acceptodds
Under review as a conference paper at ICLR 2027

Derivative Cheating in Fusion-Based PINNs: Understanding and Preventing

Abstract

Physics-Informed Neural Networks (PINNs) increasingly incorporate inter-point fusion mechanisms such as batch normalization, PointNet, and attention. In this paper, we identify a concealed but dangerous failure mode that arises when PDE residuals are derived via Automatic Differentiation (AD) in models that adopt such fusion mechanisms, in which AD may include fusion-induced paths unrelated to spatial derivatives, making the residual loss deceptively small while the absolute error remains large. We formalize this discrepancy, analyze the semantic distinction between AD-computed residual and true spatial derivatives, and introduce a diagnostic metric, Derivative Cheating Intensity (DCI), to quantify this discrepancy. We further propose a gradient-decoupled residual correction strategy that treats the fusion input as auxiliary context when computing spatial derivatives, rather than including it in the computational graph of AD. Experiments on Poisson, Helmholtz, and Heat benchmarks across BatchNorm, neural operator, PointNet, and Transformer backbones show that the proposed correction eliminates the failure and recovers accurate solutions. Our code is available at [THIS LINK](https://anonymous.4open.science/r/Derivative_Cheating-8CFE/readme.md).

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
Physics-Informed Neural Networks, Automatic Differentiation, Partial Differential Equations

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 4 reviews, above 27% of the others.
Reviewer_7NaEOpenReview ↗
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2
Confidence
4
Informativeness
3
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Paper summary

This paper primarily demonstrates a failure mode caused by inter-point derivatives in fusion-based PINNs, including physics-informed neural operators. Specifically, even when a neural network achieves a small residual error, the resulting solution function may not satisfy the physical laws.

To explain and address this issue, the authors propose treating fusion inputs as fixed context when computing coordinate derivatives, eliminating the corresponding gradient paths through gradient decoupling. They also introduce the Derivative Cheating Intensity (DCI) metric. Extensive experiments across multiple PDEs and fusion architectures demonstrate that an appropriate derivative computation method can prevent models from producing incorrect solutions caused by inter-point interactions.

Critical strengths

The paper identifies a practically meaningful problem. Through computational graph analysis, it reveals a mismatch between residual error and the final derivative fitting in some existing fusion models. Experiments and visualizations demonstrate the practical impact of this problem on solving PDEs.

The correction is simple and easy to implement. Based on a detailed analysis of the computational graph, the authors propose a simple and effective method for removing inter-point effects and provide a reasonable diagnostic metric.

The paper is clearly written and logically organized. Its motivation is clear and well defined, drawing on a reasonable computational graph analysis and experimental results from concrete applications. Based on these results and analyses, the authors develop a corresponding solution and present it through intuitive experimental designs and metrics. Readers can easily understand the core problem and the proposed solution.

Critical weaknesses

The most important weakness concerns where the core significance of the method lies. First, models with inter-point fusion can be divided into two categories: neural operators and PINNs. For neural operators, their capabilities come primarily from training data, namely supervised learning, while physics-informed training serves more as an auxiliary tool. Moreover, because their outputs are functions, their residuals do not necessarily need to be computed through automatic differentiation; finite differences and other methods can also be used. For PINNs, mainstream models currently do not use fusion. Furthermore, some existing fusion models use independently supplied query inputs (x), and therefore do not suffer from the problem described in this paper.

Therefore, I believe the paper needs stronger evidence demonstrating that the problem it addresses is meaningful, rather than merely summarizing a problem that has already been addressed through technical measures in other fusion models or does not actually arise in practice. I think the authors have identified an interesting problem, but there are further questions worth considering and discussing. The paper’s discussion of its central issue currently lacks sufficient depth.

Second, the paper overclaims its theoretical contribution. Regarding the second contribution listed in the introduction, I do not consider it a theoretical contribution if it merely applies the chain rule to derive the computational graph and illustrate a highly intuitive phenomenon.

Questions for authors

Building on the discussion of supervised training in Section 5.1, how does the severity of the identified failure mode change when supervised solution data are incorporated into physics-informed operator learning? Comparisons across data-only, physics-only, and hybrid training would help clarify whether supervision mitigates the problem and how the benefit of decoupling depends on the amount of data and the weight of the physics loss.

Can finite-difference residuals serve as a practical alternative to the proposed correction? Under comparable accuracy and sampling conditions, how do finite differences and gradient-decoupled AD compare in terms of solution accuracy, training time, and memory consumption? How do resolution and discretization errors affect this comparison?

Beyond the comparisons already provided, could the authors compare corrected fusion-based models with pointwise models under matched computational budgets? This would help clarify the practical benefit of fusion after the identified failure mode has been addressed. It would also be valuable to discuss which PDE characteristics or problem settings are most likely to make corrected fusion-based models competitive.

6 comments

We acknowledge the reviewer for your comments. However, we believe that several of your criticisms arise from an incorrect characterization of the scope and contributions of our paper. We would like to clarify the following points.


[W1] Regarding the practical significance of this research

The reviewer states that we have "identifies a practically meaningful problem" in strengths part, while ask "where the core significance of the method lies" in weaknesses part. We are puzzled by this contradictory assessment.

First, we kindly disagree with your claim that mainstream PINNs use MLPs. Our Sec.3 Related work explicitly identifies a large number of fusion-based PINNs that meet our criteria, including highly cited papers such as PIPN (JCP, cited by 226), PINNsFormer (ICLR'24, cited by 241) and so on. All these works use automatic differentiation to compute PINN residuals, and we have verified that they exhibit Derivative Cheating. More importantly, similar issues have already been sporadic observed by community, for example,

  • PI-GANO [1]: They observed that max pooling in PIPN is detrimental when performing AD residual. They attributed it to max pooling being non-differentiable and suggested using mean pooling, which was also explicitly proven to fail in our analysis.
  • R. Bischof [2]: They point that BatchNorm should not be used in PINNs, but they attributed this to numerical values being tampered with by batch statistics. Our experiments demonstrate that if gradients can be decoupled at the correct location, BatchNorm is actually usable.
  • TKNO [3]: They point that for backbones such as FNO and Transformer, AD has issues in physical training, and therefore switched to finite differences for calculating residuals across all fusion architectures. However, they neither explained the origin of the problem nor provided an alternative solution to retain AD.
  • PINNsFormer Repo [4]: In the official GitHub repo of PINNsFormer, a user pointed out that after correcting the AD residual calculation, the solution accuracy actually decreased, and expressed confusion over "why the reported performance could be good despite the PDE loss being incorrect."

