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Under review as a conference paper at ICLR 2027

Normalization as Control: Batch Normalization Is the Deadbeat Corner of a Kalman-Tuned Normalizer Family

Abstract

Batch normalization (BN) remains the standard normalizer in convolutional networks, and many variants replace its per‑batch statistics with running estimates. Yet it is unclear where BN sits among such tracking normalizers, what should set a tracker’s rate, and why principled trackers end up no better than BN. We answer in three steps. First, BN solves a small convex problem exactly on every batch; tracking that solution instead yields a family of normalizers that contains BN as its one‑step, or deadbeat, member. Second, a Kalman‑filter view sets the tracker’s gain from the noise it assumes, and we prove that, once the mean is tracked, the tracker stays at a distance from BN that grows with that assumed noise: the noise model decides how far a tracker may leave BN. Third, experiments on ResNet‑20 test this prediction. The standard noise model treats every activation as an independent sample, but the true independent units are the images, so it understates the noise 17‑ to 31‑fold. The tracker then collapses onto BN and even finishes training below it, because its stored inference state is as noisy as a single batch; a one‑pass recalibration removes the deficit. Changing only the noise model moves the same tracker away from BN in the predicted order, adding 6–11 points over plain test‑batch statistics on corrupted data at batches of 8 or fewer.

Primary area:
optimization
Keywords:
normalization, batch normalization, test-time adaptation, Kalman filtering, convergence analysis, training dynamics

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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_2as7OpenReview ↗
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Paper summary

The paper studies a family of normalization methods that track statistics across batches, with BN’s training behavior recovered at a full-update endpoint. It analyzes how the assumed observation noise controls the tracker’s distance from BN and explains why underestimating this noise makes the tracker behave almost like BN. Experiments on ResNet-20 with CIFAR datasets test these predictions through noise measurements, changes to the noise estimate, and recalibration of inference statistics.

Critical strengths
  1. The paper gives a useful explanation of why a seemingly more principled tracker can end up behaving like BN. The bounds and gain analysis turn this explanation into predictions that can be checked. I find this valuable even without a clear accuracy improvement over BN.

  2. The experiments go beyond reporting accuracy. They measure the noise and change the noise model while keeping the update rule fixed. This provides meaningful support for the proposed explanation.

Critical weaknesses
  1. The evidence is relatively limited to ResNet-20 and CIFAR datasets. Several key mechanism tests use only one or two retrained seeds, and the calibrated small-batch results use one seed. This makes it hard to judge how broadly the findings hold.

  2. The experiments compare mainly with BN, GN, and LN, rather than other methods that track statistics across batches. Direct comparisons with methods such as Momentum BN or Online Normalization would help establish what the proposed analysis adds to existing work.

Questions for authors
  1. How much of the noise-misspecification explanation applies to existing tracking normalizers, rather than only to the proposed gain rule?

  2. Are results available for the key noise-calibration and recalibration tests across more seeds or on a larger network? Such evidence could materially strengthen my assessment.

2 comments

Thank you for stating exactly what would strengthen your assessment. We aimed our new runs at it.

Q2 and W1: more seeds. Every key test now has 5 seeds. The 60 training runs are new, on a new machine, and reproduce Table 1 within seed variation.

  • Noise calibration.
    • Frozen-state noise is 17 to 30 times r_n in all 30 models: CIFAR-10 and CIFAR-100 × BN, GFN-2 and GFN-2c × 5 seeds.
    • Eq. (7) matches it to within 4% at B = 32 and 128.
    • On corrupted streams at B = 2/4/8, measured directly, Eq. (7) recovers 77/86/90%.
  • The noise model in training. Changing only the noise model removes GFN-2's deficit:
    • CIFAR-100: GFN-2c − BN = −0.27 [−0.91, +0.37]; GFN-2c − GFN-2 = +0.84 [+0.05, +1.62], 5/5 seeds.
    • CIFAR-10: GFN-2c − BN = −0.19 [−0.57, +0.19].
  • The inference-state mechanism. GFN-2's test accuracy fluctuates 3.1 to 4.1× more than BN's over the last 20 epochs. GFN-2c's is at BN's level (0.98 to 1.09×).
  • Small-batch test time. Image-level gain over the deadbeat corner at B = 8/4/2: +5.50, +8.12 and +10.69 points, with CIs [+5.39, +5.60], [+7.93, +8.30] and [+10.39, +10.98]; 5/5 seeds positive.
  • Recalibration: one deviation, stated openly. Our five-seed recalibration pass ran without the training augmentation.
    • That lowers every model, BN included, by 1.8 to 6.1 points, because the weights co-adapt to augmented statistics (App. E.3). It therefore does not test the claim.
    • Under it, GFN-2 − BN goes from −1.11 to −0.06 [−1.13, +1.01] on CIFAR-100, and from −0.59 to −0.47 [−1.30, +0.36] on CIFAR-10. This is too noisy to count either way.
    • The GFN-2c result above tests the same mechanism from the training side. The augmented pass will be in the revision.

