0.232.1 ± 1.31.37x
SkyFinder60.0 ± 0.191.5 ± 1.41.53x

F-MDS costs roughly 40–50% more per epoch than L-MDS across these three image datasets. The overhead is a single gradient-free forward pass over the training set, so it is modest in relative terms but grows in absolute terms with the size of the training set.

Considering both predictive performance and computational cost, we would therefore recommend L-MDS as the default, since it is cheaper, requires no trained model to construct its kernel, and performs better on average across the aggregate metrics. F-MDS may be preferable when zero-shot performance is the primary concern, as it achieves a better average rank on zero-shot error. It may also be useful when attributes have similar marginal target distributions but distinct representational structure, since the label-space distances used by L-MDS may not capture these differences.

We have included this analysis and the guidance for selecting between L-MDS and F-MDS in Appendix B.15 (Table 41), together with the performance ranking results in Table 19.

 

AuthorsOpenReview ↗

Response to Reviewer 7ucs (3/3)

W4&Q3a: What explains the different zero-shot results…?

We thank the reviewer for highlighting these differences. We agree that the claim of a lower worst-case zero-shot error on SkyFinder is not supported by Table 2, and we have revised our manuscript accordingly.

On CodeNet, L-MDS achieves lower overall MAE than square-root reweighting (243.4 vs. 248.2), but higher zero-shot MAE (523.6 vs. 498.1), while still improving both metrics over ERM (overall 268.7, zero-shot 565.8). This shows that improvements in overall MAE do not necessarily translate into better zero-shot performance. A similar distinction between average and worst-group performance has been observed in classification [4], where methods with higher average accuracy do not necessarily achieve better worst-group accuracy.

To understand this difference on CodeNet, we consider how L-MDS and F-MDS define cross-language similarity. L-MDS measures language similarity using Wasserstein distances between marginal runtime distributions. However, programming languages with similar runtime distributions may still differ substantially in syntax and standard library overhead, which may limit the usefulness of label-based similarities for zero-shot prediction.

In contrast, F-MDS defines language similarity using decoder-feature centroids, capturing relationships between languages in the model's representation space. These feature-based similarities may capture information relevant to runtime prediction that is not reflected in marginal runtime distributions, potentially explaining why F-MDS achieves lower zero-shot MAE than L-MDS on CodeNet (490.0 vs. 523.6).

The combined L-MDS and F-MDS variant applies both similarity-based reweighting factors and achieves the lowest zero-shot MAE on CodeNet (483.4), suggesting that label-based and feature-based similarities can provide complementary information in this setting. As discussed in our response to W3, we recommend L-MDS as the default due to its lower computational cost and stronger average performance across aggregate metrics. F-MDS may be preferable when zero-shot performance is the primary concern, as it achieves a better average rank on zero-shot error shown by Table 19. We have clarified these trade-offs and provided guidance for method selection in Appendix B.15 (Table 41), with the performance rankings reported in Table 19.

 


References:

  1. An Introduction to the Bootstrap. Chapman & Hall, 1993.
  2. Statistical Significance Tests for Machine Translation Evaluation. EMNLP 2004.
  3. Individual Comparisons by Ranking Methods. Biometrics Bulletin, 1945.
  4. Distributionally Robust Neural Networks for Group Shifts: On the Importance of Regularization for Worst-Case Generalization. ICLR 2020.

 


We hope the above responses have addressed all concerns from the reviewer adequately. We would also like to update the reviewer on our commitment to open‑sourcing Deep Spurious Regression (DSR) to support future research in the community:

  • Benchmark. We will release the complete benchmark construction pipeline, following the data use agreements of the source datasets.
  • Pretrained model. We will release the L-MDS and F-MDS checkpoints trained on each benchmark dataset, together with example code for inference and training.
  • Code. We will open-source the complete code, including implementations of all baselines, to facilitate reuse by the broader research community.

Once again, thanks for your time and constructive feedback. We would really appreciate it if the reviewer could consider raising their scores and championing the paper.

AuthorsOpenReview ↗

Discussion period ending soon; We would like to hear back from Reviewer 7ucs

We would like to thank the reviewer again for your time and effort. In response to your comments, we have provided additional results and clarifications that we hope have addressed all your concerns.