However, none of the above works correctly location the cause of this problem, while our contribution exactly lies in the identification, formalization, and causal validation of this mechanism. Therefore, the reviewer's claim that this problem "does not actually arise in practice" is clearly invalid.

Furthermore, neural operators and PINNs are not mutually exclusive categories. Even among neural operators, there are numerous examples of using automatic differentiation to compute residuals. Even if some methods primarily rely on data-driven learning, as long as they incorporate AD-based PDE residuals, correcting semantic errors in those residuals is necessary. Therefore, the failure mode we identify can be expected to affect a substantial proportion of work in the PINN community. More importantly, our work addresses a fundamental issue of correctness rather than incremental performance gains. Therefore, we believe that compared with other PINN works that propose yet another architecture or optimizer, the significance of our work is clearly greater.

We want to argue the reviewer's assessment that our "discussion of its central issue currently lacks sufficient depth." We have already provided a complete chain of evidence regarding the manifestations, causes, and solutions of this failure mode, while each additional topic you request could independently constitute another ICLR paper. These could be interesting extensions of our work, but addressing such extensive derivative topics within a single paper is impractical and would not help strengthen our core claim.

[W2] About contribution

We respectfully direct the reviewer to the ICLR 2027 Reviewer Guidelines (https://iclr.cc/Conferences/2027/ReviewerGuidelines), which define contribution in terms of whether a submission brings new knowledge to the community, rather than whether it applies sophisticated mathematical theories. We have never claimed to have reinvented the chain rule. Our contribution lies in identifying this failure mode for the first time, while the chain rule is merely a theoretical tool employed in our analysis. We argue that it is unreasonable for the reviewer to question our contribution simply because we used a chain rule decomposition.

For example, the NeurIPS 2025 Best Paper [5] did not propose any new algorithm, but merely increased the number of network layers in RL to 1024, which is an operation that everyone in machine learning knows how to perform. Nevertheless, they challenged the conventional design practice of using shallow neural networks in traditional RL. Therefore, the conference committee and reviewers still value the significant contribution of this paper.

[Q1] Regarding the data/physical hybrid-driven issue

Introducing supervised data does not automatically correct the semantic discrepancy in an AD-based PDE residual. In hybrid training, the data loss may compensate for an inaccurate physics constraint, but the underlying residual remains inconsistent. Therefore, a more likely scenario is that introducing incorrect PDE residuals would actually reduce solution accuracy compared with a purely data-driven approach. Importantly, without explicitly identifying Derivative Cheating problem, researchers would typically difficult to realize where goes wrong. This is the significance of our work.

[Q2] Finite differences vs. automatic differentiation

Finite differences can of course serve as an alternative means of evaluating spatial derivatives. However, it will introduce discretization errors and require appropriate choices of stencil, resolution, and boundary treatment, and require collocation points to lie on a regular grid. Therefore, automatic differentiation is the default implementation of PINN follows Raissi et al. (2017), while works that employ finite differences generally explicitly highlight this choice in their experimental settings.

[Q3] Comparison of Fusion-based Model and MLP

We would like to clarify that this require is out of our claim scope. Our paper is a diagnostic study, not a proposal claiming that fusion-based architectures universally outperform point-wise MLPs. Requiring a diagnostic paper to first demonstrate that the target methods it diagnoses outperform other methods is unreasonable. This is like we claiming to have fixed a car, but the reviewer require us to proof that it is faster than other cars. We have never seen a similar precedent in the past diagnostic papers. For example, Krishnapriyan et al. [6] diagnosed gradient pathologies in PINNs without first having to demonstrate that PINNs outperform other numerical methods, while Wang et al. [5] investigated the relationship between network depth and performance in Contrastive RL without first having to demonstrate that Contrastive RL outperforms other RL methods.


We appreciate that the reviewer recognizes the practical relevance of the identified problem and the effectiveness of our correction. However, we believe the current assessment does not adequately account for the evidence already presented in our paper and outside community. We respectfully request that the reviewer reconsider whether the stated weaknesses actually challenge our contribution.


References

[1] W. Zhong et al., Physics-Informed Geometry-Aware Neural Operator, CMAME, 2025.

[2] R. Bischof, 4 Ideas for Physics-Informed Neural Networks that Failed, Towards Data Science (practitioner report), 2023.

[3] S. Ding et al., Physics-informed Neural Operator Learning for Nonlinear Grad-Shafranov Equation, in ICML, 2026.

[4] Issue #9, PINNsFormer repo. https://github.com/AdityaLab/pinnsformer/issues/9.

[5] K. Wang et al., 1000 Layer Networks for Self-Supervised RL: Scaling Depth Can Enable New Goal-Reaching Capabilities, in NeurIPS, 2025.

[6] A. Krishnapriyan, A. Gholami, Characterizing Possible Failure Modes in Physics-Informed Neural Networks, in NeurIPS, 2021.

Thank you for your response. First, I acknowledge that the identified problem exists. However, considering the practical capabilities of fusion-based models and the fact that many existing fusion models do not exhibit this derivative-cheating issue, I believe its practical significance remains limited. As you emphasize, this is an “academic paper, not a novel,” and its conclusions should therefore be supported by sufficient evidence. In your response, I have not seen additional experimental data supporting the claimed significance of the problem. My questions were raised precisely to clarify this significance, based on my understanding of the paper. In my view, the paper’s main contribution lies in its analysis of the problem rather than in the design of the correction method. Therefore, without sufficient evidence addressing the significance of that problem, I respectfully maintain that my concerns remain unresolved.

Reviewer_LWGROpenReview ↗
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Paper summary

This paper discusses the derivative cheating issue in fusion-based PINN training. For fusion-based PINNs, the PDE loss gradient contains an extra fusion term that couples contributions from different collocation points. The paper proposes a metric called Derivative Cheating Intensity (DCI), which measures the difference between the true spatial differential operator and the AD/full gradient of the fusion-based PINN. The paper then demonstrates that by applying a stop-gradient to the fusion input, which removes the extra fusion term, the DCI drops to zero by definition. The paper then empirically demonstrates that for fusion-based PINNs, applying the decoupling trick improves solution errors.