Larger network. The ResNet-18 runs did not finish in the discussion window on our shared GPU. We commit to them for the camera-ready version.

What the present data say about scale: the noise excess grows with the feature map. At B = 2 on corrupted streams, true noise / r_n is:

Feature maptrue noise / r_n
32×3254 to 263
16×1611 to 19
8×84.5 to 27

At every resolution this corresponds to 2 to 24 effectively independent values per image. We therefore expect a network with larger feature maps to be further from the per-position model.

Q1: how much applies to existing tracking normalizers?

  1. The noise excess is a property of the activations, measured in BN networks too.
    • A rule that counts B·H·W positions understates the noise by this factor.
    • A rule that counts each image as one sample overstates it by the 2 to 24 values per image.
    • Eq. (7) measures it.
  2. The stored state. Any tracker that applies its training state at inference stores an average whose noise is set by its rate. The 3 to 4× fluctuation above is that effect.
  3. The gain law. Prop. 9 applies to any innovation-based rule α = 1 − r/S. For hand-set rates, the right rate depends on the true noise.
  4. The update rule matters little. At equal rate, our log-scale update and a plain mean/variance EMA differ by at most 0.11 points at any batch size. The rate moves accuracy by up to 21 points.

W2: Momentum BN and Online Normalization. We could not retrain both in the discussion window. We ran the comparison that isolates the ingredient they share with us, a running average of the statistics, on the same five checkpoints and streams, with momentum chosen on held-out corruptions. On stationary streams it matches the best fixed gain, and with the correct noise our gain reaches the same accuracy without a validation set. Both methods will be retrained for the camera-ready version, and Table 13 will compare them mechanism by mechanism.

We hope this five-seed evidence strengthens your assessment, and thank you again.

Thank for the detailed explainations. My concerns have mostly be addressed.

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Paper summary

This paper interprets batch normalization as the exact solution of a per-batch centering and log-scale objective and embeds it in a family of stateful normalization rules. An update-then-output corner recovers BN's training-mode forward and backward computations. The proposed GFN-2 normalizer uses a Kalman-inspired gain that compares innovation power with assumed observation noise. The main theoretical results bound proximity to the BN solution and predict a mean-field steady-state gain under noise misspecification. Experiments on Res-20 investigate underestimated observation noise, noisy inference states, recalibration, and small-batch test-time normalization.