Given there is only less than 1 day left in the discussion period, we wanted to kindly follow up to check whether you have seen our responses and whether there are any final clarifications we can address. If the concerns of the reviewer are resolved and the reviewer is convinced of the novelty and completeness of our work, we'd be grateful if the reviewer could update your review and score to reflect that, so we know that our response has been seen.

Once again, many thanks for your time and dedication to the review process, we are extremely grateful.

Reviewer_XH2kOpenReview ↗
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Paper summary

The paper studies spurious correlations in regression, where a model may use an attribute that is correlated with the target in the training data but does not generalize well. Unlike classification, regression has continuous labels, so nearby target values can provide useful information to each other. The paper proposes two methods, L-MDS and F-MDS, that reweight training samples based on the density of nearby target values and the similarity between different spurious attributes. L-MDS measures this similarity using the label distributions, while F-MDS uses the learned features. The methods are evaluated on several regression tasks including age, temperature, poverty, and code runtime prediction, and generally improve performance, particularly for target-attribute combinations with limited or no training data.

Critical strengths

The problem is interesting and relatively underexplored because most spurious-correlation work focuses on classification, while continuous regression has a different structure. I also find the observation that nearby regression targets can provide useful information to each other intuitive and interesting. The idea of additionally transferring information between similar spurious attributes is reasonable, and the paper evaluates it across several different domains rather than only on a synthetic example. Experiment section is quite extensive.

Critical weaknesses

My main concern is that the setting assumes that the spurious attribute is known beforehand. This is a strong assumption because in realistic applications we may not know which feature the model is exploiting as a shortcut, and there may be multiple interacting spurious attributes rather than one predefined attribute such as race, camera ID, country, or programming language. The authors also acknowledge that their formulation currently assumes availability of these attributes.

I also think the conceptual novelty of the method itself is somewhat limited. Much of the method can be understood as distribution smoothing/reweighting: smooth across nearby continuous labels and then additionally smooth counts across predefined attributes according to their similarity. The use of MDS makes this more structured, but I am not completely convinced that MDS itself is essential rather than one particular way of constructing an attribute-similarity kernel. Finally, the improvement is not uniform the methods can perform similarly to or worse than baselines in data-dense regions, indicating a tradeoff between improving sparse regions and preserving performance where sufficient data already exists.

Questions for authors

The method assumes that the spurious attribute is already known. How would the method work when we do not know what shortcut the model is using, or when there are multiple spurious attributes at the same time?

What happens if the attribute we provide is not actually the main spurious feature that the model is using?

The final method is essentially reweighting the training samples. How important is MDS specifically? Could you directly use the distances between the label to calculate the weights?

The method improves the results in few-shot and zero-shot regions, but sometimes like on PovertyMap, L-MDS and F-MDS slightly degrade MAE in the many-shot region while improving performance in the sparse regions. Why does the reweighting hurt the samples, and can this trade-off be avoided?

7 comments
AuthorsOpenReview ↗

Response to Reviewer XH2k (1/5)

Thank you for your detailed feedback! We appreciate your recognition of the importance of studying spurious correlations in regression, the intuition behind leveraging nearby continuous targets, and our extensive experimental evaluation across several domains. Below, we provide additional explanations and experimental results in response to your questions. We hope these clarifications address your concerns and strengthen our submission.

 

W1&Q1a: …assumes that the spurious attribute is already known…when we do not know what shortcut the model is using?

Thank you for raising this point. We agree that the scope of our method deserves to be stated more explicitly.

The known-attribute setting is widely adopted in the spurious-correlation literature. GroupDRO [1], group balancing and reweighting [2], last-layer retraining [3], LISA [4], and the subpopulation-shift benchmarks WILDS [5] and SubpopBench [6] all study settings involving group or attribute annotations. Even methods designed to operate without training-group annotations, such as JTT [7], LfF [8], and EIIL [9], do not fully eliminate the challenges of group-aware model selection and evaluation. Our assumption is therefore consistent with a widely studied setting in the literature, rather than being specific to our method.