Critical strengths

The problem that's being identified and the proposed remedy are very straightforward. The paper is also relatively easy to follow. The substantial reductions in solution error across several fusion-based backbones are useful empirical evidence.

Critical weaknesses
  1. The contribution is limited. The paper contains an unnecessary number of theorems and proofs, while the core idea is very simple. The additional derivative term follows directly from the chain rule, and DCI becomes zero by construction after removing that term. In my humble opinion, the extensive theorems and proofs distract from a very simple observation rather than strengthen it. And although decoupling improves accuracy, the simpler pointwise MLP still achieves lower errors on both Poisson and Heat in Table 9. The practical advantage of retaining fusion is therefore unclear on these benchmarks.

  2. I am not convinced that removing the fusion term generally restores the correct physical derivative. For a query-dependent context, this term is a valid chain-rule contribution, not an AD error. The paper needs to justify why the frozen-context function is the intended physical field; zero DCI alone does not establish this. Appendix H itself acknowledges a mismatch between the forward-evaluated and AD-differentiated functions under module-level decoupling. There is also an algebraic error in Appendix A.3: substituting a=−b/Na=-b/N into Equation (49) gives gi(t)=bxˉ−bxi/Ng_i(t)=b\bar{x}-bx_i/N, which is constant, contrary to Equation (55). The counterexample's conclusion about this moving-context function is therefore incorrect as written.

Questions for authors
  1. Is the inference field defined with fixed context or with context regenerated from the query? Do the proposed derivatives agree with finite differences of that same field?
  2. How does correcting Equation (55) affect the counterexample and its interpretation?
  3. Given the pointwise MLP results, what practical benefit of fusion do the experiments establish beyond correcting the failure of the original implementations?
3 comments

We acknowledge the reviewer for your unique perspective. Before addressing your concerns, we would first like to respectfully point out an obvious factual error in your review:


In Weaknesses 2, you argue that the counterexample presented in our Appendix A.3 is incorrect. We do not agree with this assessment.

This is essentially a very simple one-dimensional ODE, and a single numerical example is sufficient to verify it directly. In the setting of Eq. 47: u′(x)=0u'(x)=0, suppose that an analytical solution is u=5u=5, which is a constant. Consider a fixed collocation set X={1,2,3}, consisting of three sampling points: x1=1x_1=1, x2=2x_2=2, and x3=3x_3=3. We then construct the fusion model uf(xi,X)=bxˉ−bxi/Nu^f(x_i,X)=b\bar{x}-bx_i/N, where the mean xˉ\bar{x} denotes the geometric center of the set XX, which is always equal to 2, whereas bxi/Nbx_i/N varies with xix_i and is therefore not constant. Consequently, uf(x1,X)=1.67bu^f(x_1,X)=1.67b, uf(x2,X)=1.33bu^f(x_2,X)=1.33b, and uf(x3,X)=1.00bu^f(x_3,X)=1.00b. Clearly, as long as parameter b≠0b\neq 0, the fusion model ufu^f cannot simultaneously output the same value at points x1x_1, x2x_2, and x3x_3.

How could this be a constant???

When b=0b=0, the contribution of the fusion term bxˉb\bar{x} is also eliminated, which corresponds precisely to the case excluded by our Assumption A.2: the fusion model degenerates into a point-wise model. Our DCI is specifically designed to directly measure whether such a situation occurs. And the results in Table 1 demonstrate that this coincidence is almost impossible to occur, as the optimizer only requires that a+b/N=0a+b/N=0, and does not impose any constraints on bb itself. Therefore, aa and bb can take any values but not only 0 as long as this residual is satisfied.

This example also illustrates the correctness of our decoupling operation. When we constrain only the derivative of the point-wise term in the fusion model uf(xi,X)=axi+bxˉu^f(x_i,X)=ax_i+b\bar{x}, i.e., daxi/dxi=0dax_i/dx_i=0, the optimal solution must satisfy a=0a=0. At this point, the optimizer can independently adjust the parameter b=2.5b=2.5 so that uf≡5u^f \equiv 5 for any xi∈Xx_i \in X, without having to enforce a=−b/Na=-b/N to make the total derivative equal to zero.


We are aware that when you ask an LLM (especially ChatGPT 6 Sol) to check this paper for mathematical errors, it will tell you that Eq. (55) is constant with respect to tt. However, we have already explicitly defined in Section 2.2 (Lines 131–135) of the main text that XX is the input collocation set, and xix_i is the ii-th collocation point in this set. Therefore, the query point xix_i itself is part of the context XX. We have also explicitly stated in Line 879 that we replace xix_i in the set XX with tt. Therefore, Eq. (55) essentially expresses ufu^f as a function of the point xix_i with index ii, while tt is merely an intermediate quantity constructed for the convenience of differentiation.

In our own review tests across several LLMs, only ChatGPT inexplicably equated ufu^f in Eq. (55) with gtg_t in Eq. (49), thereby concluding that ufu^f is constant. However, Eq. (55) only concerns the forward values of ufu^f (as we explicitly emphasized in Line 900), which are unrelated to whether the fusion context is frozen during backward gradient computation, and it represents neither gtg_t nor hth_t. We do not believe that human readers would have such a misunderstanding. Even so, to further eliminate ambiguity, we have updated our manuscript by fully restoring Eq. (55) to the representation of the fusion model in Eq. (48): uf(xi,ϕ(X))=−bNxi+bxˉu^\mathrm f\bigl(x_i,\phi(X)\bigr)=-\frac{b}{N}x_i+b\bar{x}, abandoned the use of tt as notation. We are very confident that, with this minor change alone, ChatGPT will no longer claims that this counterexample is incorrect.

Therefore, we highly suspect that this assessment stems from an LLM hallucination, rather than a correct evaluation based on the context of this counterexample. The ICLR reviewing policy explicitly prohibits reviewers from citing any false or hallucinated content generated by LLMs, and we also kindly request the AC/SAC to pay attention to this unusual comment.

The following is the response to your main concerns.


