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Under review as a conference paper at ICLR 2027

The Standardization Trap: Certifying Joint Label Processing in Tabular Foundation Models

Abstract

Linear regression and kernel smoothing offer tractable explanations of in-context learning: in both, the features determine the weight assigned to each context label. However, whether this fixed-weight account describes pretrained tabular foundation models (TFMs) remains unclear. Testing this account using derivatives runs into a standardization trap: public TFM packages standardize the labels before the model sees them, yet ordinary derivatives also reflect behavior outside the set of standardized labels, making a model appear nonlinear even when every prediction it makes agrees with a fixed-weight map. We propose two certificates that depend only on predictions at standardized labels and can reject two distinct explanations: fixed-weight prediction and sums of independent nonlinear label transformations. Across the five public TFMs that we evaluate, our certificates show that changing one context label alters how other labels influence the prediction, a behavior we call joint processing. We further find that joint processing emerges with training and that attention scores carry most of the measured interaction. Together, these findings motivate TFM explanations that account for how context labels change the influence of individual examples.

Primary area:
foundation or frontier models, including LLMs
Keywords:
tabular foundation models, in-context learning, label interaction

Reviews

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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_3fXnOpenReview ↗
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2
Confidence
2
Informativeness
2
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Soundness
2
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Paper summary

The paper asks if tabular foundation models use context labels only as values combined with fixed weights, like in linear regression or kernel smoothing. Or does one label change how much the others matter? The authors point out a trap. The packages standardize labels first, so plain second derivatives can look nonlinear even when every real prediction is fixed-weight. They propose two tests that only use predictions at standardized labels. One rules out fixed weights, the other also rules out per-label transforms. Across five public models and four regression datasets, both tests come out nonzero. The effect is much weaker in random copies, and most of the measured interaction goes through the attention scores.

Critical strengths
  1. The paper identifies a real and easily overlooked pitfall: because TFM packages standardize labels onto a sphere M\mathcal{M}, naive Hessian and permutation tests report label adaptation even for maps that apply fixed weights on every admissible input.
  2. Claims are carefully scoped and backed by meaningful controls. Random copies and an entropy-matched control tie the interaction to training, and the authors state explicitly that the stop-gradient identifies derivative paths rather than necessity, and that the default ensemble is only shown to be non-affine.
Critical weaknesses
  1. The evidence is local and its practical size is unclear. The certificates are pointwise second-order quantities at the observed labels, and Xˉsep\bar X_{\text{sep}} is a share of curvature, not of prediction change.
  2. The scope is narrow relative to the framing. Only regression is evaluated, the certificates apply to a single internal estimator rather than the deployed ensemble, and several analyses omit TabFM.
  3. Since the related work already notes that label-driven task inference changes every label’s weight and that the measurements agree with this picture, joint processing is arguably expected, and the novelty rests mainly on the methodology.
Questions for authors
  1. Can XsepX_{\text{sep}}, or a four-point test calibrated against a separable null, be applied to the packages’ default ensemble predictions?
  2. How were the four queries per context selected, and do the certificates stay stable at label vectors other than the observed ones and with more contexts?
4 comments

[1/2] Thank you for the review. Its first weakness led us to the main addition of the revision.

Weakness 1: The evidence is local and its practical size is unclear. The certificates are pointwise second-order quantities at the observed labels, and Xˉsep\bar X_{\mathrm{sep}} is a share of curvature, not of prediction change.

Response: We agree with both points. In the revision, we give the certificates a practical size and we test it at finite label changes (Appendix C.10).

The certificates are second derivatives of the prediction, so they say how fast the sensitivities change with the labels. The sensitivity to a label is the weight of that example in the prediction. We make this reading exact in Proposition 1: the ratio Xsep/∥PTa∥X_{\mathrm{sep}}/\lVert P_T a\rVert gives the relative change of the sensitivities of a group of rows when the labels of the other rows change.

We tested this prediction on 29 tables with finite label changes. When the labels of half of the rows move by 3% of a standard deviation, the measured change of the sensitivities of the other half is 0.94 to 1.08 times the predicted one on average, with no fitted constant (Table 18). At 10% the first-order prediction overestimates the change, with a ratio of 0.64 to 0.94, and the change remains large: 29% to 65%. The certificates therefore give the size of the change for label changes of a few percent, and its order of magnitude at 10%.

