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Theoretical Limits and Sampling Guarantees for Machine-Learned Interatomic Potentials

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

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Abstract

Machine-learned interatomic potentials (MLIPs) accelerate molecular dynamics (MD) simulations by learning the energies and forces that govern atomic motion. Recent work shows that relaxing physical inductive biases can improve computational efficiency and predictive accuracy, raising the question of whether energy-and-force matching alone ensures accurate sampling. We show that the relationship between prediction error and sampling accuracy is exponentially ill-conditioned in dimension. In particular, prediction errors that decay exponentially with dimension can still coexist with nearly maximal total variation distance between the learned and target distributions. We identify two distinct failure mechanisms. The first is kinetic trapping: relaxation to an accurate learned equilibrium requires exponentially long times, even when simulations start from training configurations whose energies and forces are matched exactly. The second is equilibrium mismatch: the learned stationary distribution itself is far from the target. Under explicit assumptions, we show that equilibrium mismatch can persist in local, symmetry-preserving models, where small per-atom errors coexist with a distributional discrepancy that approaches its maximum as system size increases. Finally, we establish global energy-control conditions that ensure equilibrium accuracy and identify additional conditions needed for rapid relaxation.

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
Machine Learned Interatomic Potentials, Molecular Simulations, Langevin Dynamics, Sampling

Reviews

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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.
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Paper summary

The paper studies whether small errors in the energies and forces predicted by machine-learned interatomic potentials are sufficient for reliable molecular-dynamics simulations. The main analysis considers smooth potentials with forces derived from their energies, without imposing locality or invariance under translations, rotations, and permutations of identical atoms. The authors construct examples with small errors averaged over the reference equilibrium distribution, but whose simulations remain trapped for long times or approach an incorrect equilibrium. One example also reproduces every training energy and force exactly. Appendix H shows that, under the stated assumptions, local models invariant with respect to translations, rotations, and permutations of identical atoms can also produce an incorrect equilibrium distribution. The authors also give bounds on energy errors that guarantee an accurate equilibrium distribution and further conditions for convergence to it. Numerical examples use an Einstein crystal and a harmonic model of solid argon.

Critical strengths

The paper addresses an important question for atomistic simulations, i.e., how errors in predicted energies and forces affect simulation results. The authors work toward a formal understanding of this relationship through explicit mathematical examples. These examples show how small average prediction errors can coexist with simulations that remain trapped for long times or approach an incorrect equilibrium distribution. The examples also have clear physical interpretations, i.e., that artificial wells can trap trajectories, while underestimating the energy of a competing region can make the model favor the wrong equilibrium state.

Critical weaknesses

I appreciate the authors’ effort to formalize the relationship between prediction errors and simulation results. My assessment focuses mainly on the relevance of this work to atomistic simulations and the development of interatomic potentials. From this perspective, it remains unclear to me what new physical insight the results provide and how they could help us develop or assess these models.

W1. The mechanisms behind the presented results are well known, i.e., that errors in energy barriers can keep simulations trapped, while errors in relative free energies can make a model favor the wrong state. Although the authors show that these problems can occur even with very small average energy and force errors, it remains unclear to me what new physical insight this provides or how it could help us develop or assess interatomic potentials.

W2. I find it difficult to assess the physical significance of the reported differences between probability distributions. A total-variation distance approaching one does not necessarily mean that errors in quantities such as local structure or heat capacity per atom are large.

W3. Appendix H extends the analysis to local models, but the paper does not demonstrate this result for a concrete atomistic system. An example showing how a local potential incorrectly favors one atomic arrangement over another would make the physical meaning clearer.

W4. The discussion of electronic-structure failures needs clarification. The theorems do not address difficulties in generating reference data, and a calculation failing to converge does not mean that the underlying physical energy is undefined.

W5. It is unclear how the conditions in Theorem 4.6 could be used in practice. They require bounds on energy errors across all configurations, including those without reference data. The authors should explain how these conditions could guide the development or validation of interatomic potentials.

W6. Exponential convergence does not establish that equilibrium will be reached within a practical simulation time. Reaching equilibrium also does not guarantee accurate transition rates or transport coefficients. The authors should consider distinguishing these questions when discussing „dynamical accuracy“.