[W1] The contribution is limited

We direct the reviewer to the ICLR 2027 Reviewer Guidelines (https://iclr.cc/Conferences/2027/ReviewerGuidelines), which define contribution in terms of whether a submission brings new knowledge to the community, rather than whether it applies sophisticated mathematical theories. The key question is whether the conclusions of a paper are likely to surprise a broad audience or change established practices in the field. It is ridiculous for the reviewer to question our contribution simply because we used a chain rule decomposition, especially for a diagnostic paper dedicated to understanding negative results. For example, the NeurIPS 2025 Best Paper [1] did not propose any new algorithm, but merely increased the number of network layers in RL to 1024, which is an operation that everyone in machine learning knows how to perform. Nevertheless, they challenged the conventional design practice of using shallow neural networks in traditional RL. Therefore, the conference committee and reviewers still value the significant contribution of this paper.

In contrast, our paper challenges the default practice in the PINN field of directly using automatic differentiation to optimize fusion models, while fusion-based PINNs themselves remain an actively developing research area. Our analysis and experiments demonstrate that highly cited papers in the field, including PIPN [2] and PINNsFormer [3], have used incorrect automatic differentiation to construct residuals, and such papers still have continued to emerge in recent years (ICML'26 [4,5], NeurIPS'26 [6]). Therefore, the failure mode we identify can be expected to affect a substantial proportion of future work in the PINN community, and we do not believe that this constitutes a so-called “limited contribution.”

The reviewer explicitly acknowledges that the substantial reductions in solution error across multiple fusion-based backbones constitute useful empirical evidence. Yet the review simultaneously assigns the lowest informativeness score, without explaining why identifying and experimentally correcting a previously uncharacterized failure mode provides little or no new knowledge. We respectfully request a concrete justification for this assessment, particularly given that the diagnosed architectures have already been widely adopted in the existing PINN literature.

Regarding our presentation, we would like to kindly remind the reviewer that you are reviewing an academic paper, not a novel. This means that every claim must be supported by rigorous theoretical or experimental evidence, rather than relying solely on intuitive narratives. To demonstrate that derivative inconsistency occurs in PDEs of arbitrary order, constructing a higher-order chain rule expansion is a necessary step. Nevertheless, considering readability for a junior audience, we have retained only the proof sketch with first-order chain rule (Eq. 16) in the main text, accompanied by Fig. 3 for visualization, while deferring the more complex rigorous proof steps to the appendix. We would be very appreciate if the reviewer could provide any simpler proof chain you think, but we do not accept penalizing this work only for being "overly rigorous" without identifying any specific errors in the proof.

[W2 & Q2] Regarding the semantic of derivatives

We respectfully believe that this concern stems from a fundamental misunderstanding of our paper and the counterexample presented in Appendix A.3, as we discussed above. Frankly, we believe that ICLR reviews are supposed to be rigorous and professional. Therefore, we are unable to understand why you select “Confidence: 4: I have substantial direct research experience on this topic”, while make such an incorrect assessment on a high-school-level algebra problem.

Appendix H investigates whether gradient decoupling weakens the ability of fusion-based models to represent geometric features, thereby introducing inductive biases. This is a potential side effect of module-level decoupling, which we discuss as a limitation of our work and to support the Line 416 in our main text. We do not understand how the reviewer could interpret this as meaning that “decoupling itself is incorrect.” Or is this yet another LLM hallucination?

[Q1] Is the inference field defined with fixed context or with context regenerated from the query?

The reviewer seems to have misunderstood the fundamental nature of Derivative Cheating. This failure mode is unrelated to the inference stage. Its essence lies in the fact that derivatives of the point-set context are mixed into the PDE residual during training, which naturally requires the query points themselves to originate from the point-set context. This is standard practice in fusion-based PINNs, and models including PIPN and PINNsFormer all follow this pattern. We have already explicitly defined this in Lines 131–135 of the main text. Fixing the context is merely an intermediate step used in constructing our proof, and we believe that we have already clearly stated this in Lines 331–332 of the main text. This step also directly corresponds to the gradient decoupling in Section 6 (Corollary 6.1). Therefore, we are unclear as to how this could have caused any ambiguity.

Under this setting, according to Theorem 5.2/A.4, the residual obtained through automatic differentiation is naturally different from the approximate spatial derivatives obtained using finite differences, even assuming that the finite difference method introduces no approximation error. The numerical example above has well demonstrated this: The finite differences between x1x_1, x2x_2, and x3x_3 are clearly 0.33b0.33b, whereas the value obtained through automatic differentiation is 0.

[Q3] Comparison of Fusion-based Model and MLP

We know that LLMs frequently raise such concern. However, this require is out of our claim scope.

We have never claimed that the fusion-based model is superior to the MLP.

Requiring a diagnostic paper to first demonstrate that the target methods it diagnoses outperform other methods is extremely unreasonable. This is like we claiming to have fixed a car, but the reviewer require us to proof that it is faster than other cars. We have never seen a similar precedent in the past diagnostic papers. For example, Krishnapriyan et al. [7] diagnosed gradient pathologies in PINNs without first having to demonstrate that PINNs outperform other numerical methods, while Wang et al. [1] investigated the relationship between network depth and performance in Contrastive RL without first having to demonstrate that Contrastive RL outperforms other RL methods.

Perplexingly, on the one hand, the reviewer penalizes our theory for being “overly complex” and weakening the core claim; while on the other hand, simultaneously demanding additional justification for the advantages of fusion models, which clearly falls outside the scope of our core claim. We find these contradictory demands difficult to understand. We therefore sincerely ask the reviewer:

Is substantiating a hypothesis outside the scope of a paper's core claim really more necessary than rigorously proving the core claim itself? Is the reviewer applying technically neutral standards, or imposing a presumption of guilt on our work from the outset?


References

[1] K. Wang, I. Javali, 1000 Layer Networks for Self-Supervised RL: Scaling Depth Can Enable New Goal-Reaching Capabilities, in NeurIPS, 2025.

[2] A. Kashefi, T. Mukerji, Physics-Informed PointNet: A Deep Learning Solver for Steady-State Incompressible Flows and Thermal Fields on Multiple Sets of Irregular Geometries, J. Comput. Phys., 2022.

[3] Z. Zhao, X. Ding, PINNsFormer: A Transformer-Based Framework for Physics-Informed Neural Networks, in ICLR, 2024.

[4] H. Jia, P. Yin, Learning to Think in Physics: Breaking Shortcut Learning in Scientific Diffusion via Representation Alignment, in ICML, 2026.