In a second test, we change the labels of two random groups of rows, separately and together. For a model that treats labels one at a time, the two effects add up (Section 4.4 and Appendix C.7). We measured the departure from this sum. It certifies that every such model misses the predictions of the tested model by at least 0.9% to 2.2% of its root mean squared error in the typical case, for label changes as large as that error. With the forward intervention we measure accuracy directly: the error is 2.1 times higher in median when the attention weights no longer follow the labels (Table 16). In this intervention we act on the attention weights and not on the certificate itself.

Weakness 2: The scope is narrow relative to the framing. Only regression is evaluated, the certificates apply to a single internal estimator rather than the deployed ensemble, and several analyses omit TabFM.

Response: We agree with the three points. We now state the scope for the first, and we added experiments for the other two.

  • Regression: The certificates are derivatives with respect to the labels. A class label is discrete, so such a derivative depends on how one extends the predictor between classes. Classification therefore needs a discrete version of the test, which we do not provide. We now state in the abstract that the results concern regression.
  • Single estimator: The certificates need derivatives, which are well defined for a single estimator and not for a complete package that refits its preprocessing. For the deployed ensembles, we added a test that needs no derivative. With it we find the interaction in the default predictions of all five packages (Table 14, see Question 1).
  • TabFM: We added it to the attention replacement, the other label vectors, the test on default predictions and the 29-table study (Tables 3 and 12 to 17). Some earlier controls still cover four models, and we disclose which ones in Appendix B.2.

[2/2]

Weakness 3: Since the related work already notes that label-driven task inference changes every label’s weight and that the measurements agree with this picture, joint processing is arguably expected, and the novelty rests mainly on the methodology.

Response: We agree that joint processing is expected and that the novelty lies in the methodology. Our contributions here are the two tests: the first detects non-affinity, which is a departure from fixed weights, and the second detects joint label processing. We identified the standardization trap, in which the tests in use report label adaptation even for a model with fixed weights, and we fixed it. We believe that a rigorous and solid test is a scientific contribution, even when its findings are expected, because an expectation cannot be verified without such a test.

The measurements also add three things that an expectation does not give.

  • The amount of joint processing differs between models: Copies of TabICL-v2 and TabDPT with random weights, built with the reset procedure of Appendix C.3, have a joint share below 1% on average, against 40% to 71% for the trained models. Among the trained models, the ratio Xsep/∥PTa∥X_{\mathrm{sep}}/\lVert P_T a\rVert differs more than threefold (Table 17).
  • The certificate measures how stable an explanation by examples is: The certificate predicts by how much the influence of the examples changes when other labels change. An explanation of a prediction by its most influential examples therefore holds only near the observed labels (Appendix C.10).
  • Label-dependent weights can decide the accuracy: We added Appendix C.11 to show an example on synthetic tasks. When a table has many variables and only the labels reveal the few that matter, the five models are far more accurate than the best predictor with fixed weights. A predictor that transforms the labels one at a time does not reach the models either. We keep this example in the appendix because we want the paper to stay centered on the theory.

Question 1: Can XsepX_{\mathrm{sep}}, or a four-point test calibrated against a separable null, be applied to the packages’ default ensemble predictions?

Response: Yes. We ran the four-point test that you describe on the default predictions of the five packages, and we find the interaction in all of them.

In this test, we change the labels of two disjoint groups of rows, separately and together. For every model that treats labels one at a time, the two effects add up, so the contrast between the four predictions is zero. We use separable maps that we construct as the null, and a map with interacting labels as a positive control (Appendix C.7).

The contrast is nonzero and above the numerical noise in 192, 119, 144, 192 and 59 of 192 comparisons for TabICL-v2, TabPFN-3, TabPFN-2.6, TabFM and TabDPT (Table 14). We could not resolve the remaining comparisons numerically, and they do not show an absence of interaction.

These contrasts describe the complete package, with its label preprocessing and its averaging over estimators.

Question 2: How were the four queries per context selected, and do the certificates stay stable at label vectors other than the observed ones and with more contexts?

Response: We draw the queries at random. The detection is stable at other label vectors and with more contexts, and the magnitude changes with the label vector.