Critical strengths
  • This paper structure is coherent. The paper does more than introducing another normalizer and compare accuracy. Instead, it measures frozen-state noise, recalibrated inference state, which help explain why the proposed tracker behaves similarly to BN.
  • The BN corner identity and the basic log-domain recursion are straightforward. Theorem 8 provides a clean property of the proposed gain law under its stated conditions. The distinction between the motivating Kalman model and the implemented rule is also explicitly acknoledged.
  • The manuscript keeps transparent about reporting its limitations and negative results, which is appreciated. The authors report the CIFAR-100 deficit, the stronger performance of fixed smoothing in some settings, and GN's advantage at the smallest batches.
Critical weaknesses
  • The contribution needs sharper positioning relative to existing stateful normalizers. There have been numerous precedents that share several major components with the current framework. For example, Batch Renormalization already combines running-statistics forward normalization; Streaming Normalization explicitly address temporal statistics and approximate backward estimation; MABN emphasizes that backward statistics instead of forward moments matter for small-batch stability; MECTA includes a data-dependent forgetting gate for updating running statistics, making it a closer related work than a fixed EMA alone. The paper corrected cited many of these works, yet insufficient differentiation and experimental comparison are lacking. The potential novelty apprears to lie primarily in the particular log-scale noise gain law, its proximity bound, and the empirical diagnosis of noise misspecification, which however does not establish a broader conclusion that the noise model generally matters more than the update rule across normalization methods.
  • The image-level noise estimator is validated on frozen network activations at B=32 and 128. The remaining underestimation invoked to explain the B=2/4/8 results is quantified primarily using synthetic images instead of actual small-batch corruption streams.
  • The backward approximation is insufficiently evaluated in the regime where the method departs from BN. Appendix A.8 derives the exact fixed-gain derivative and acknowledges that the proposed surrogate can differ substantially for particular upstream directions. However, the small test compares the projection-based surrogate with a stop-gradient diagonal; it does not compare the surrogate with the exact fixed-gain derivative under full-training conditions. Moreover, ignoring the current batch's effect on the gain is also an underlying approximation.
Questions for authors
  • What is the actual observation noise and the bias of Eq. 7 at B=2/4/8? Does an independently calibrated reference noise estimate produce the predicted changes in gain and performance?
  • Is it possible to compare the proposed surrogate, the exact fixed-gain derivative in A.8, and the stop-gradient diagonal under matched full-training conditions?
  • How frequently does the history condition in Theorem 8(c) hold during actual runs?
2 comments

Thank you for the precise questions. Each is answered with a new measurement.

Q1: actual noise and bias of Eq. (7) at B = 2/4/8; does an independent reference give the predicted changes? We used five trained GFN-2 models on CIFAR-10-C (5 corruptions × 2 severities).

  • Measurement. On the first half of each cell we froze all states, drew 400 batches per B, and measured the variance of each layer's batch log-scale. We repeated this after 0, 10 and 100 adaptation steps.
  • Reference arm. We ran the gain rule with that measured noise as r and evaluated on the untouched second half.

Medians over seeds, cells and layers:

B24832128
true noise / r_n14.114.915.015.815.3
Eq. (7) / true noise0.770.860.900.971.02
settled gain, reference noise0.050.050.050.050.17
accuracy (%): reference / image-level / analytic / deadbeat76.9 / 66.9 / 57.8 / 56.178.4 / 74.2 / 66.8 / 66.179.0 / 77.7 / 72.6 / 72.279.3 / 79.3 / 77.7 / 77.679.4 / 79.4 / 79.2 / 79.1
best fixed gain (%)77.478.579.079.379.4
  • Bias of Eq. (7). On real activations it is far less biased than our synthetic check suggested (0.36 to 0.46 at B = 2). It still falls short as B shrinks.
  • Reference noise. The gain settles at its floor, as Prop. 9 predicts for a correct noise model. Accuracy follows the assumed noise in the predicted order at every B ≤ 8, and reaches the best fixed gain without tuning.
  • Preregistration. Two predictions passed (bias falls with B; accuracy order). One failed: we predicted a median gain error of at most 0.05 for every rule.
    • The analytic rule meets it (0.04).
    • The image-level rule does not (0.16).

The failure is informative. At B = 2 the shortfall of Eq. (7) sits in the stem and the last layer, where the rule assumes only 45% and 23% of the true noise. There Prop. 9 predicts gains of 0.71 and 0.87, and the recorded gains are 0.71 and 0.84. In the middle layers the rule sits at its floor, although Eq. (7) still misses 25 to 40% of the frozen-state noise. Adapting upstream layers renormalize each batch and lower the noise those layers see (App. E.2), so the mean-field prediction (0.4 to 0.6) is too high there.

At B = 128 each half-cell gives only 40 updates, so the start-up transient is still visible in the settled gain (0.17).

Q2: surrogate vs. exact fixed-gain derivative vs. diagonal, matched full training. Done on CIFAR-100, 3 seeds (tables in our reply to nC8W, Part 1).