Questions for authors

My questions follow directly from the weaknesses presented above and would be answered by addressing them.

9 comments

We thank the reviewer for taking the time to carefully evaluate our work and for providing a thoughtful review from a physical perspective. We particularly appreciate their engagement with the physical significance. We address their questions below

W1. The mechanisms behind the presented results are well known, i.e., that errors in energy barriers can keep simulations trapped, while errors in relative free energies can make a model favor the wrong state. Although the authors show that these problems can occur even with very small average energy and force errors, it remains unclear to me what new physical insight this provides or how it could help us develop or assess interatomic potentials.

We would first like to clarify a point regarding the characterization of the mechanisms. Errors in energy barriers can either slow down or accelerate transitions, depending on their sign. We believe the reviewer is referring to the well-known physical principles that energy barriers govern metastability and relative free energies determine equilibrium populations. We agree that these principles are well understood in statistical mechanics. However, they do not directly establish anything about how energy and force RMSE affect the equilibrium distribution sampled or the dynamics through which it is reached.

Our contribution is to show that an unconstrained MLIP trained only through energy-and-force matching can admit potentials with arbitrarily small population errors yet fundamentally incorrect sampling behavior, and that these failures become exponentially more severe with the number of degrees of freedom. The physical insight is based on an energy-entropy effect (Remark 4.4), which makes energy and force errors an exponentially poor indicator of sampling accuracy in high dimensions. In a large system, the Boltzmann weight of a region depends exponentially on the number of atoms, through both its energy and its configurational volume. A model that is extremely accurate on the training data, but underestimates the energy by just a few kBTk_BT per atom in a large, rarely sampled region, can therefore shift almost all of the equilibrium probability into that region. Its energy and force errors on the training data stay tiny, and its forces remain physically reasonable, of order one per atom. Why such large regions are rarely sampled is discussed in our response to W4 below. Additionally, we examine which failure modes can be ruled out by explicitly incorporating common physical constraints, such as conservativity, locality, and symmetry, and which can still persist despite these constraints.

Regarding the significance for MLIP development, we believe understanding the role of physical inductive biases, the guarantees they provide, and their limitations is important for developing reliable MLIPs. In particular, whether future MLIPs should incorporate stronger architectural constraints or move towards more flexible, unconstrained potentials is an important open question in the MLIP community (Creed et al., 2026). Our results provide a theoretical perspective on this question by identifying the limitations of unconstrained energy-and-force matching and showing why conventional energy and force error metrics, even at the population level, can be misleading indicators of sampling reliability.

On the implications for assessing MLIPs, please see our response to Reviewer HjH2 (Practical interpretation) and the new Section 5 of the revised paper. In short, we suggest simple practical checks, beyond standard prediction metrics, to validate MLIPs and detect failures that affect physical property predictions.

W2. I find it difficult to assess the physical significance of the reported differences between probability distributions. A total-variation distance approaching one does not necessarily mean that errors in quantities such as local structure or heat capacity per atom are large.

We have addressed this concern in detail in our response above to Reviewer 9dG2. Our results not only show TV approaching one, but also demonstrate significant discrepancies in physically meaningful observables, including intensive structural quantities and displacement fluctuations.

W3. Appendix H extends the analysis to local models, but the paper does not demonstrate this result for a concrete atomistic system. An example showing how a local potential incorrectly favors one atomic arrangement over another would make the physical meaning clearer.

We have now added an atomistic example (Appendix A.4) using an fcc Lennard-Jones argon crystal with 108 atoms, following the construction of Theorem H.5. The constructed potential introduces a local energy correction that favors compressed nearest-neighbour bonds, configurations that are extremely rare under the true equilibrium distribution (mean descriptor value 1.9×10−61.9\times10^{-6} per site).

Despite this, the model achieves a per-atom energy MAE of only 6×10−5kBT6\times10^{-5}k_BT and a force RMSE of 4% of the reference force scale, with 79% of validation configurations reproduced exactly. Yet MD simulations produce a completely different atomic arrangement. 99–100% of atoms form short bonds, compared with none in the reference crystal, resulting in a dimerized solid with a new peak in the pair-distance distribution. This state is reached from two different initializations and persists in a larger 256-atom system.