[5] S. Ding, Z. Zhang, Physics-informed Neural Operator Learning for Nonlinear Grad-Shafranov Equation, in ICML, 2026.

[6] B. D. Shaffer, B. Kinch, A Meshfree Exterior Calculus for Generalizable and Data-Efficient Learning of Physics from Point Clouds, in NeurIPS, 2026.

[7] A. Krishnapriyan, A. Gholami, Characterizing Possible Failure Modes in Physics-Informed Neural Networks, in NeurIPS, 2021.

Reviewer_zdtjOpenReview ↗
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Paper summary

This work investigates derivative computation in physics-informed neural networks (PINNs) with information fusion over collocation points. The authors identify that when predictions depend on both a query coordinate and a fused set of collocation points, automatic differentiation of the PDE residual computes gradients through the fusion pathway. This outcome deviates from the spatial derivative evaluated with the fusion context fixed. They term this issue derivative cheating, define the Derivative Cheating Intensity (DCI) to quantify the residual mismatch, and propose gradient decoupling to rectify derivative evaluation. The method is validated on Poisson, Helmholtz and heat equations using BatchNorm, PI-DeepONet, PointNet and Transformer-based architectures. Additional ablation studies and results for temporal fusion are provided in the appendix.

Critical strengths

The paper shows how gradients through cross-point fusion can enter PINN residuals, offering a testable explanation for low residual loss alongside large solution error.

Gradient decoupling preserves the forward computation while changing how residual derivatives are computed.

Critical weaknesses

The assumptions in Appendix A.1 + A.3 are too strong. When put together, the conclusion follows without derivation: since the AD operator output equals the target ff, while the output of the fixed-context PDE operator differs from it, the latter naturally does not equal ff. What really needs to be proved is under what conditions the fusion architecture necessarily or easily produces the operator discrepancy required by A.3. The paper treats this step as an assumption, so the theorem can only demonstrate a conditional possibility of failure and cannot support a general claim about fusion PINNs. In Appendix A.1, the paper states that zero residuals at all points within each sampling batch are equivalent to the PDE being satisfied over the entire domain. This does not hold for a batch-conditional model, because each batch actually corresponds to a different frozen function. Zero residuals at finite sampling points cannot imply global satisfaction. Although the authors state that the sampling is dense, even if the union of sampling points across iterations is dense, what is constrained is still a family of functions that varies across batches rather than one and the same function.

Questions for authors

For an ordinary point-wise MLP, there is no need to conduct experiments that change the batch. However, for fusion-based models, the output depends on the entire batch X. Have the authors tested the following: keeping the same set of test points fixed and only changing the other accompanying input points or the batch size, how much do the predicted values and errors change? If the changes are significant, can the existing results represent that the model has learned a stable PDE solution?

Theorem 5.2 aims to explain how a fusion-based model can achieve zero residual with an incorrect solution. However, Assumption A.3 already postulates that the fusion-induced derivative discrepancy changes the output of the PDE operator, so the conclusion appears to rely critically on A.3. Which properties of the studied architectures and PDEs establish that A.3 holds? If A.3 cannot be justified from such properties, should Theorem 5.2 be framed only as a conditional or existence-style failure case, rather than as a broader claim? The authors should clarify the scope of the theorem and, if possible, provide sufficient conditions or empirical evidence supporting A.3.

5 comments

We thank the reviewer for your comments. We would like to clarify the theoretical assumptions underlying our analysis and provide additional experimental evidence to address your concerns.


[W1 & Q2] About theory assumptions

The reviewer considers our Assumption A.3 (differential detectability) to be too strong, but your description that "the fusion-induced derivative discrepancy changes the output of the PDE operator" seems to refer instead to our Assumption A.2 (non-degeneracy of the fusion model). Therefore, we clarify all assumptions together here.

  • Assumption A.1 only requires the parameter capacity of the model enough to be capable of fitting the AD residual it currently uses, without assuming that it can recover the correct physical solution. This should be a standard requirement for any reasonable PINN implementation.

  • Assumption A.2 is aims to exclude a zero-measure coincidence, namely: Regardless of how the fusion features ϕ\phi change, the model's output remains unchanged. That is, the output of the model does not respond to changes in geometric features at all, and the fusion model actually degenerates into a point-wise model. Because only in this case is dudϕ\frac{du}{d\phi} identically equal to 00, causing Eq. (29) to not hold.

  • Assumption A.3 is also aims to exclude an extremely rare exception, namely: at the point x0x_0, when the kk-th order derivative dkudxk\frac{d^k u}{dx^k} of the model undergoes a slight change along a specified direction, the internal changes within the differential operator N\mathcal{N} exactly cancel each other out, resulting in the value of N[u](x)\mathcal{N} [u] (x) remaining completely unchanged. This is virtually almost non-existent in practice. Therefore, for any PDE operators that genuinely depend on derivatives, this assumption holds naturally.

The reviewer request us to prove "which properties of the studied architectures and PDEs establish that A.3 holds" In fact, our paper has already provided empirical evidence: our definition of DCI is exactly the directly measurement of A.2 & A.3. When A.2 and A.3 does not hold at all points ∀xi∈X\forall x_i \in X, theoretically ∑iNdϕdxi\sum_{i}^{N} \frac{d\phi}{dx_i} should be strictly equal to 00, that is, DCI = 0. Therefore, our experiments in Table 1 verify that Assumptions A.2 & A.3 almost always hold in practice. The DCI sweep in Appendix F also provides empirical support for A.2.

[Q1] Batch Dependence and Prediction Stability

We thank the reviewer for raising this question. In fact, we do not use a fixed collocation set when training fusion-based models. Instead, we randomly regenerate the collocation points at each iteration, as we have already stated in Line 1079. Therefore, the fusion representation learned by the model should theoretically correspond to the geometry Ω\Omega, rather than depend on a specific collocation set XX. A sufficiently accurate physics-informed solution should ideally exhibit consistent predictions across different batches and respond only to changes in geometry. This implies that resampling collocation points uniformly at random within the same geometric domain should have little effect on the fused representation and, consequently, on the model output. Here, we have conducted an additional experiment on PIPN on Poisson to demonstrate the prediction accuracy of the model with different batch sizes during inference:

Inference Batch SizePIPN (Original)PIPN (Decoupled)
N=1000N=10002.87e-11.62e-2
N=2000N=20001.66e-11.77e-2
N=3000N=30002.24e-11.60e-2
N=4000N=40001.31e-11.59e-2

As can be seen, before decoupling, the model still fails to produce the correct solution even when the batch size is changed, whereas after decoupling, the model's prediction accuracy does not vary significantly with batch size.