Our contribution is to extend this setting to regression. To our knowledge, this is the first work to systematically study spurious correlations in regression with continuous targets. We formulate DSR as regression learning under attribute–target confounding, where models must generalize across the full target range and all attribute–target combinations. We also curate benchmark datasets spanning vision, environmental sensing, and LLM regression, and introduce regime-wise evaluation (many-shot / medium-shot / few-shot / zero-shot) to assess performance under varying levels of training support. We adopt the known-attribute setting to isolate the challenges specific to regression, without introducing the additional problem of inferring unknown groups.

We have explicitly acknowledged this limitation in Section 5 (Discussion). Our current framework assumes that spurious attribute annotations are available during training. In principle, the attribute–target count table and regime-wise evaluation could also be constructed using inferred groups, since L-MDS requires per-group target distributions and F-MDS requires per-group feature centroids. However, identifying meaningful groups without attribute annotations remains an open problem, particularly for continuous targets. We have included this limitation and identified partially observed or unknown spurious attributes as an important direction for future work in Section 5 (Discussion).

AuthorsOpenReview ↗

Response to Reviewer XH2k (2/5)

W1&Q1b: How would the method work … when there are multiple spurious attributes at the same time?

Thank you for raising this important question. Our method extends to multiple spurious attributes by treating each joint attribute combination as a single attribute, constructing the corresponding joint attribute–target count table, and applying the same L-MDS or F-MDS procedure. To evaluate this extension, we conduct additional experiments on ColoredRotatedMNIST and UTKFace, examining its effectiveness in both controlled and real-world settings.

ColoredRotatedMNIST. Building on the original setting in Appendix C.1, we introduce stroke intensity (dim or bright) as a second spurious attribute alongside background color, associating it with rotation angles below or above 90°, respectively. We set ρc=0.75\rho_c=0.75 and ρs=0.9\rho_s=0.9, denoting the probabilities of assigning the background color and stroke intensity associated with each image's target angle, respectively. We use 2,400 training images and 7,200 images each for validation and testing, balanced across rotation angles and both attributes. To measure shortcut dependence, we change each test image's background to each of the other three colors or switch its stroke intensity while keeping the digit and rotation fixed. We report two metrics: sensitivity, the mean absolute change in predicted angle, and shortcut reliance, the mean signed prediction change toward the new attribute's training-associated angle. Lower sensitivity indicates less dependence on the attribute, while lower positive shortcut reliance indicates weaker dependence on the spurious attribute–target correlation learned during training.

MethodMAE (°) ↓Color sensitivity (°) ↓Color shortcut reliance (°) ↓Stroke sensitivity (°) ↓Stroke shortcut reliance (°) ↓
ERM16.57 ± 3.2213.99 ± 3.829.82 ± 3.8120.68 ± 6.8217.10 ± 7.25
L-MDS Single-attribute (color)15.28 ± 1.925.17 ± 0.292.31 ± 0.7819.64 ± 4.0414.49 ± 3.95
L-MDS Single-attribute (stroke)13.64 ± 2.6911.47 ± 3.547.21 ± 2.509.57 ± 4.086.97 ± 3.21
L-MDS Multi-attribute (color + stroke)11.60 ± 0.655.84 ± 1.133.61 ± 0.907.09 ± 1.755.04 ± 1.54

The multi-attribute variant achieves the lowest MAE, reducing error by approximately 30% relative to ERM, while substantially reducing sensitivity to both color (13.99° to 5.84°) and stroke intensity (20.68° to 7.09°). Shortcut reliance also decreases for both attributes (9.82° to 3.61° for color and 17.10° to 5.04° for stroke), indicating weaker dependence on their spurious training associations.

UTKFace. We also test the multi-attribute extension on UTKFace, using race and gender as spurious attributes for age prediction. Since we cannot directly change these attributes in real images, we instead shift the model's feature representations using differences between attribute-specific training feature means at matched ages. We measure sensitivity as the mean absolute change in predicted age and shortcut reliance as the signed prediction change in the direction of the difference between the two attribute groups' mean training ages.

