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Under review as a conference paper at ICLR 2027

POST-SELECTION CERTIFICATION OF GRADIENT CORESETS

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Abstract

Gradient sketches make coreset optimization tractable; valid post-selection certificates require accounting for how the residual was chosen. We give an exact characterization for Gaussian sketches. For least-squares reweighting over a fixed -dimensional affine family, the selected residual’s sketch-to-exact squared-norm ratio is a scaled product of independent chi-square and beta variables. This law supplies an exact model-specific correction and identifies two distinct thresholds: relative distortion vanishes when , while uncorrected fixed-vector coverage can vanish when . For arbitrary selectors, a fresh Gaussian projection after commitment gives exact conditional intervals with rank-independent audit dimension. We also account for support-search multiplicity, numerical error, and fidelity to the deployed update. Experiments on Qwen2.5-1.5B/0.5B and GSM8K/MBPP tasks complement the theory with constrained real-model diagnostics: at 512 sketch rows, median residual distortion is 3.4% and ranking correlation is 0.95. Reweighting lowers the primary joint-subset exact residual by 23.6%, while increasing sketch optimism in 43 of 45 matched cells. Uniform bounds cover all 27 primary residuals, with six meeting the full-update tolerance. Together, these results distinguish accurate optimization from useful certification and provide calibrated routes to certifying the selected coreset update.

Primary area:
learning theory
Keywords:
gradient coresets, post-selection inference, Gaussian sketching, randomized numerical linear algebra, data selection, certification, large language models

Reviews

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_abyROpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper studies how selecting data subsets and optimizing their weights using a Gaussian gradient sketch affects subsequent certification of the reconstruction residual. For exact least-squares fitting within a fixed affine family, it derives a distributional characterization of the selected residual's sketched-to-exact squared-norm ratio. This yields a distinction between the dimensions needed for accurate estimation and those needed for valid uncorrected confidence bounds: relative distortion can vanish while coverage approaches zero. The paper also presents a model-specific correction and an independent Gaussian audit after committing the selected residual, with extensions for simultaneous claims, numerical error, and repeated decisions. Experiments on Qwen2.5-1.5B/0.5B using GSM8K and MBPP subsets examine residual estimation, reweighting, conservative uniform certificates, and downstream performance. These experiments provide descriptive evidence of sketch optimism, while the independent-audit results are analytical power calculations based on measured residuals.

Critical strengths

The paper clearly distinguishes estimation accuracy from post-selection coverage. The exact affine-family analysis and its two-threshold consequence provide a useful explanation of why an accurate sketch estimate can still yield an unreliable confidence bound. The assumptions and limitations of the different guarantees are stated explicitly.

Critical weaknesses
  1. The main certification mechanisms lack direct empirical validation. The exact correction assumes least-squares fitting within a fixed affine family, whereas the real-model experiments use sketch-selected supports and constrained, regularized, normalized weights. The independent-audit protocol is not run in these experiments; Table 3 reports analytical power calculations from known residual norms. The observed coverage of conservative uniform bounds therefore does not directly validate either principal calibration route. A comparison of realized coverage, bound tightness, and computational cost across the proposed certification approaches is missing.

  2. The practical usefulness of the certificates remains insufficiently demonstrated. Even with a tolerance equal to the full-update norm, only 6 of 27 primary uniform bounds meet the tolerance criterion, coming from behavior-only and random selection; the joint variants do not. Functional diagnostics remain at the numerical precision floor, leaving the empirical fidelity evidence confined to parameter-update space. The study uses only 128 tasks, one rank-8 adapter location, and 64 training steps, with no statistically established downstream advantage. These results leave limited evidence that the certificates support useful decisions in realistic training settings.

  3. Model coverage is limited to small, older models. All real-model experiments use Qwen2.5-0.5B and Qwen2.5-1.5B, from a family released in September 2024. Despite the availability of newer open models such as Qwen3, released in April 2025, the paper provides no evaluation on a newer model family or a substantially larger model. This limits evidence that the observed certificate usefulness and computational trade-offs extend to contemporary language-model training.

Questions for authors
  1. Can you directly evaluate the independent-audit protocol on the constrained selectors, reporting repeated-audit coverage, certification rates, and measured overhead relative to uniform certification and exact residual computation?
  2. What evidence connects the chosen residual tolerance to meaningful training fidelity, beyond the one-step parameter identity and functional measurements at the numerical precision floor?
  3. Why is the evaluation restricted to Qwen2.5-0.5B/1.5B, and do the empirical findings hold on newer and larger models?
3 comments
AuthorsOpenReview ↗

Direct calibration, certification rates, and overhead (Weakness 1/Q1)

Thank you for recognizing the exact affine analysis and its explanation of why accurate estimates can yield unreliable certificates. We agree that the two calibration routes needed experiments matching their respective assumptions.