We have also added a second example with a trained model in Appendix A.6. NequIP, an equivariant GNN trained on alanine dipeptide, develops an unphysical energy well outside the training data that drives the molecule into a collapsed arrangement absent from the reference, despite small validation errors. A correction enforcing condition (a) of Theorem 4.6(ii) outside the data removes this failure, with validation error unchanged.

W4. The discussion of electronic-structure failures needs clarification. The theorems do not address difficulties in generating reference data, and a calculation failing to converge does not mean that the underlying physical energy is undefined.

We believe there may be a slight misunderstanding of the point we are making. For a system of 'N' atoms, the configuration space is R3N\mathbb{R}^{3N}, and obtaining reliable reference data throughout this space is practically infeasible.

Consider even a simple molecule such as N2N_2, with bond length as its only internal degree of freedom. Although the bond length can vary over (0,∞)(0,\infty), training data may cover only a limited range, say 1-2 A˚\mathring{A}. We cannot expect an unconstrained neural network trained on this data to predict accurate energies and forces uniformly over all possible bond lengths. Classical force fields address this partly through physical priors, such as harmonic bond potentials and short-range repulsion, which discourage excursions into poorly sampled configurations.

More importantly, we do not necessarily need accurate energy predictions everywhere. If we have approximate physical knowledge of configurations the dynamics should avoid, we can impose repulsive priors or sufficiently high energy barriers to strongly suppress visits to those regions, while maintaining accurate predictions where reliable training data are available. This is also the motivation behind the one-sided energy conditions in Theorem 4.6(ii). Physically, this can be understood as an energy-entropy competition. Poorly sampled regions have enormous configurational volume in high dimensions, and underestimating their energies can give them disproportionately large equilibrium probability. Appropriate physical priors can help prevent this by keeping these regions energetically unfavourable.

The difficulty becomes much greater in the 3N-dimensional configuration space of larger systems. Our point is that limited training-data coverage cannot guarantee uniformly accurate predictions, but appropriate constraints can help control behavior outside the sampled region. This argument concerns the availability and coverage of reference data, not whether the underlying physical energy is defined.

W5. It is unclear how the conditions in Theorem 4.6 could be used in practice. They require bounds on energy errors across all configurations, including those without reference data. The authors should explain how these conditions could guide the development or validation of interatomic potentials.

We have partly addressed this concern in our response to Reviewer 9dG2. While verifying global energy-error bounds is difficult in practice, Theorem 4.6 provides a theoretical guide for developing physical constraints that control the learned potential in poorly sampled regions, without requiring accurate predictions everywhere (see our new NequIP example on alanine dipeptide, Appendix A.6). It also suggests a simple practical check for validating MLIPs beyond RMSE and MAE. Because, by Theorem 4.6(ii), a model that is accurate where the system spends most of its time can shift the equilibrium only by underestimating the energy elsewhere, the sign of the energy error along the model’s own trajectories is a useful diagnostic (please see our response to Reviewer HjH2, Validation).

W6. Exponential convergence does not establish that equilibrium will be reached within a practical simulation time. Reaching equilibrium also does not guarantee accurate transition rates or transport coefficients. The authors should consider distinguishing these questions when discussing „dynamical accuracy“.

The main point here is that, even as the force RMSE approaches zero, the learned potential can take much longer to equilibrate than the true system, and this gap grows with the degrees of freedom. The reason exponential timescales come up is that, for the Einstein crystal, Langevin dynamics under the true potential is known to equilibrate in at most polynomial time in the number of degrees of freedom of the crystal (Cheng et al., 2018). Here, we show that the learned potential can instead remain trapped for exponentially long times, even with arbitrarily small force errors. This establishes a large separation between the equilibration times of the true and learned systems. In physical terms, an MLIP can predict forces almost perfectly yet take much longer to equilibrate than would normally be expected for that system. Moreover, this trapping can be difficult to detect, since standard observables may appear stable and converged even though the system has not reached the correct equilibrium distribution. Accurate transition rates and transport coefficients are a separate, stronger requirement that require a different analysis that we do not address here.