  • Queries: We take a seeded random permutation of the rows, which gives the context rows and then the query rows. We select no query with a certificate value (Appendix B.2).
  • Other label vectors: We recompute the certificates at two other label vectors, on two datasets: the observed labels in shuffled order, and labels in which only the residuals of a regression on the features are shuffled. We detect the interaction at 12 of 12 predictions for every model in both cases. The joint share moves by less than 9 points in median for four models. It is less stable for TabDPT, where it falls by 12 points with shuffled residuals and by 40 points with shuffled labels (Table 13).
  • More contexts: We extended the experiment of Table 2 from three to six contexts per dataset and from four to eight datasets, and the conclusions stay the same (Tables 2 and 9). We also computed the certificates on 29 tables with one new context each (Table 17). With longer contexts of 1,024 rows, the joint share is lower than at 256 rows in 15 of 16 settings, by 0.085 on average, and it stays between 0.30 and 0.82 (Appendix C.7).

Thank you for your detailed responses and experiments. I appreciate the authors' efforts to address my concerns, particularly regarding the practical significance and experimental scope. However, I remain concerned about the methodological novelty of the proposed tests and the significance of the findings. While the additional experiments strengthen the paper, my main concerns have not been fully resolved. Therefore, I will maintain my original rating

Thank you for reviewing the additional experiments and acknowledging that they strengthen the paper.

We would appreciate clarification of your remaining concerns about methodological novelty and significance. In your original review, you described the standardization pitfall as "real and easily overlooked". Our methodological contribution addresses this pitfall through the two certificates in Lemmas 1–2.

Could you clarify which aspect of this contribution you consider insufficiently novel? If the concern is overlap with existing work, we would appreciate the relevant references so that we can explain the relationship precisely.

Regarding significance, the added analyses connect the certificates to changes in example sensitivities and examine predictive consequences. Could you clarify which limitations of these results remain decisive in your assessment?

Thank you again for your feedback.

Reviewer_Q1psOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
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Soundness
1
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Paper summary

The paper provides a deep study of the pretrained transformer models to explain if pretrained tabular foundation models use context labels and how they use them. They prove an interpretation of that function, but do not establish if this finding improves prediction which limits the impact of the paper.

The paper first identifies a measurement pitfall: TFM packages standardize labels, so the network is only ever evaluated on a sphere inside the mean-zero subspace, yet ordinary Hessians also describe off-manifold behaviour. It then derives two extension-invariant certificates. Then they provide experiments across 5 public TFMs × 4 regression datasets.

Critical strengths
  1. The standardization trap is a real and non-obvious methodological result, cleanly demonstrated by construction (Eq. 2) and then made numerical in the calibration table.

  2. The two certificates are the right shape for the question: extension-invariance (Lemmas 1–2) is exactly the property that makes the test about predictions rather than about an arbitrary off-manifold continuation, and the three-way taxonomy (fixed-weight / per-label / joint) is a genuine refinement over treating all nonlinearity alike.

Critical weaknesses

The main grid is 4 datasets × 3 contexts × 4 queries with one synthetic dataset, Table 2 reports no dispersion at all, and the random-copy, readout-head, and attention-entropy controls each rest on 2 datasets (2 architectures for the entropy control). A reader cannot tell whether TabDPT's 40.4% vs TabPFN-v2.6's 73.4% is a real model difference.

The conclusion is essentially that large trained transformers are not exactly affine in their inputs. The paper concedes (§5) that it establishes the presence of label interaction but not its necessity. Appendix C.5 is the closest answer and it points the other way: a score-blocked model, where labels cannot influence the attention scores at all, lands within 9% of token injection under contamination, while the label-linear control is 96% worse. So nonlinear use of labels appears to matter, but the specific pathway the paper localises may not. That belongs in the main text, and it weakens the contribution.

Questions for authors

Is there a stronger positive conclusion the certificates support beyond the fixed-weight account fails? If so, please state it explicitly

2 comments

[1/2] Thank you for the review. We answer each point and the soundness score.

Summary: They prove an interpretation of that function, but do not establish if this finding improves prediction which limits the impact of the paper.

Response: In the revision, we now test whether the finding matters for prediction. The accuracy drops when the attention weights of the models no longer follow the labels.

We compute the attention weights of a model from shuffled labels and freeze them. We then run the model again with the original labels and the frozen weights. The weights no longer depend on the labels, and about 95% of the measured interaction disappears in median (Section 4.4, Table 15). The error rises in all 40 settings and is 2.1 times higher in median. When we shuffle only the residuals of a regression of the labels on the features, so that the labels keep their relation to the features, the error is still 12% to 33% higher in median (Table 16).