  • GFN-2: exact minus surrogate −0.15 points; gradient cosine 0.999.
  • GFN-2c: the exact derivative is 12.1 points worse, and the diagonal 31.8 points worse. At low gain the exact derivative removes only a fraction α of what BN's backward removes. Training accuracy stalls at 60% and the tracked means drift to |μ| ≈ 240, against 3.0 with the surrogate.
  • Your point about the batch moving the gain: differentiating the gain path changes the gradient by at most 3% (cosine 1.000) and accuracy by less than 0.7 points.

Q3: how often does the history condition of Thm. 8(c) hold? We logged it at every step.

  • Training, GFN-2: 100% of steps, in every layer, in all 10 runs (1,485,800 layer-steps per run).
  • Training, GFN-2c: 85% (CIFAR-10) and 88% (CIFAR-100) overall, and at least 72% in every layer.
  • Test-time streams, analytic rule: at least 98.8% on average at every B.
  • Rules with a calibrated noise sit at the floor, where the condition must fail often, because a gain at the floor hides a negative unclipped value.
  • Part (b), the cap √(r/β), needs no such condition; (c) only tightens its constant.

(continued next)

We agree with your reading: the new part is the log-scale gain law, its proximity bound and the noise diagnosis. We will make that boundary explicit in a contribution list. We also accept that our experiments do not show "the noise model matters more than the update rule" for all normalizers, and we will narrow that sentence to trackers whose rate is set from a noise model.

Within that scope, the new runs give direct evidence on both halves of the sentence.

The update rule matters little. On the same five checkpoints and streams we compared our log-scale update with a plain EMA of mean and variance at the same rate. Accuracy (%) at B = 2:

ratelog-scale updateplain mean/variance EMA
0.0577.1877.07
0.175.2975.18
0.368.8568.76

Over all rates and all B, the two differ by at most 0.11 points.

The rate, hence the noise, matters a great deal. At B = 2, going from rate 1 to 0.05 moves accuracy from 56.0% to 77.2%. A correct noise model finds that rate without tuning (Part 1).

Two parts of the diagnosis reach beyond our rule.

  • The noise excess is a property of the activations. It appears in all 30 new models, BN included: BN's ratio to r_n is 17.4 and 19.0 on CIFAR-10, and 24.8 and 28.9 on CIFAR-100, at B = 32 and 128.
  • The stored-state effect applies to any tracker that uses its training state at inference. GFN-2's test accuracy fluctuates 3 to 4× more than BN's late in training. A lower gain removes this.

Mechanism by mechanism. These rows will be added to Table 13:

  • Batch Renormalization solves on each batch and corrects toward fixed-momentum running averages, with gradients through the batch statistics.
  • Streaming Normalization tracks running estimates with an approximate backward.
  • MABN. As you note, it locates small-batch instability in the batch statistics of the backward pass. Our ablation supports that emphasis from another side: removing the backward projection costs about 30 points, and keeping only a fraction α of it costs 12.
  • MECTA. Its forget gate is β = 1 − exp(−D), where D is a symmetric KL divergence between the running and the batch statistics. The gate contains no noise level, so on a stationary stream sampling noise alone keeps D, and with it the rate, above zero. Our gate subtracts an explicit noise level from the same kind of discrepancy. That is the term our measurements show to be decisive, and it is what makes the settled gain predictable (Prop. 9).

We did not retrain these methods in the discussion window. The plain-EMA comparison isolates the ingredient they share.

We hope these answers address your concerns, and that you will consider updating your assessment.

Reviewer_nC8WOpenReview ↗
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Paper summary

This paper presents a control theory perspective on Batch Normalization (BN) and proposes a family of normalization methods that track batch statistics through adaptive updates. The authors first formulate BN as the exact solution of a convex optimization problem and show that standard BN corresponds to a special case of the proposed family with a one step update. They then connect the update rule to Kalman filtering and derive theoretical results describing convergence, gain selection, and the distance between the proposed tracker and standard BN.

Based on this framework, the paper introduces GFN 2, which estimates normalization statistics using an adaptive gain determined by an assumed observation noise model. The authors also propose GFN 2c, which estimates observation noise at the image level to account for correlations among spatial activations.

Critical strengths

The paper provides an interesting theoretical interpretation of Batch Normalization. In Sections 2 and 3, the authors formulate normalization as an optimization problem and show that standard BN can be recovered as a special case of their tracking framework. This offers a useful perspective for understanding the relationship between BN and normalization methods that maintain statistics across batches.