Furthermore, we respectfully believe that the issue you raised is actually an architectural issue inherent to fusion-based models, independent of the failure mode we identified, which is an issue with the loss function. In other words, even in the absence of Derivative Cheating, the dependence of fusion-based models on specific batches is still worth further discussion. Therefore, we leave this issue for future work, as discussed in Appendix H.


We hope these clarifications and additional experimental results adequately address the reviewer's concerns regarding the validity of our theoretical assumptions and the stability of fusion-based PINNs under different batch configurations.

  1. Thank you for the authors’ response and additional experiments. The clarification of the distinction between Assumptions A.2 and A.3 is helpful.

  2. However, my main concern about the scope of Theorem 5.2 remains. Once A.1–A.3 hold, the fact that the operator output with the fusion context held fixed is not equal to ff follows almost directly from the assumptions. The authors have not addressed this point.

  3. The chain-rule expansion explains how the derivative discrepancy enters the computation, but it does not establish that A.3 generally holds for the fusion architectures and PDEs studied in the paper. In other words, I am not arguing that the theorem is logically incorrect under its assumptions. Rather, its conclusion is conditional, and the key condition has not been justified in general. The DCI experiments support the observed phenomenon in the evaluated settings, but are not sufficient on their own to establish that A.3 is a generally mild assumption or that it “almost always” holds. I suggest that the authors explicitly qualify the scope of the theorem and related claims. This is only a suggestion; if the authors disagree, they are welcome to explain why, but I would appreciate a direct response to this concern rather than a response addressing only the suggestion.

  4. Regarding batch dependence, I accept the authors’ point that it is a distinct mechanism from derivative cheating. The additional experiments show that the decoupled model achieves low errors across the tested inference batch sizes, which is useful. However, aggregate errors across different batch sizes do not directly show how predictions at fixed query points change when the other context points are resampled. Thus, these results partly address the stability concern but do not directly answer my original question about resampling the context. If the authors consider this issue outside the scope of the paper, they could qualify their claims about solution stability accordingly. Batch dependence is still relevant to how the outputs of fusion-based models should be interpreted.

We sincerely thank the reviewer for the follow-up request and we remain open to academic discussion within any reasonable scope. We provide the following clarifications in the hope that they address your main concerns.


[2] "The result follows almost directly from A.1–A.3."

We would like to clarify the steps of our proof:

  1. Apply the chain rule to expand the total derivatives of the fusion model (Eqs. (35)–(36)).
  2. Use this expansion to construct a contradiction. The total derivatives of the fusion model are in exact agreement with the PDE, but only the pointwise component corresponds to the mapping defined by the PDE in Eq. (1) (Eqs. (37)–(39)).
  3. Consequently, even when the total derivatives of the fusion model are in exact numerical agreement with the PDE, the forward value u(x)u(x) differs (Eq. (40)).

Thus, the key step in the argument is the application of the chain rule (Step 1). Without this step, we cannot construct the contradiction that establishes that the forward values of the fusion model differ from the ground truth even when the derivatives are in exact agreement. Although the proof is indeed very simple, the conclusion cannot follow directly from A.1–A.3 alone.

[3] Regarding Assumption A.3

In our argument, Assumption A.3 only requires detectability at the level of the governing PDE itself, irrespective of the fusion model used. We say that Assumption A.3 holds everywhere because for the governing PDE itself, the points at which it fails form a set of Lebesgue measure zero.

We consider a numerical example with the following two-dimensional Poisson equation.

\qquad \Delta u=\partial_{xx}u+\partial_{yy}u,$$ Fix a collocation point $(x_0,y_0)$. Let $z_{xx}$ and $z_{yy}$ denote the two second derivative values at that point, and let $\delta_{xx}$ and $\delta_{yy}$ denote their perturbations. Following the notation of Eq. (31), the operator values before and after perturbation are, respectively, $$z_{xx}+z_{yy} \qquad\text{and}\qquad (z_{xx}-\delta_{xx})+(z_{yy}-\delta_{yy}).$$ Their difference is $$(z_{xx}+z_{yy}) - [ (z_{xx}-\delta_{xx})+(z_{yy}-\delta_{yy}) ] = \delta_{xx}+\delta_{yy}.$$ Thus, Assumption A.3 fails at this point if and only if $\delta_{xx}+\delta_{yy}=0$. All perturbations for which A.3 fails form the set: 𝒞 = { (δₓₓ, δᵧᵧ) ∈ ℝ² | δᵧᵧ = −δₓₓ }. For any given $\delta_{xx}$, there is only one value of $\delta_{yy}=-\delta_{xx}$ for which the two perturbations cancel exactly. In actual random sampling, **the probability that all sample in the 2D plane fall exactly on this diagonal approaches zero**. And Assumption A.3 holds as long as at least one sample falls outside this diagonal line. This is why we say that it holds “almost always.” However, when viewed in conjunction with the proof of Theorem A.4, one can indeed deliberately construct a highly specialized fusion model (such as an MLP that uses only a single mean-pooling layer), so that the two derivative perturbations in the Laplacian cancel exactly at every sampled point. In this case, we acknowledge that Assumption A.3 is indeed violated and that the DCI is also zero. We thank the reviewer for pointing this out. We would like to emphasize that **this exact cancellation occurs only for specific combinations of a PDE and a model architecture**. It can serve as a theoretical counterexample to our analysis, but **it is uncommon in practice**. In the most common uses of fusion models, Assumption A.3 still holds, as demonstrated in Table 1. We therefore consider Assumption A.3 mild in the settings studied in this paper. We have explicitly added this clarification to **Appendix A.1 (line 758)** to delimit the scope of the assumption. We thank the reviewer again for helping strengthen the argument in our paper.
Reviewer_JYCxOpenReview ↗
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Paper summary

The paper studies a failure mode of PINNs whose backbones use inter-point fusion mechanisms, in which the prediction at a collocation point also depends on the other points in the batch. As a result, PDE residuals computed with automatic differentiation include fusion-induced terms in addition to the true spatial derivatives. The optimizer can exploit these terms to drive the residual loss close to zero even though the predicted field does not satisfy the PDE. The authors call this phenomenon derivative cheating. To prevent it, they treat the fusion input as a stop-gradient input, which removes the fusion contribution ∂uθf∂ϕ∂ϕ∂x\frac{\partial u^{\mathrm{f}}_{\theta}}{\partial \phi}\frac{\partial \phi}{\partial x} from the AD derivatives while still allowing the parameters to be trained. Experiments show that this decoupling brings the errors of fusion-based models close to those of a point-wise MLP. The authors also propose a diagnostic metric, the Derivative Cheating Intensity (DCI), which drops to zero after decoupling.