We look forward to further discussion, and to improving the manuscript and its accessibility to physical scientists based on your feedback.

References

Creed, I., Rein, T., et al. Six open questions in machine-learned interatomic potential foundation models. arXiv preprint arXiv:2606.07327, 2026.

Cheng, X., Chatterji, N. S., et al. Underdamped Langevin MCMC: A non-asymptotic analysis. Conference on Learning Theory (COLT), PMLR 75:300–323, 2018.

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Paper summary

The paper argues that arbitrarily small errors in energies and forces can still result in bad sampling behaviour in MLIP-based molecular dynamics through a theoretical analysis. This is based on previous work on Langevin dynamics with learned score functions by Cao et al. The authors identify two failure mechanisms: kinetic trapping and equilibrium mismatch. Experiments on an Einstein crystal and harmonic FCC argon are used to illustrate the mechanisms. Based on the analysis, the authors propose additional conditions that ensure better sampling behavior.

Critical strengths

This is a relevant topic to the atomistic modeling community, even if the practical impact of this work is not immediately clear

The writing is clear and mostly accessible

The proofs appear technically sound

Theorem 4.6(ii) gives a concrete design target, even though it is unclear how it could be enforced in practice

Critical weaknesses

Novelty: A large part of the paper is based on work by Cao et al. It would be useful if the authors could make clear which arguments and constructions are taken from Cao et al. and which ones are novel.

In Section 2, the authors state that Theorem 4.3 “strengthens the asymptotic separation from 1−ε1-\varepsilon to 1−e∧{−Ω(d)}′′1-e^{\wedge}\{-\Omega(d)\}^{\prime \prime}” but these theorems have completely different structures. Cao et al.’s theorem 3.11 works at any fixed dimension and arbitrarily small errors, whereas theorem 4.3 in this work requires d→∞d \to \infty with an error tied to the dimension and stronger assumptions (F.1 and F.2).

Connection between experiments and theory: The Einstein crystal experiment uses a soft well, while the theorems ask for a stiff well. It appears the argon networks escape the crystal basin rather than getting trapped near the training data.

Questions for authors

Could the authors state which constructions and lemmas are adapted from Cao et al. and what specifically fails when their overdamped argument is applied to kinetic Langevin?

How relevant is it that the actual training setup does not sample from the true Boltzmann distribution necessarily? Remark E.2 suggests the trapping mechanism extends to other training distributions, but commonly used schemes like rattling structures, active learning, etc. deliberately cover off-equilibrium regions.

Any arguments or evidence that a realistic architecture and optimizer (equivariant neural network + SGD) would ever reach such solutions?

Condition a) in Theorem 4.6(ii) requires a global upper bound on the true energy, which is unknown in practice. How could one verify and/or enforce this condition?

Several works in the score-matching literature already discuss related failure modes and remedies (as discussed in Cao et al.), for example Lee, Lu, and Tan (2022), Koehler and Vuong (2024), Koehler, Lee, and Vuong (2025), and Song and Ermon (2019). Could the authors please engage with this literature and clarify how their results relate to it (especially what is specific to the MLIP setting).

Is total variation (TV) the right metric? It feels overly aggressive and easy to break in high dimensions. Could the results (esp. Thm. 4.6) be stated in intensive quantities? Some of the positive results degrade with system size and the negative results would be more convincing.

3 comments

We thank the reviewer for their assessment. We address their questions below.

Novelty and connection to overdamped Langevin dynamics: Cao et al. (2026) study first-order overdamped Langevin dynamics in score-based sampling, whereas our work concerns molecular dynamics governed by second-order kinetic Langevin equations driven by an MLIP. We elaborate on our new theoretical contributions and their relationship to overdamped dynamics in our responses below.

Could the authors state which constructions and lemmas are adapted from Cao et al.?