The paper attempts to connect theoretical predictions with empirical observations. In Sections 4 and 6.2, the authors analyze how the assumed observation noise affects the adaptive gain and investigate why the original noise model produces gains close to standard BN. The image level noise analysis and the recalibration experiments provide useful insights into the behavior of normalization statistics. These findings have value even though the proposed method does not consistently improve classification performance.

Critical weaknesses

In Section 6.1, Table 1 shows that GFN 2 achieves 91.87% accuracy on CIFAR 10 and 66.48% on CIFAR 100, compared with 92.09% and 67.39% for standard BN. The difference on CIFAR 100 is statistically significant according to the reported confidence interval. This raises a fundamental concern about the practical value of the proposed method, since it introduces additional state tracking and gain estimation without improving standard classification performance. Although Section 6.2 shows that recalibration can reduce this gap, the calibrated method does not consistently outperform BN either.

In Section 5, the authors state that "the backward pass reuses BN's gradient formula at the controller's state," while acknowledging that this is only a surrogate when the gain is below one. This is a serious methodological limitation because the backward pass does not fully represent the actual forward computation of GFN 2. The authors further acknowledge that the approximation becomes less accurate at low gains, precisely where the calibrated method operates. Section 3 also reports that 13 of 36 fixed gain settings diverge. These observations raise concerns about the correctness and stability of the training procedure.

Questions for authors

In Section 6.1 and Table 1, GFN 2 performs worse than standard BN, while Table 2 shows that recalibration only reduces the performance gap. What evidence demonstrates that the proposed adaptive gain provides a meaningful advantage over conventional running statistics or existing normalization methods with memory?

In Section 5, the proposed method uses the BN backward formula as a surrogate gradient. Could the authors provide experiments comparing this approximation with exact gradients across different gain values? In particular, does the surrogate affect training stability or final accuracy when the gain approaches its minimum value?

2 comments

Thank you for pressing on the backward pass. We ran the experiment you asked for in Q2. Its outcome changes how the backward pass should be read.

Short answer. The BN-formula backward does not hurt training. Where the gain is near one, the exact derivative makes no difference. Where the gain is low, the exact derivative trains much worse.

Q2: surrogate vs. exact gradients, in full training. ResNet-20 on CIFAR-100, the paper's recipe, 3 seeds, four backward rules on the same forward pass. Final-epoch accuracy (%), mean ± s.d.:

surrogate (paper)exact, gain fixed (App. A.8)exact, incl. gain pathstop-gradient diagonal
GFN-2 (final gains 0.76 to 1)66.94 ± 0.4266.79 ± 0.6966.38 ± 0.1737.32 ± 1.59
GFN-2c (final gains 0.05 to 0.24)67.54 ± 0.1855.45 ± 0.6256.11 ± 0.7135.73 ± 0.97
  • GFN-2. Exact minus surrogate is −0.15 [−2.86, +2.55]. The two gradients have cosine similarity 0.999 at all five recorded epochs.
  • GFN-2c. Exact minus surrogate is −12.09 [−13.42, −10.76], in 3/3 seeds.

Why the exact derivative is worse. App. A.8 shows that the exact derivative of a tracker with gain α removes only a fraction α of the gradient along the two directions the normalization fixes (the constant and ẑ). BN's backward removes them fully. Accuracy is ordered by that fraction:

Backward ruleShare of the fixed directions removedGFN-2c accuracy (%)
Diagonalnone35.7
Exact derivative at low gainabout α55.5
BN-formula surrogateall67.5

The failure is one of optimization, not generalization:

  • With the exact derivative, GFN-2c reaches only 59.9% training accuracy, against 91.8% with the surrogate.
  • Its tracked means drift. The largest |μ| is 234 to 248, against 3.0 with the surrogate and above 1,200 with the diagonal.

Without the full projection, updates keep pushing pre-activations along directions that the normalizer later cancels.

This agrees with Xu et al. (NeurIPS 2019), who found for layer normalization that the derivatives of the mean and variance matter more than the forward normalization. We will cite it. The surrogate is BN's own backward applied at the tracker's state, and the ablation supports that design choice.