MethodMAE (years) ↓Race sensitivity (years) ↓Race shortcut reliance (years) ↓Gender sensitivity (years) ↓Gender shortcut reliance (years) ↓
ERM7.39 ± 0.071.12 ± 0.190.72 ± 0.170.84 ± 0.230.35 ± 0.33
L-MDS Single-attribute (race)7.30 ± 0.090.85 ± 0.070.52 ± 0.090.79 ± 0.080.35 ± 0.16
L-MDS Single-attribute (gender)7.36 ± 0.100.94 ± 0.050.65 ± 0.070.53 ± 0.040.26 ± 0.30
L-MDS Multi-attribute (race + gender)7.23 ± 0.030.79 ± 0.070.49 ± 0.040.71 ± 0.030.17 ± 0.02

The multi-attribute variant achieves the lowest MAE (7.23 vs. 7.39 for ERM), while reducing race sensitivity from 1.12 to 0.79 and gender sensitivity from 0.84 to 0.71. Shortcut reliance also decreases for both attributes (0.72 to 0.49 for race and 0.35 to 0.17 for gender).

Together, these results show that our method effectively handles multiple spurious attributes, achieving better prediction accuracy than the single-attribute variants while reducing reliance on both shortcuts. We have included the multi-attribute extension in Section 3.3 and the additional experiments on ColoredRotatedMNIST and UTKFace in Appendix B.7 (Tables 29–30).

AuthorsOpenReview ↗

Response to Reviewer XH2k (3/5)

Q2: What happens if the attribute we provide is not actually the main spurious feature that the model is using?

Thank you for raising this important question. The multi-attribute experiments in Q1b allow us to examine this case on both datasets.

On ColoredRotatedMNIST, stroke intensity is the stronger shortcut under ERM, with higher sensitivity (20.68° vs. 13.99°) and shortcut reliance (17.10° vs. 9.82°) than background color. When only color is provided to our method, color sensitivity decreases from 13.99° to 5.17° and shortcut reliance from 9.82° to 2.31°, while MAE improves from 16.57° to 15.28°.

On UTKFace, race shows greater sensitivity (1.12 vs. 0.84) and shortcut reliance (0.72 vs. 0.35) than gender under ERM. When only gender is provided to our method, gender sensitivity decreases from 0.84 to 0.53 and shortcut reliance from 0.35 to 0.26, while MAE improves from 7.39 to 7.36.

Together, these results show that our method remains effective even when the provided attribute is not the dominant shortcut, reducing reliance on the specified spurious attribute and improving prediction accuracy on both datasets. We have included this analysis in Appendix B.8, based on the experimental results reported in Tables 29–30.

 

W2: I also think the conceptual novelty of the method itself …

Thank you for raising this concern. We agree that the individual components of our method are classical, and this is deliberate. To the best of our knowledge, we are the first to systematically study spurious correlations in regression by addressing imbalance along two axes: the target axis, where neighbouring label values can share information, and the attribute axis, where attributes with similar target or feature distributions can share statistical strength.

The simplicity of our method also has practical value. Both L-MDS and F-MDS reduce to a reweighted regression loss, requiring no architectural changes or auxiliary training, and can be applied across different model architectures. This makes them applicable to modern LLM settings, as demonstrated by our CodeNet benchmark, where the same weighting framework is applied to a language model for continuous runtime prediction.

Beyond the method itself, the novelty of our work also lies in the development of DSR benchmarks and a unified evaluation protocol spanning computer vision, environmental sensing, and code runtime prediction. Unlike conventional regression benchmarks that primarily focus on overall prediction error, our evaluation explicitly examines generalization across different attribute–target combinations and density regimes, including few-shot and zero-shot regions. These benchmarks and evaluation protocols provide a new setting for systematically studying spurious correlations in continuous regression.

Together with our problem formulation and proposed reweighting methods, they represent the key novel contributions of our work. These contributions are described in Section 1 (Introduction), with the two-axis smoothing framework detailed in Section 3 (Methods) and the benchmark and evaluation protocol presented in Section 4 (Benchmarking DSR).

 

W2&Q3: How important is MDS specifically? …directly use the distances…?

Thank you for this insightful question. The main motivation for using MDS is to provide a principled construction of attribute similarities with well-defined mathematical properties. In L-MDS, attribute dissimilarities are measured using 1-Wasserstein distances between per-attribute target distributions. By Schoenberg's theorem [10], a Gaussian kernel k(x,x′)=exp⁡(−λd(x,x′)2)k(x,x')=\exp(-\lambda d(x,x')^2) is positive semidefinite (PSD) for every λ>0\lambda>0 if and only if d2d^2 is conditionally negative definite. General Wasserstein distances are not guaranteed to satisfy this condition, so directly applying a Gaussian RBF to the original distance matrix does not guarantee a PSD kernel. In contrast, MDS provides Euclidean attribute coordinates on which the Gaussian RBF is PSD by construction, prior to row normalization.