One of the mechanisms we study, kinetic trapping (Theorems 4.1/4.2), shares some technical ingredients with Cao et al., including the placement of confining traps in regions of exponentially small target probability, smooth radial cutoffs and standard Gaussian concentration arguments. However, extending these arguments to kinetic dynamics requires a different proof, since inertia changes the short-time dynamics (as discussed in our response to the next question). Our main technical contributions are:

  • A new hypoelliptic exit-time bound for kinetic Langevin dynamics (Lemma C.1)
  • Simultaneous control of energy and force errors under a conservative force field, including exact energy–force interpolation of the training set (Theorem 4.2)
  • A conservative equilibrium-mismatch construction (Theorem 4.3)
  • An extension to local, permutation-invariant, and E(3)-invariant potential classes (Theorem H.5)
  • Sufficient conditions for equilibrium accuracy and relaxation (Theorems 4.6 and I.1)

What specifically fails when their overdamped argument is applied to kinetic Langevin?

In overdamped dynamics, the process inside the trap is an Ornstein-Uhlenbeck process in position, which can be controlled directly. In kinetic dynamics, the position evolves through a coupled position-velocity system governed by the Green's function of a damped harmonic oscillator. Large initial velocities can therefore produce substantial transient displacements before friction dominates. The key estimate is a hypoelliptic exit-time bound, which we establish in Lemma C.1.

Our constructions must also control both energy and force errors, rather than score errors alone. For example, Cao et al.'s construction has incorrect scores at every training configuration, which empirical force matching in MLIPs would penalize directly.

How relevant is it that the actual training setup does not sample from the true Boltzmann distribution necessarily? Remark E.2 suggests the trapping mechanism extends to other training distributions, but commonly used schemes like rattling structures, active learning, etc. deliberately cover off-equilibrium regions.

The trapping mechanism is not specific to Boltzmann-distributed training data. For any training distribution ν\nu, a perturbation confined to a region of exponentially small ν\nu-mass has exponentially small energy and force error under ν\nu, yet can still cause trapping. Rattling and active learning improve coverage but cannot guarantee sufficient coverage of every region in high dimensions.

On-the-fly active learning can detect trapping wells like those in Theorems 4.1 if trajectories visit them and the errors are flagged. However, it may miss errors that prevent trajectories from entering certain regions. For example, an overestimated energy barrier in a poorly sampled region can leave predictions accurate wherever the dynamics visits while exponentially slowing transitions. The equilibrium distribution can still remain close to the target under the conditions of Theorem 4.6(ii).

Any arguments or evidence that a realistic architecture and optimizer (equivariant neural network + SGD) would ever reach such solutions?

Our results are existence results (as described in Introduction and Conclusion) and characterize what the energy-and-force matching objective permits, independently of the architecture or optimizer. Which solutions SGD reaches for equivariant networks is an open problem (Vardi, 2023), with theory largely limited to linear equivariant networks (Lawrence et al., 2022). Nevertheless, several observations support the practical relevance of our findings:

  • In our new example (Appendix A.6), NequIP trained on alanine dipeptide fails in MD for both seeds despite nearly identical validation errors. One seed develops an unphysical well 34-44 kBTk_BT below the physical structure, in bond-stretching directions absent from the data, analogous to Theorem 4.3. Enforcing condition (a) of Theorem 4.6(ii) outside the data, with validation error unchanged, prevents failure in all 192 replicas.

  • In our argon experiments (Appendix A.2), networks with energy errors of about 0.003 kBTk_BT per atom still escape the crystal basin. Figure 3 shows that errors stay small on the data, but just outside it the learned energy drops by thousands of kBTk_BT while the true energy rises. This persists with more data, longer training and smaller time steps.

  • Universal MLIPs systematically soften potential-energy surfaces (Deng et al., 2025), consistent with the underestimation in Theorem 4.3, and models with low force errors can still give unstable simulations or wrong properties (Fu et al., 2023; Mannan et al., 2026).

While these observations do not prove that trained models reach our constructions, they show that the mechanism our theory isolates, small errors on the data with energy underestimation away from it, occurs in trained models.

Condition a) in Theorem 4.6(ii) requires a global upper bound on the true energy, which is unknown in practice. How could one verify and/or enforce this condition?