"13 of 36 fixed gain settings diverge." We reran fixed gains α = α_μ on CIFAR-10, with and without a 5-epoch warm-up from α = 1:

Fixed αsurrogate, coldsurrogate, warm-upexact, coldexact, warm-up
0.05diverged at epoch 1diverged at epoch 4773.3%83.0%
0.1diverged at epoch 1diverged at epoch 11477.9%86.4%
0.3diverged at epoch 128diverged at epoch 12490.9%91.0%

The divergences in Fig. 5 need two things together: the BN-formula backward and a fixed slow gain. The exact derivative removes the divergence but trains poorly, with the same drift (|μ| up to 320 at α = 0.05). The adaptive gain avoids both:

  • None of the 38 adaptive-gain runs in this response diverged, under any backward rule or noise model.
  • None of the 16 adaptive-gain runs in the paper diverged.

This is what Thm. 8 leads one to expect. The adaptive gain caps how far the state may leave BN's batch solution, for any input; a fixed gain has no such cap. The history condition of Thm. 8(c) held at 100% of training steps for GFN-2.

Sec. 5 and App. A.8 will be rewritten around these results. (continued below)

Q1. At the standard batch size the adaptive gain does not beat BN in accuracy, and we do not claim it does. What the evidence shows is that the noise model, the one input the gain law takes, decides how the tracker behaves. Three five-seed results follow.

1. In training, the right noise model removes GFN-2's deficit. Final-epoch accuracy (%), 5 seeds:

CIFAR-10CIFAR-100
BN92.22 ± 0.0767.77 ± 0.38
GFN-2 (analytic noise)91.63 ± 0.2966.67 ± 0.48
GFN-2c (image-level noise)92.03 ± 0.2467.51 ± 0.39
  • GFN-2c vs BN: −0.19 [−0.57, +0.19] on CIFAR-10 and −0.27 [−0.91, +0.37] on CIFAR-100. Both intervals include zero.
  • GFN-2c vs GFN-2 on CIFAR-100: +0.84 [+0.05, +1.62], positive in 5/5 seeds.

The mechanism is the one the paper names: the stored inference state. Over the last 20 epochs GFN-2's test accuracy fluctuates 4.1× (CIFAR-10) and 3.1× (CIFAR-100) more than BN's. GFN-2c's fluctuates 0.98× and 1.09× as much as BN's.

2. At test time, the gain moves as the noise model predicts. CIFAR-10-C, 5 corruptions × 2 severities, 5 seeds. Image-level gain minus deadbeat corner:

Bdifference (pp)95% CI
8+5.50[+5.39, +5.60]
4+8.12[+7.93, +8.30]
2+10.69[+10.39, +10.98]

All 5 seeds are positive at each B.

3. Against conventional running statistics. We ran a plain EMA of the batch mean and variance (the update behind BN's running averages), with momentum chosen on three held-out corruptions.

On these stationary streams the validated EMA is as good as the best fixed gain, and better than the image-level rule at small batches:

BBN + validated EMA (%)image-level rule (%)
879.0077.43
478.4773.88
277.3466.72

Two facts put this in context:

  • The update rule is not what matters. At equal rate, the log-scale update and the plain EMA differ by at most 0.11 points at any B. Changing the rate moves accuracy by up to 21 points.
  • The right rate follows from the noise. Given an independently measured noise, the same gain rule settles at its floor and matches the best fixed gain at every B without a validation set: within 0.1 points at B ≥ 4 and 0.5 at B = 2. The validated EMA momentum has to change with B, from 0.3 at B = 128 to 0.05 at B ≤ 8.

For stationary streams we claim no more than this.

What a reader takes away.

  • BN's exact place among trackers: the one-step corner, reproduced to float64 precision.
  • A law tying a tracker's distance from BN to its assumed noise.
  • The measurement that convolutional activations carry 17 to 30 times more batch noise than per-position counting assumes, in BN networks too.
  • New in this response: what a tracker must keep from BN is its gradient projection.

Cost. Two values per channel and one scalar per layer, BN's two reductions, and 1.02× BN's compiled training time (Table 9).

We hope the backward ablation and the five-seed evidence resolve your concerns about correctness and value, and that you will consider updating your assessment. We are glad to answer further questions.

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

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