Weakness 1 and Q1: Can the independent audit be evaluated directly, including coverage, decision rates, tightness, and cost?

Yes. We now commit 45 constrained deployed residuals per model, from nine selectors and five selection projections, before drawing 2,000 fresh shared-projection trials at each of 64, 128, and 256 audit rows. At 128 rows:

ModelAll-45 coverage / 2,000Mean certification rate at half-update tolerance
Qwen2.5-0.5B1,934 (96.70%)88.91%
Qwen2.5-1.5B1,930 (96.50%)89.02%
Qwen3-8B1,935 (96.75%)100.00%

Both columns use simultaneous endpoints with per-residual risk 0.05/45. Coverage counts the joint event per projection; certification averages the 45 residuals' trial rates at tau=0.5 ||g_V||. This is a sensitivity tolerance, separate from the validation-selected policy below. Marginal endpoints have median bound/exact-norm ratios 1.112-1.114. Section 5.3, Table 2, and Figure 2 (page 7), with Appendix K.3 (page 25), report the repeated experiment and its uncertainty.

To address the fixed-affine mismatch separately, we also ran unconstrained, unregularized fits on independently fixed uniform/high-loss gradient families. Corrected coverage is 93.8-97.2% over the 36 original-grid settings, with 1,000 trials each. Under the i.i.d. Gaussian assumption, this is an implementation and calibration check of the exact pivot, not evidence for Rademacher or structured sketches. At k=64, m=512, naive coverage is 1.0-1.2% versus 94.6-94.8% after correction across the three models. Section 5.2 (pages 5-7) and Table 1 (page 6) provide the corresponding implementation evidence for the other principal calibration route.

Uniform and exact cost comparisons. We acknowledge your point that usable decisions must be evaluated alongside cost. The six-of-27 small-pool observation is retained in Appendix L (page 30); the new comparison uses the full training pool. On that pool, full-span uniform certification uses 13,824 rows and accepts 5/9, 5/9, and 7/9 residuals at the same half-update tolerance on selection seed 4501. Uniform projection preparation takes approximately 105, 161, and 403 ms, respectively. These cover a larger residual class than a committed audit.

For 1.5B, sealed/exact sparse queries take 0.310/0.539 ms after preparation. Sealed projection and target preparation cost 1.427 ms plus 0.054 ms map generation, versus 0.452 ms exact target preparation. With the residual already resident, exact is cheaper: 0.026 ms versus 0.090 ms fresh generation/application. Section 5.4 and Table 4 (pages 8-9), with Appendix J.4 (page 21), separate these measured access regimes rather than imply universal acceleration. Our second comment answers Q2 and Q3 on functional usefulness and model breadth.

AuthorsOpenReview ↗

Functional decisions and newer-model evidence (Weaknesses 2-3/Q2-Q3)

Weakness 2 and Q2: What connects the tolerance to meaningful fidelity beyond the numerical floor?

We acknowledge this concern and added actual FP32 full-pool/subset updates, not only the parameter identity. For each model/adapter variant, a common step is selected on all 837 validation tasks using fixed KL/NLL and resolution criteria, then frozen before testing. Repeated identical-update forwards measure the numerical floor. Every cell evaluates full-vocabulary, teacher-forced distributions on all 1,319 GSM8K and 500 MBPP test tasks.

ModelHeld-out cells above floorLargest mean KL (budget 0.01)Residual/logit Spearman range
Qwen2.5-0.5B225/2250.002910.817-1.000
Qwen2.5-1.5B225/2250.002320.767-1.000
Qwen3-8B225/2250.0005210.717-0.983

The repeated-update controls are below the registered 1e-8 logit floor, and all 675 cells exceed the resulting 1e-7 threshold. The held-out KL is KL(full update || subset update), not the validation pilot's KL(base || full update). All 75 nine-method Spearman comparisons exceed the registered 0.65 descriptive criterion. These configuration comparisons share tasks and gradients; KL is a benchmark-balanced mean, not a per-task maximum.