We also examine how much of the attribute geometry is preserved by the 2D embedding:

Dataset# AttributesVariance retained in 2D
UTKFace599.5%
PovertyMap2098.6%
SkyFinder4795.2%
CodeNet1398.5%

The 2D embeddings retain over 95% of the measured variance across all four datasets, including SkyFinder (47 attributes) and PovertyMap (20 attributes). These results suggest that MDS captures much of the attribute geometry in a compact Euclidean representation while providing a mathematically grounded construction of attribute similarities. We have included this analysis and the corresponding results in Appendix B.9 (Table 31).

 

Comments on the paper

1 comment
AuthorsOpenReview ↗

General Response to All Reviewers

We thank all the reviewers for acknowledging the contributions of our work and providing insightful comments and suggestions! We are glad to see that the reviewers found that:

  1. Studying spurious correlations in continuous regression is an interesting and relatively underexplored problem (Reviewers XH2k, CcXZ).
  2. Exploiting nearby regression targets and transferring information across similar spurious attributes is intuitive and reasonable (Reviewer XH2k).
  3. Considering attribute-conditional target distributions addresses a limitation of marginal label balancing (Reviewer 7ucs).
  4. Our methods are simple and easy to integrate into existing models, with L-MDS requiring no additional inference overhead (Reviewers 7ucs, CcXZ).
  5. The experimental evaluation is extensive and covers four diverse real-world regression applications (Reviewers XH2k, 7ucs, CcXZ).
  6. The paper is clearly presented and easy to follow (Reviewers 7ucs, CcXZ).

 

To address concerns raised by the reviewers, we have made the following changes and updated the manuscript accordingly (all changes are highlighted in red in the updated paper):

  1. We added an extension to multiple spurious attributes in Section 3.3, with additional experiments in Appendix B.7 (Tables 29–30), and examined cases where the provided attribute is not the dominant shortcut in Appendix B.8, as suggested by Reviewer XH2k.

  2. We evaluated our methods on ColoredRotatedMNIST under varying spurious correlation strengths while keeping the marginal target distribution fixed in Appendix B.11 and Tables 34–35. We also measured color sensitivity and shortcut reliance to assess whether our methods reduce dependence on spurious attributes, as suggested by Reviewers 7ucs and CcXZ.

  3. We added attribute-only prediction analyses and evaluated robustness under different test distributions in Appendix B.12 and Tables 36–38. We further conducted counterfactual and feature-space interventions in Appendix B.13 and Table 39 to directly measure shortcut reliance, as suggested by Reviewer CcXZ.

  4. We analyzed MDS geometry and kernel properties in Appendix B.9 and Table 31, compared MDS-based affinities with identity and uniform affinities under the same reweighting framework in Appendix B.14 and Table 40, and evaluated global versus target-conditioned feature centroids for F-MDS in Appendix B.16 and Table 42, as suggested by Reviewers XH2k, 7ucs, and CcXZ.

  5. We investigated the effects of reweighting strength in Appendix B.10 (Tables 32–33) and added an analysis of method selection and computational efficiency in Appendix B.15 (Table 41), clarifying the trade-offs across different target-density regions and the differences between L-MDS and F-MDS, as suggested by Reviewers XH2k and 7ucs.

  6. We clarified the construction of CodeNet by specifying the language-dependent runtime distributions and reporting empirical statistics for all 13 programming languages in Appendix C.5 and Table 45, as suggested by Reviewer CcXZ.

  7. We corrected the dataset statistics for UTKFace and PovertyMap in Appendices C.2 and C.4, and clarified the validation-based hyperparameter selection protocol and implementation details in Appendix D and Tables 46–47, as suggested by Reviewer CcXZ.

 

We hope our responses have addressed all concerns from the reviewers adequately. We thank all reviewers again for their time and feedback, and please feel free to let us know if there are other clarifications or experiments we can offer. We would really appreciate it if the reviewers could consider raising their scores after evaluating our updates.

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

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