The predictions of the released models therefore depend on attention weights that follow the labels.

We also added Appendices C.10 and C.11 to show examples of the practical consequences of our findings. We keep them in the appendix because we want the paper to stay centered on the theory.

Weakness 1: The main grid is 4 datasets × 3 contexts × 4 queries with one synthetic dataset, Table 2 reports no dispersion at all, and the random-copy, readout-head, and attention-entropy controls each rest on 2 datasets (2 architectures for the entropy control). A reader cannot tell whether TabDPT's 40.4% vs TabPFN-v2.6's 73.4% is a real model difference.

Response: We agree with each point. We added the missing measurements to the revision, and the pattern of Table 2 holds.

  • Dispersion: In Table 2, we now report the standard deviation of each quantity over the 192 predictions of a model. These values include the differences between datasets, contexts and queries, so they describe the spread and not whether two models differ.
  • Grid: We extended the experiment of Table 2 from four to eight datasets and from three to six contexts, and we updated Table 2. Each model now has 192 predictions, against 48 in the submission. The four new datasets come from the TabArena benchmark, so seven of the eight datasets are real tables. The conclusions stay the same. We also computed the certificates on 29 real public tables with one new context each (Table 17).
  • Controls: We extended the random-copy control to ten tables for two architectures, and the separation holds: the joint share of the random copies is below 1% on average, against 40% to 71% for the trained models (Table 17). We also extended the readout-head control to ten tables and to TabDPT, and we now remove the curvature of the head exactly, with the head replaced by its linearization at the observed labels. The joint share is then 66%, 68% and 43% for TabPFN-3, TabPFN-2.6 and TabDPT, against 55%, 65% and 41% with the head (Appendix C.1). The interaction is therefore present before the head. The entropy control still rests on two datasets.

Weakness 2: The conclusion is essentially that large trained transformers are not exactly affine in their inputs. The paper concedes (§5) that it establishes the presence of label interaction but not its necessity. Appendix C.5 is the closest answer and it points the other way: a score-blocked model, where labels cannot influence the attention scores at all, lands within 9% of token injection under contamination, while the label-linear control is 96% worse. So nonlinear use of labels appears to matter, but the specific pathway the paper localises may not. That belongs in the main text, and it weakens the contribution.

Response: We agree that Appendix C.5 belongs in the main text and that the submission did not establish necessity. We respecfully disagree on one point: the conclusion is stronger than non-affinity.

  • Beyond non-affinity: A model can be nonlinear in every label and still treat labels one at a time, as a sum of terms that each depend on one label. The second certificate is exactly zero for every such model, and it is nonzero for all five models. The finding is therefore that one label changes how the others influence the prediction. Non-affinity alone does not give this property. Copies of TabICL-v2 and TabDPT with random weights, built with the reset procedure of Appendix C.3, are also not affine in the labels, yet when the labels of other rows change, the weights that these copies give to the examples change 50 to 800 times less than in the trained models (Appendix C.10).

[2/2]

  • Appendix C.5: We now discuss it in Section 4.4. In C.5 we show that attention scores are not the only route to joint processing. On a task with contaminated labels, a small model whose attention scores cannot depend on the labels is only 5% to 20% worse than the model whose scores depend on them, whereas a model that is linear in the labels is 91% to 96% worse. The score-blocked model can still process labels jointly, through the nonlinear layers that follow the attention. C.5 limits what we can claim about the attention route. It does not test joint processing itself, because none of its nonlinear models is constrained to treat labels one at a time. In the released models, attention carries 72% to 94% of the measured interaction (Table 2), and replacing it raises the error (Table 16).
  • Necessity: We establish the presence of joint processing and the cost of replacing the attention weights that follow the labels. We also prove necessity in one situation: when a table has many variables and only the labels reveal the few that matter, no predictor with fixed weights reaches the accuracy of the models (Proposition 2, Appendix C.11).

Question: Is there a stronger positive conclusion the certificates support beyond the fixed-weight account fails? If so, please state it explicitly

Response: Yes. The certificates support three positive conclusions, and we discuss them in the revision.