A validation-only policy then chooses tau=0.1 ||g_V|| using mean KL<=0.01 and relative logit RMS<=0.1, where relative error divides subset-versus-full discrepancy by full-update-versus-base discrepancy. It accepts 29/135, 36/135, and 92/135 main-adapter cells, respectively, with zero observed violations among accepted cells. Alpha=0.2 does not satisfy the validation rule. This connects the residual to resolvable output changes and selective decisions. Its scope is measured local additive-update fidelity, not semantic equivalence or preservation throughout AdamW training. Section 5.3 and Table 3 (page 8), Appendix J.3 (page 21), and Appendix K.4 (pages 25-26) give the definitions and results.

Weakness 3 and Q3: Do the findings extend to newer and larger models?

We appreciate the request to go beyond the smaller exact-gradient reference models. Qwen3-8B now participates in the same calibration, functional, tolerance, and cost protocols, including rank-8, rank-16, and four-location adapters. The training workload uses 7,097 examples and 444 steps, with longer horizons reaching 1,331 steps.

For completeness, equal-GSM8K/MBPP macro rewards are:

ModelBaseJointFull-pool matched
Qwen2.5-0.5B20.04%20.04%20.41%
Qwen2.5-1.5B53.83%48.34%48.45%
Qwen3-8B72.10%61.06%61.40%

These comparisons use fixed training seed 4401; task-bootstrap intervals describe that seed, and exact seed sign-flip p-values are 1. Downstream superiority is not established. Retention is benchmark-dependent: Qwen3 main-run HumanEval base/joint scores are 86.59/47.56%, while MMLU subject-macro scores are 73.03/73.34%. Section 5.5 and Table 5 (pages 9-10), with Appendix K.6 (pages 27-29), report these separate outcomes.

The newer model supports transfer of calibration and measured local fidelity, not a universal learning benefit.

Thank you for your time and we hope these additions address all three questions and would be grateful if you would reconsider your assessment.

Thank you for the author's response. In my view, this work still requires further refinement and optimization to meet the acceptance criteria for ICLR; therefore, I maintain my rating.

Reviewer_boy3OpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
1
Soundness
1
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Paper summary

The paper tackles the coreset selection and certification problem. Since the problem setup is not clearly formulated in the paper, it is hard to tell the exact challenge the paper is trying to address.

Based on my knowledge of the literature and my interpretation of the paper, it seems that the problem tackled by the paper is to find a measure tailored to selecting the coreset for training and to certify that this choice is correct after training (in inference).

To do so, the paper invokes heavy mathematical machinery that seems to have been written by an LLM after many iterations with the author. The author mentions in the AI statement that LLMs helped write the paper. However, a significant portion of the details is hidden or abstracted away. After every Theorem, there is a sentence that mentions what this Theorem does or does not without much context. The appendix is heavily cited. The paper consists of a collection of mathematical tools with little explanation onto how they are supposed to solve the problem.

The math seems to be solid, but what is the point of showing solid math without detailing the problem being addressed?

Critical strengths

The paper tackles a timely and very interesting problem. The results may have good potential.

Critical weaknesses

The paper is very hard to read and understand. The results are not positioned within the literature. A few selected papers used to derive the mathematical results are mentioned in the beginning. The related work section comes at the end and lists the related work with one or two sentences on what the paper does, but not much of a connection.

The paper seems to be a summary of a long discussion between the author and LLMs, abstracting away the problem and the intuition behind the need for and interest in the developed tools.

Some concepts, such as the Gaussian channel, coverage, and full-pool weights, appear without explanation or their role in the derived theory.

Questions for authors

Could you please explain the following:

  1. What problems and challenges are tackled by this paper that have not been solved in the literature?

  2. What is the importance of the derived theory in solving this problem?

  3. What is the connection of the Gaussian channel here?

  4. What is the role of the Gaussian sketch?

  5. What is the challenge resulting from the choice of the coreset selection measure and certification measure?

  6. What is the learning setting considered in the paper?

  7. How do the numerical experiments complement the theory?

  8. Is Low rank adaptation (LoRA) being used in the experiments? Does that match the theory?

3 comments
AuthorsOpenReview ↗

Problem, novelty, and Gaussian observations (Q1-Q4)

Thank you for recognizing the problem's timeliness and potential. We acknowledge your presentation concern: the decision and the role of each result needed to be clearer. Our question is: before replacing a full-pool update by a selected coreset update, can we trust the reported upper bound on their discrepancy? Sections 1-2 (pages 1-2) now introduce that decision before the mathematical extensions.

Q1 and the literature-positioning concern: What challenge is not already solved?