For verification, Theorem 4.6(ii) shows that, when a model is accurate in regions where the true system spends most of its time, a shift in equilibrium requires the model to underestimate the energy elsewhere. The sign of the energy error along the model's own trajectories is therefore a useful diagnostic. (please see our response to Reviewer HjH2, Practical interpretation: Validation, and Section 5).

For enforcement, we see two promising directions.

  • Impose physical constraints locally, using approximate physical knowledge, such as short-range repulsive baselines from classical physics or the coercive baselines explored in our argon experiments.
  • Use targeted sampling to identify regions where the learned potential significantly underestimates the true energy.

While neither approach guarantees the global condition in Theorem 4.6(ii), our result provides a mathematical target for developing and evaluating such safeguards.

Several works in the score-matching literature already discuss related failure modes and remedies (as discussed in Cao et al.), for example Lee, Lu, and Tan (2022), Koehler and Vuong (2024), Koehler, Lee, and Vuong (2025), and Song and Ermon (2019). Could the authors please engage with this literature and clarify how their results relate to it (especially what is specific to the MLIP setting).

We have now added a paragraph in Section 2 discussing the relevant score-matching literature and their connection to force learning in MLIPs.

Is total variation (TV) the right metric? It feels overly aggressive and easy to break in high dimensions.

TV could be a strong metric in high dimensions, though standard in robustness analysis. Our constructions, however, also produce discrepancies in physically meaningful observables.

  • For Theorem 4.3, W2(π^,πtar)=Ω(d)W_2(\hat{\pi}, \pi_{\mathrm{tar}}) = \Omega(\sqrt{d}), corresponding to an Ω(1)\Omega(1) per-atom RMSD and hence a structurally different equilibrium state (Remark F.4).

  • The trapping constructions in Theorems 4.1 and 4.2 produce incorrect local displacement fluctuations, as illustrated by the phonon frequencies and Debye–Waller factors in Fig. 1b and Table 3.

  • Theorem H.5 implies an order-one discrepancy in an intensive structural observable, the fraction of atoms in decoy environments, even as system size increases.

Could the results (esp. Thm. 4.6) be stated in intensive quantities? Some of the positive results degrade with system size and the negative results would be more convincing.

Appendix I now gives an intensive version of Theorem 4.6 (Theorem I.1). It establishes:

  • bounds on per-atom free-energy and relative-entropy errors
  • a bound on the normalized Wasserstein distance
  • bounds on errors in intensive physical observables
  • conditions under which kinetic Langevin dynamics converges at a rate independent of system size.

Connection between experiments and theory: The Einstein crystal experiment uses a soft well, while the theorems ask for a stiff well. It appears the argon networks escape the crystal basin rather than getting trapped near the training data.

  • Einstein Crystal: The stiffness condition in Lemma C.1 is sufficient but not necessary. The exponential trapping rate is governed by s2=αR2/ds^2=\alpha R^2/d (twice the well depth at the exit radius, in units of kBTk_BT per degree of freedom), rather than by stiffness alone. To verify this, we simulated the trap of Theorem 4.1 with stiffnesses α=0.066\alpha=0.066, 11, and 1212 (relative to the target curvature), choosing the exit radius as R=sd/αR=s\sqrt{d/\alpha} (new Fig. 5). In all three cases, the mean exit time grows as ecde^{cd}, with nearly identical fitted rates of 0.4400.440, 0.4480.448, and 0.4360.436 at s2=3s^2=3, close to the large-deviation prediction of 0.4510.451. Stiffness primarily affects the prefactor. The soft well in Fig. 1a also has exit radii scaling as d\sqrt{d}, keeping s2s^2 fixed and placing it in the same exponential trapping regime.

  • FCC Argon: The argon experiment is not intended to demonstrate kinetic trapping, which is illustrated by the Einstein crystal, as stated in Section A.2. Instead, it illustrates a violation of condition (a) of Theorem 4.6(ii): the unconstrained training objective does not control the learned energy away from the data, allowing it to fall below the true energy in these regions. The new Fig. 3 provides evidence of this behavior (please see our response to Reviewer HjH2). Energy errors remain at their typical levels until a walker reaches the boundary of the training data, beyond which the learned energy drops by thousands of kBTk_BT while the true energy rises.