Critical strengths

The experiments support the claim that derivative cheating degrades the accuracy of fusion-based PINNs. In the main text, all four fusion-based backbones (MLP+BatchNorm, PI-DeepONet, PIPN, and MMET) reach low residual losses on the Poisson, Helmholtz, and Heat benchmarks but have large relative L2 errors (mostly above 10%). After gradient decoupling, all of them fall below 5%, close to the point-wise MLP baseline. Appendix E shows that the same behaviour occurs for two temporal-fusion backbones, PINNsFormer and PINNMamba, on the nonlinear NS2d-LT benchmark: decoupling reduces their L2 error from ~0.6–0.7 to ~0.04–0.05.

The paper introduces the DCI, a metric that quantifies how much the fusion pathway contributes to the AD-computed residual. It can be computed at inference time by comparing the full AD operator with its stop-gradient counterpart. This makes it applicable to new architectures and PDE problems where reference solutions are unavailable, allowing to check whether a fusion-based PINN is affected by derivative cheating.

Critical weaknesses

Corollary 6.1 is circular as stated. Equation (19) assumes that the true residual N[u~θ⋆f]�0�−f�1�=0\mathcal{N}[\tilde{u}^f_{\theta^\star}]�0� - f�1� = 0 on Ω\Omega, so u~θ⋆f∈S\tilde{u}^f_{\theta^\star} \in \mathcal{S} follows directly from the definition of S\mathcal{S}, without any reference to decoupling or to the capacity assumption. The statement that would carry the paper's argument is that, after decoupling, the operator computed by AD coincides with the true differential operator of the predicted field, that is, NAD[u~θf]�2�=N[u~θf]�3�\mathcal{N}^{\mathrm{AD}}[\tilde{u}^f_{\theta}] �2� = \mathcal{N}[\tilde{u}^f_{\theta}]�3�, so that a vanishing AD residual implies a valid solution.

The paper does not specify the number, distribution, and resolution of the test points, whether these are evaluated in a single forward pass or in batches, whether BatchNorm-based models use batch or running statistics at inference, or which point set is used to compute the DCI. Since the paper's own premise is that a fusion-based prediction depends on the set of points XX processed jointly with it, the reported L2L_2 errors and DCI values depend on these choices as well as on the trained model. Without the protocol, the results cannot be reproduced, and their sensitivity to the test configuration remains unclear.

Questions for authors
  • Could the authors restate Corollary 6.1 with the hypothesis expressed in terms of the AD-computed operator, assume NAD[u~θ⋆f]�0�=f�1�\mathcal{N}^{\mathrm{AD}}[\tilde{u}^{\mathrm{f}}_{\theta^\star}]�0� = f�1�, and show that this implies u~θ⋆f∈S\tilde{u}^{\mathrm{f}}_{\theta^\star} \in \mathcal{S}?

  • How many test points are used to compute the reported L2L_2 errors and error maps, and how are they distributed and at what resolution?

  • Are the test points passed through the model in a single forward pass or in batches? If in batches, what is the batch size and how are the batches composed?

  • For the BatchNorm-based models, does inference use batch statistics (train mode) or running statistics (eval mode)?

  • Which point set XX is used to compute the DCI in Equation (23)?

1 comment

We sincerely thank you for your constructive comments and for recognizing the empirical evidence across spatial and temporal fusion backbones, as well as the usefulness of DCI as a diagnostic. The following is the response to your concerns.


[W1 & Q1] Representability under Gradient-Decoupled Fusion

We agree that Corollary 6.1 should state its hypothesis in terms of the PDE residual computed by AD, and we thank you for pointing this out. Following your suggestion, we have restated Corollary 6.1 as Lemma 6.1 and provided a proof in Appendix A.3. We outline the proof strategy below.

  1. Fix the collocation set XX and use the same fusion feature ϕ(X)\phi(X) at every query point xx, as specified in Assumption A.8. The resulting field h(x)=uθ⋆f(x,ϕ(X))h(x)=u_{\theta^\star}^{f}(x,\phi(X)) and the gradient-decoupled model have identical forward values because stop-gradient preserves the value of the fusion feature (Eqs. (47)–(48)).
  2. Apply the chain-rule expansion in Eq. (35). Each fusion-induced term contains a derivative of the fusion feature with respect to the query coordinate. These terms vanish under gradient decoupling, so the AD derivatives coincide with the classical spatial derivatives of hh up to the order required by the PDE (Eq. (49)).
  3. Substitute the common forward values and derivatives into the governing operator. This gives NAD[u~θ⋆f](x)=N[h](x)\mathcal{N}^{\mathrm{AD}} [ \tilde u_{\theta^\star}^{f} ] (x)=\mathcal{N} [ h ] (x), where N\mathcal{N} is the classical differential operator (Eq. (50)). A vanishing AD residual throughout Ω\Omega therefore implies N[h](x)=f(x)\mathcal{N} [ h ] (x)=f(x) throughout Ω\Omega, so hh belongs to the PDE solution set S\mathcal S.

[W2 & Q2–Q5] Reproducibility and Batch Sensitivity

  • Test grid and forward pass. For each benchmark in the main text, we generate a separate 100×100100\times100 evaluation grid for the error maps. All evaluation points are processed jointly in a single forward pass and form one fusion context.
  • BatchNorm statistics. For MLP+BatchNorm, we use PyTorch’s BatchNorm implementation with the mean and variance of the current batch during evaluation.
  • DCI point set. At each training iteration, we compute DCI on the same 2,800 collocation points used for the training objective, comprising 2,000 interior points and 800 boundary points. Both operator terms in Eq. (23) are evaluated on that same set, and DCI is recorded throughout training.