We agree that the distinction from prior work should be explicit. Gradient-matching selection and Gaussian sketched-regression inference are established. Bartan and Pilanci (2020) and Epperly and Webber (2026) give exact expected residual formulas for Gaussian sketch-and-solve least squares; Ahfock et al. (2021) and Browne and Andrews (2024) give coefficient and residual-sum laws. Our contribution is the full projected-to-exact residual ratio and its independent chi-square-times-beta factorization, which yields an exact quantile correction and distinct estimation/coverage thresholds. Section 1 (page 1) and Section 6 (page 10) position this target relative to those results and adaptive-sketch analyses.

Q2: Why is the theory useful for this problem?

Your question highlights why accurate optimization diagnostics alone are insufficient. With m=512 and k=16, the expected squared-norm ratio is 0.939, yet an ordinary nominal-95% upper bound covers only 73.7% under the exact law. Theorem 3.1 supplies the missing adjustment; Theorem 3.2 explains why increasing sketch size can resolve estimation error before it resolves miscalibration. Both are on page 3. The gradient-derived comparison in Table 1 (page 6) numerically checks the complete Gaussian fitting and endpoint implementation rather than leaving the correction only as a symbolic calculation.

Q3 and the terminology concern: What is the Gaussian channel?

We appreciate the need to define its role. After committing a residual v, the auditor observes z=Qv. Conditional on the committed state, z has distribution N(0,||v||^2 I/m_a): its coordinate variance is the unknown squared norm divided by the audit dimension. This observation model gives the chi-square interval and tolerance test. Section 4 (pages 3-4) defines it before discussing optimality, which is restricted to procedures observing z.

Q4: What does the Gaussian sketch do?

Your question also calls for separating two uses. The visible P compresses gradients for selection; an independent, unopened Q measures the selected residual after commitment. Gaussianity supplies the explicit probability law, while independence prevents the selection from exploiting the audit. Sections 2 and 4 state which information is visible and when. Here coverage means the probability, over the specified projection randomness, that the upper endpoint contains the target squared norm. Our second comment answers Q5-Q8 in order.

AuthorsOpenReview ↗

Selection, learning setting, experiments, and LoRA (Q5-Q8)

Q5: Why do selection and certification interact?

We appreciate this distinction. In v=Ga-G_Sw, G contains per-example gradients, a specifies the full-pool target, and w contains the deployed subset weights. Selection and certification can concern the same norm. The issue is that optimizing S,w using PG makes v depend on P, so fixed-vector calibration does not automatically apply. Section 2, Equations (1)-(2) (page 2), now states this directly. The paper provides model-specific correction, simultaneous preservation, and independent auditing for their respective information conditions.

Q6: What is the learning setting?

We agree that the learning target must be concrete. We study supervised per-example gradients at a frozen parameter anchor. The loss averages target-token negative log likelihood within each example; full-pool weights are proportional to target-token counts. The subset uses its final deployed sampling weights. Thus Ga and G_Sw are the two expected gradients being compared. Section 2 (page 2) explains this target, and Appendix J.1 (page 20) specifies the training protocol. The local additive-update comparison is separate from the reported multi-step AdamW evaluations.

Q7: How do the numerical experiments complement the theory?

Your concern prompted an explicit separation of experimental roles. The new experiments test both calibration routes and their connection to model outputs:

ExperimentMain observation and location
Gaussian fitting on gradient-derived affine familiesCorrected coverage 93.8-97.2% over the 36 original-grid settings; Section 5.2, pages 5-7
Repeated constrained-selector auditsAll-45 coverage 96.50-96.75% at 128 rows across three models; Table 2, page 7
Actual FP32 additive updates675 held-out cells above the numerical floor; the validation-only policy accepts 157/405 cells with no observed joint-budget violation; Table 3, page 8
Full-test training and retentionSeparate downstream comparisons; Section 5.5, pages 9-10

The affine experiment matches unconstrained fixed-family Gaussian fitting and checks its implementation; the law itself is geometry-invariant for fixed k and m. Capped, regularized, support-selected weights use fresh auditing instead. The 75 descriptive residual/logit Spearman correlations range from 0.717 to 1.000, connecting the residual to measured local output differences rather than treating calibration as a claim of improved final accuracy.

Q8: Is LoRA used, and does it match the theory?

Yes, and thank you for asking us to identify the coordinates. A is fixed and B is trainable; gradients in B coordinates instantiate G. We now evaluate rank 8 at one location, rank 16, and rank 8 at the last four locations. For an additive step, the parameter discrepancy is eta ||v||. Conversion to the underlying weight matrix uses the fixed map B -> (alpha_adapter/r)BA. Section 2 (page 2), Appendix H (page 18), and Appendix J.1 (page 20) state this connection.