  • The models process their labels jointly: The second certificate excludes more than fixed weights: it excludes every model that treats labels one at a time. In all five models, changing one label changes how the others influence the prediction (Section 4.2).
  • The certificate estimates the size of the joint-processing: We show in Proposition 1 that the ratio Xsep/∥PTa∥X_{\mathrm{sep}}/\lVert P_T a\rVert is a rate. It gives the relative change of the weights of a group of examples when the labels of the other examples change. We call these weights sensitivities in the paper. For the five models, a change of 1% of a standard deviation in the labels of half of the rows changes the weights of the other half by about 3% to 10%. This prediction has no fitted constant, and on 29 tables the change that we measured at an edit of 3% is 0.94 to 1.08 times the predicted one on average (Table 18).
  • We demonstrate that explanations by examples are fragile: When all labels move by 10% of a standard deviation, three to six of the ten most influential examples of a prediction are replaced, while the test error changes by 1% or less in median (Table 18). The explanation of a prediction by its most influential examples is therefore much less stable than the prediction itself. This instability comes with weights that depend on the labels in general: copies with random weights also lose two to four of their ten most influential examples. What is specific to the trained models is the effect of the labels of other rows, which is 50 to 800 times larger than in the copies (Appendix C.10).

Soundness: 1: I have significant concerns about the paper’s soundness that do not appear easy to address.

Response: We hope that the answers above remove the concerns behind this score. The weaknesses listed in the review concern sampling and interpretation, and we address both. For the measurement itself, we rely on four checks.

  • Proofs: We prove that each certificate is zero for every model of the class that it tests (Lemmas 1 and 2).
  • Known answers: On maps that we construct with fixed weights or with one-label-at-a-time transformations, the corresponding certificate reads zero to floating-point precision (Table 4).
  • Numerical validation: We compared the Hessians with finite differences of the gradients of the unmodified models, and they match (Table 7).
  • Prediction of new measurements: We used Hessians computed in the same way to predict the size of the change of the sensitivities after finite label edits on 29 tables, and the measurements agree (Table 18).

If a specific concern remains, we will gladly address it.

Reviewer_MZdhOpenReview ↗
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3
Confidence
2
Informativeness
3
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3
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Paper summary

This paper study how TFM use context label. Previous explanation: labels are just averaged with fixed weights decided by feathers The authors want to know whether this is really true: can one label change the weight of another label.

The experiments cover five public TFMs and four datasets (including a self-built synthetic one). Results: all five models show joint processing, the interaction comes from training (randomly initialized networks show almost none); and blocking the derivative paths from labels to attention scores removes 75–95% of the measured interaction with the predictions unchanged

Critical strengths

The standardization trap is a real issue and the fix (tangent-space projection) is clean this might be useful for the whole direction of derivative-based ICL analysis.

Critical weaknesses

The core conclusion is only existential: all five models have the interaction, but whether it matters for prediction is unknown it could be worth 0.1% of accuracy or be the main source of error, and this paper does not study this.

Questions for authors

Can you add a forward intervention that removes the interaction from the computation (e.g. freezing the attention-score path) and check whether the accuracy drops? This is the most important experiment.

1 comment

Thank you for stating plainly which experiment matters most. We ran it.

Question: Can you add a forward intervention that removes the interaction from the computation (e.g. freezing the attention-score path) and check whether the accuracy drops? This is the most important experiment.

Response: Yes, the accuracy drops when the attention weights no longer follow the labels.

Freezing the attention weights at the observed labels leaves every prediction unchanged, so it cannot test accuracy. We instead compute the attention weights from shuffled labels and freeze them. We then run the model again with the original labels and use the frozen weights in place of the ones that it computes. The weights no longer depend on the labels, and about 95% of the measured interaction disappears in median (Section 4.4, Table 15). The error rises in all 40 settings (five models, eight datasets) and is 2.1 times higher in median (Section 4.4, Tables 3 and 16).

Fully shuffled labels have lost their relation to the features, so the error might rise only because the attention weights come from a meaningless task. We therefore repeat the test with a milder replacement: we fit a regression of the labels on the features and shuffle only its residuals between rows, so that the labels keep their relation to the features. The error still rises by 12% to 33% in median, depending on the model (Table 16).

The predictions therefore depend on attention weights that follow the labels. With fully shuffled labels the models even fall below a simple kernel predictor (Table 12), so the factor of 2.1 shows that the models rely on these weights. The milder replacement is the more informative of the two: there the models stay ahead of that kernel predictor.

Weakness: The core conclusion is only existential: all five models have the interaction, but whether it matters for prediction is unknown it could be worth 0.1% of accuracy or be the main source of error, and this paper does not study this.