To address your concern about sensitivity to the inference context (which was also pointed out by the reviewer zdtj.), we added a controlled experiment on the Heat benchmark in Appendix H. For PIPN and MMET, we keep the trained weights and 100 evaluation points fixed and resample 1,000 context points in each of five inference runs. Both decoupled models retain a relative L2L_2 error below 1%1\% in all five runs, with mean errors of 9.40×10−39.40\times10^{-3} for PIPN and 7.68×10−37.68\times10^{-3} for MMET (Table 12). These results indicate that, after gradient decoupling, both models maintain their solution accuracy at fixed query points when the fusion context is resampled within the same domain.


Manuscript Changes

  • We added a proof in Appendix A.3 for Lemma 6.1.
  • We documented the evaluation grid, single-pass inference, BatchNorm statistics, and DCI point set in Appendix C.2.
  • We clarified the batch-consistency assumption in Contribution 4 and Section 6, added the context-resampling experiment in Appendix H, and identified a broader study of inference-batch dependence as future work in the conclusion.

Comments on the paper

3 comments
AuthorsOpenReview ↗

Consolidated Response to Reviewers and Concerns Regarding Evaluation Standards

Dear All Reviewers and AC,

We thank all reviewers for their comments. However, we must point out that several reviewers' assessments clearly deviate from the criteria for evaluating scientific contributions emphasized in the ICLR 2027 Reviewer Guidelines. Not only do these assessments fail to adequately consider the new knowledge revealed by our research and its potential impact, but they also use unreasonable demands beyond the core claims of our paper as grounds for dismissing its contributions. We believe that this approach to evaluation deserves reconsideration. Therefore, we provide a unified response to the relevant concerns and respectfully request the AC's attention.


[1] Regarding the significance of this research (Reviewer 7NaE)

We note that Reviewer 7NaE acknowledges the significance of our research in the strengths section (“The paper identifies a practically meaningful problem.”), but then states in the weaknesses section that “The most important weakness concerns where the core significance of the method lies.” We are puzzled by this contradictory assessment.

We would like to clarify that the problem revealed by our research is by no means something that “does not exist or has already been resolved.” On the contrary, we have already explicitly demonstrated in the related work and experimental sections of our paper that this failure mode exists in numerous published models, including highly cited works such as PIPN (JCP, cited by 226) and PINNsFormer (ICLR'24, cited by 241). There have also been sporadic observations of this phenomenon within the community (see our response to Reviewer 7NaE). However, no one has explicitly discussed the reasons behind it. Therefore, our contribution lies precisely in the first identification, formalization, and causal validation of this mechanism.

[2] Insufficient contribution because the mathematical principles are simple (Reviewers LWGR & 7NaE)

The ICLR 2027 Reviewer Guidelines explicitly state that contributions should be evaluated based on whether they bring new knowledge to the community or change established practices in the field, rather than the sophistication of the theories employed. Theory itself is merely an analytical tool. Therefore, in light of the discussion in [1], we believe that our work clearly meets the contribution criteria specified in the guidelines.

Conversely, if papers were evaluated solely based on the sophistication of their methods or theories according to the reviewers' standards, then numerous high-impact works, including the NeurIPS 2025 Best Paper (1000 Layers RL), should have been rejected, as they do not even involve mathematical analysis. Their core method is merely to scale reinforcement learning networks from the traditional few layers to over 1000 layers, an operation that anyone in the AI field knows how to perform.

[3] Additional discussions (batch dependence, MLP vs. fusion-based models, finite differences vs. automatic differentiation) (All Reviewers)

These topics could themselves serve as interesting directions for future work extending our paper, and we are also very willing to address the reviewers' questions within the rebuttal space constraints. However, these topics do not themselves strengthen our core claim, and expecting a single paper to thoroughly discuss all these supplementary topics is unrealistic, especially considering that our paper is already nearly 30 pages long and already includes extensive additional discussions (including engineering/theoretical-level decoupling, DCI sensitivity, inductive biases of fusion-based models, etc.). Meanwhile, almost every one of the above topics could independently constitute another ICLR paper.

[4] Regarding the reasonableness of the assumptions (Reviewer zdtj)

We believe that these assumptions are relatively mild in the context of our paper, and we have provided a direct metric for measuring the relevant assumptions, namely DCI. Our experiments demonstrate that these assumptions almost always hold.

[5] The counterexample in Appendix A.3 is incorrect (Reviewer LWGR)

We believe this is a clear factual error and highly suspect that it originates from an LLM hallucination. We respectfully request the AC's attention to this unusual issue.


Sincerely,

Authors of Submission 34564

Dear reviewers,

Thank you for your reviews. The author-reviewer discussion closes on November 18, so please respond to the authors' rebuttal before then. Please say whether it addressed your concerns, and update your score if your view has changed.

AuthorsOpenReview ↗

Summary of Manuscript Updates

Dear All Reviewers and AC,

We thank reviewer JYCx for conducting an emergency review and for the positive feedback, reviewers 7NaE and zdtj for their replies, and the AC for continuing to follow up. In response to the reviewers’ feedback, we have revised the manuscript to further address your main concerns. The updates are summarized below.


Theoretical Proofs

  • We upgraded Corollary 6.1 to Lemma 6.1 and added a proof in the new Appendix A.3 (reviewer JYCx).
  • We further emphasized the applicability of Assumption A.3 on line 758 (reviewer zdtj).

Experiments

  • We added Appendix H to examine and verify batch sensitivity through controlled experiments (reviewers JYCx and zdtj).
  • We added Appendix I to empirically evaluate the hybrid data- and physics-driven setting (reviewer 7NaE).
  • We added Appendix J to empirically verify the difference between finite differences and automatic differentiation (reviewer 7NaE).

Further Discussion

  • We added Section 6.3 to discuss finite differences as an alternative solution (reviewer 7NaE).
  • We qualified the assumption about batch sensitivity in both Contribution 4 and line 364 (reviewers JYCx and zdtj).
  • We added a discussion of future work to the conclusion in Section 8 (reviewer zdtj).

Reproducibility

  • We expanded the reproducibility details in Appendix C.2, including the size of the evaluation set and the batching used during inference (reviewers JYCx).

We thank all reviewers and the AC/SAC again for the time and effort you have devoted to the review process and for helping us improve the manuscript.

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

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