Thank you for your time and we hope these answers make the problem, novelty, and experimental purpose clear, and would be grateful if you would reconsider your assessment.

Reviewer_boy3OpenReview ↗

Thanks a lot, I retain my score of 1

Dear Authors,

Thank you very much for the detailed response. Based on your answers, the paper has good potential but requires additional work and resubmission for a full review.

Best regards, Reviewer boy3

Reviewer_Js1BOpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
2
Soundness
3
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Paper summary

The paper studies certification when a gradient coreset is optimized and evaluated using the same random sketch. It derives an exact selected-residual distribution for fixed affine families and shows that accurate estimation can coexist with severe undercoverage. It also develops independent audits for arbitrary selectors, with extensions covering repeated decisions and numerical errors.

Critical strengths

The separation between estimation accuracy and inferential validity is the strongest contribution. The exact distribution and the two different dimensional thresholds make the issue much clearer than a generic warning about adaptive sketch reuse.

I like the explicit treatment of information access. The paper carefully distinguishes same-sketch correction, simultaneous guarantees, and fresh auditing, including what happens when supports, weights, or numerical representations change. This makes the theoretical conclusions precise.

Critical weaknesses

The strongest new theorem concerns fixed-support, unconstrained fitting, while the real-model experiments use selected supports and constrained weights. The paper clearly acknowledges this distinction, but the experiments provide only an indirect connection to the exact distribution and its correction.

Practical usefulness remains less established than validity. Only 6 of the 27 primary uniform certificates meet the chosen tolerance, which is already the full-update norm. Fresh auditing looks more promising, but its evaluation consists of analytic power calculations, leaving its computational advantage and decision value uncertain.

Questions for authors

Could a fixed-support, unconstrained experiment on the real gradient matrices directly demonstrate the predicted undercoverage and the corrected coverage? This would connect the main theorem to the application before introducing the practical weight constraints.

For the constrained selectors, what would a useful fresh audit cost relative to computing the exact residual?

How should a practitioner choose the update-fidelity tolerance?

2 comments
AuthorsOpenReview ↗

Fixed-support validation and audit cost (Q1-Q2)

Thank you for identifying the estimation-inference separation as the strongest contribution. Your questions motivated direct fixed-support experiments and measured comparisons of fresh, uniform, and exact certification.

Q1 and Weakness 1: Does the exact correction work on fixed-support, unconstrained real-gradient fits?

We agree that this experiment is needed to connect the theorem to the application. We fixed uniform and high-loss supports before drawing the Gaussian calibration sketches, then fitted unregularized, unconstrained least squares. For k=64, m=512 on the uniform support, each entry uses 1,000 trials:

ModelNaive coverageDF-only correctionExact affine correction
Qwen2.5-0.5B1.2%38.5%94.8%
Qwen2.5-1.5B1.0%38.7%94.8%
Qwen3-8B1.2%40.2%94.6%

The complete two-support, two-k, three-m grid has 36 settings across the models, with corrected coverage 93.8-97.2%. This isolates why the beta factor matters beyond subtracting fitted degrees of freedom. Because the exact Gaussian pivot is rotation-invariant once k and m are fixed, the gradient-derived families exercise the fitting, rank, stationarity, and endpoint implementation; we do not claim that this correction transfers to non-Gaussian sketches. Section 5.2 (pages 5-7) explains the experiment; Table 1 and Figure 1 (page 6) show the central comparison, and Appendix K.2 (pages 23-24) gives the complete grid and intervals.

Q2 and Weakness 2: What does a useful fresh audit cost relative to the exact residual?

We acknowledge that rank-independent audit dimension alone does not answer the computational question. We therefore measured preparation and queries separately, using the same platform, precision, and data. On the 1.5B model, a sealed 128-coordinate sparse query takes 0.310 ms versus 0.539 ms for its full-coordinate counterpart. Sealed projection plus target preparation costs 1.427 ms, plus 0.054 ms for projection generation; exact target preparation costs 0.452 ms. When the residual itself is already resident, its exact norm is preferable: 0.026 ms versus 0.090 ms for fresh generation plus application. These are seven-measurement medians, not end-to-end timings.