Response: We agree that the submission did not study this. We added this study to the revision. The effect is not negligible, and its exact size remains open.

With the forward intervention above, we measured the effect on accuracy. In median, the error rises by 12% to 33% under the milder replacement and is 2.1 times higher with shuffled labels. Both figures can overstate what joint processing contributes, because the later layers receive attention weights that they did not produce.

We did a second test, directly on the predictions. We change the labels of two random groups of rows, first separately and then together. For a model that treats labels one at a time, the effect of the joint change is the sum of the two separate effects (Section 4.4 and Appendix C.7). We measured the departure from this sum. It certifies that every such model misses the predictions of the tested model by at least 0.9% to 2.2% of its root mean squared error in the typical case, for label changes as large as that error.

Joint processing therefore changes the predictions of these models by at least this certified lower bound. The intervention shows in addition that their accuracy depends on attention weights that follow the labels.

We also added Appendix C.11 to show an example in which joint label processing matters for prediction. It is a common situation: a table records many variables, only a few of them drive the target, and only the labels reveal which ones. A predictor with fixed weights cannot use this information, and the five models are far more accurate than the best such predictor. We keep this example in the appendix because we want the paper to stay centered on the theory.

In the revision, we also quantified a consequence that does not depend on accuracy. When the labels of half of the rows change by 10% of a standard deviation, the sensitivities of the prediction to the other rows change by 29% to 65% (Appendix C.10). These sensitivities are the weights that the model gives to the examples.

Your question also led us to correct Appendix C.4: at the observed labels, freezing the attention weights and blocking their derivatives give the same prediction, gradient and Hessian. The attention drop of Table 2 is therefore the part of the interaction that disappears when the attention weights are frozen. Thank you for that.

Comments on the paper

3 comments
AuthorsOpenReview ↗

General response

Dear Reviewers and Area Chair,

Thank you for your time and the constructive reviews.

The main contribution of the paper is a pair of certificates for testing how a model uses its context labels. The first detects departures from fixed-weight averaging. The second detects joint label processing that no sum of independent per-label transformations can explain. Both certificates come with proofs (Lemmas 1 and 2). Their validity does not depend on a particular architecture, so they apply beyond the five models studied here. We appreciate that you recognize this solidity: the fix is "clean" (MZdh), the certificates are "the right shape for the question" (Q1ps), and the claims are "carefully scoped and backed by meaningful controls" (3fXn).

Joint label processing may be expected from the architecture or from task inference. However, that expectation does not certify it in a particular trained model, and the standardization trap shows that the available tests report label adaptation even for a model with fixed weights. Our certificates separate genuine interaction from this artifact.

Our objective is to improve the understanding of how tabular foundation models work. The paper belongs to the same category as work such as "Transformers Learn In-Context by Gradient Descent" (arxiv:2212.07677), which investigates the computations behind in-context learning and whose value lies in the understanding that it provides. This position is in line with the ICLR reviewer guide, which asks whether a submission contributes new knowledge and notes that this does not necessarily require state-of-the-art results.

We also agree that practical magnitude, coverage and predictive consequences matter. We therefore added to the revised paper a forward intervention with accuracy measurements (Section 4.4 and Appendix C.8), a larger main experiment with standard deviations (Table 2), a replication on 29 tables (Appendix C.9), and tests of the default ensemble predictions (Table 14). We also added Appendices C.10 and C.11 to show examples of practical consequences of our findings. With these additions we strengthen the empirical assessment.

Area_Chair_n3r1OpenReview ↗

Prompting for Discussion

Hi Reviewers,

The authors have responded to your reviews. Can you please discuss with them? Has your opinion changed at all?

Regards, AC

Dear Area Chair and Reviewers,

First, we would like to thank the Area Chair for their efforts to encourage further discussion, and the reviewers for their time and constructive feedback.

As the discussion period approaches its end, we would like to kindly follow up on our rebuttals and the revised manuscript.

We have made substantial additions to address the main concerns raised in the reviews, including new experiments on the predictive consequences of joint label processing, expanded evaluations, and additional theoretical and empirical results.

We would greatly appreciate hearing whether these additions have addressed your concerns. If so, we would be grateful if you could consider updating your assessments and scores accordingly.

Of course, if any concerns remain, we would be happy to discuss them further before the deadline.

Thank you again for your time and consideration.

Best regards,
The Authors

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