The practical benefit is therefore access-dependent. The 8B extraction/storage experiment retains a 7.29 MB projected-feature table instead of 1.86 GB of full-coordinate FP64 features, with extraction and preparation charged separately. Section 5.4 and Table 4 (pages 8-9), with Appendix J.4 (page 21), make this tradeoff explicit. Our second comment answers your tolerance question and connects these costs to actual update decisions.

AuthorsOpenReview ↗

Choosing a useful tolerance (Q3)

Q3 and Weakness 2: How should a practitioner choose the update-fidelity tolerance?

We appreciate the request for a decision rule, rather than only a valid confidence interval. For a specified parameter-discrepancy budget Delta and additive step size eta>0, choose tau=Delta/eta. Section 2 (page 2) states this identity and the decision workflow: certify the replacement update when its upper norm bound is at most tau; otherwise retain the full update or revise the subset and obtain a fresh audit.

We also added a validation-only policy to connect the parameter tolerance to measured functional fidelity. For each model/adapter variant, we select the step size on all 837 validation tasks using fixed KL/NLL and numerical-resolution criteria. We then choose alpha using mean KL<=0.01 and relative logit RMS<=0.1, and freeze tau=alpha ||g_V|| before held-out assessment. Relative logit RMS divides subset-versus-full logit discrepancy by full-update-versus-base discrepancy.

All three models select alpha=0.1; alpha=0.2 does not satisfy the validation rule. The held-out results are:

ModelAccepted main-adapter cellsAccepted cells outside either budget
Qwen2.5-0.5B29/1350
Qwen2.5-1.5B36/1350
Qwen3-8B92/1350

Each cell evaluates all 1,319 GSM8K and 500 MBPP test tasks. KL is a benchmark-balanced mean. These configuration comparisons share tasks and are not independent datasets. The policy establishes measured local additive-update fidelity under the tested distributions, rather than a universal semantic or multi-step training guarantee.

The functional evaluation requested by another reviewer also strengthens the rationale for this policy: all 675 held-out cells are above the logit numerical floor, and all 75 nine-method residual/logit Spearman correlations exceed the registered 0.65 descriptive criterion. Thus the residual tracks resolvable output differences, and a tolerance selected without test outcomes makes selective held-out decisions.

Section 5.3 and Table 3 (page 8) report the policy and functional results. Appendix J.3 (page 21) defines the metrics and validation rule; Appendix K.4 (pages 25-26) gives the configuration-level results.

Thank you for your time and we hope these direct experiments address your distinction between validity and usefulness, and would be grateful if you would consider updating your assessment.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Exact post-selection inference with direct real-model validation

We thank the reviewers for recognizing the distinction between accurate gradient reconstruction and valid post-selection inference. PSGC makes that distinction quantitative: Theorems 3.1 and 3.2 give the selected-residual chi-square-times-beta law, an exact same-sketch correction, and different dimension requirements for accurate estimation and valid uncorrected coverage. For constrained selectors, the independent audit certifies the committed update without a selector-search complexity penalty.

The additional experiments directly address the shared empirical questions on Qwen2.5-0.5B/1.5B and Qwen3-8B.

Direct calibration. At fixed-support k=64, m=512, naive nominal-95% coverage is only 1.0-1.2% across the three models; the exact correction gives 94.6-94.8%, over 1,000 trials per model. Under the i.i.d. Gaussian assumption, the pivot is geometry-invariant once k and m are fixed, so the gradient-derived families test the complete fitting, rank, stationarity, and endpoint implementation. The separate 48-setting fresh-audit study evaluates constrained deployed selectors. Section 5.2 and Table 1 (pages 5-6), together with Section 5.3 and Table 2 (page 7), report the direct comparisons.

Functional relevance beyond the numerical floor. Actual FP32 additive updates yield measurable logit differences in all 675 held-out cells. The reported held-out KL compares the full-update distribution with the subset-update distribution; the validation pilot separately compares base with the full update. A validation-only policy is the decision-relevant result. Across all 75 nine-method comparisons, descriptive residual/logit-discrepancy Spearman correlations are 0.717-1.000. A validation-only tolerance policy accepts 157 of 405 main-adapter cells with no observed violations of its joint KL and relative-logit budgets. Section 5.3 and Table 3 (page 8) report these results.

These additions connect the exact inference contribution to measured local update fidelity. The reviewer-specific replies explain the decision protocols, measured costs, and separate downstream outcomes. The mathematical statements and proof organization are preserved.

The paper now pairs a precise characterization of post-selection miscalibration with constructive remedies and direct real-model evidence addressing the previously missing connection. We would be grateful for reconsideration in light of these additions.

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

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