  • Alanine dipeptide (new Appendix A.6): In our new example with NequIP, an equivariant GNN trained on alanine dipeptide, one of the two seeds does get trapped. Replicas fall into an unphysical energy well outside the training data, 34-44 kBTk_BT below the physical structure, and never leave within 1 ns. This is analogous to the mechanism of Theorem 4.3, and a correction enforcing condition (a) of Theorem 4.6(ii) outside the data removes it.

In Section 2, the authors state that Theorem 4.3 “strengthens the asymptotic separation from to ” but these theorems have completely different structures. Cao et al.’s theorem 3.11 works at any fixed dimension and arbitrarily small errors, whereas theorem 4.3 in this work requires with an error tied to the dimension and stronger assumptions (F.1 and F.2).

We agree that "strengthening" suggests a direct comparison between results with different mechanisms and structural requirements, and may also have obscured the novelty of our own results. Our intention was to emphasize that our construction preserves conservativity and admits a well-defined Gibbs equilibrium, unlike the non-gradient drift construction of Cao et al. (Remark 4.5). We have revised the wording accordingly.

For the practical interpretation of our results, please also see our response to Reviewer HjH2 (Practical interpretation) and the new Section 5 of the revised paper.

References

Cao, D. Y., Chen, A. Y., et al. On the robustness of Langevin dynamics to score function error. ICML, 2026.

Lawrence, H., Georgiev, K., et al. Implicit bias of linear equivariant networks. ICML, PMLR 162, 2022.

Vardi, G. On the implicit bias in deep-learning algorithms. Communications of the ACM, 66(6):86–93, 2023. Deng, B., Choi, Y., et al. Systematic softening in universal machine learning interatomic potentials. npj Computational Materials, 11,9, 2025.

Fu, X., Wu, Z., et al. Forces are not enough: Benchmark and critical evaluation for machine learning force fields with molecular simulations. TMLR, 2023.

Mannan, S., Bihani, V., et al. UniFFBench: Evaluating universal machine learning force fields against experimental measurements. Nature Computational Science, 6:894-906, 2026.

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Paper summary

This paper investigates whether small energy- and force-matching errors guarantee accurate sampling with machine-learned interatomic potentials. Through explicit worst-case constructions, it establishes two distinct failures: exponentially long kinetic trapping despite an accurate stationary distribution, and a stationary distribution nearly maximally separated from the target in total variation. The principal constructions preserve smoothness, conservativity, and dimension-independent Hessian bounds. The training-data construction additionally achieves exact energy and force interpolation at configurations used for initialization. The paper also provides sufficient global energy-control conditions for equilibrium accuracy and additional assumptions for exponential relaxation. Conditional local and symmetry-preserving extensions and controlled numerical illustrations supplement these results.

Critical strengths
  1. The separation between kinetic and equilibrium failures is meaningful. The paper establishes that the trapping constructions have stationary distributions close to the target, showing that accurate equilibrium and efficient finite-time sampling require distinct safeguards.

  2. The counterexamples satisfy substantive constraints. Smoothness, conservativity, bounded curvature, and exact interpolation exclude several straightforward explanations for failure. Theorem 4.3 further demonstrates equilibrium mismatch while retaining a normalizable Gibbs distribution and ergodic dynamics.

  3. The scope is generally stated carefully. The authors distinguish worst-case existence results from practical prevalence and explicitly acknowledge that the experiments illustrate finite-time behavior rather than instantiate every theorem assumption.

Critical weaknesses
  1. The implications for practical MLIP modeling remain largely qualitative. Sections 4.3–4.4 discuss competing structures, repulsive priors, and the distinction between confinement and global energy comparison. These are useful connections. However, the paper leaves limited guidance on how this distinction should change validation or prior design for a specific atomistic application beyond the controlled harmonic examples. The authors appropriately identify broadly enforceable energy control as an open problem; this acknowledged gap nevertheless limits the current practical reach of the positive guarantees.

  2. The numerical evidence provides limited information about the learned energy landscape responsible for failure. The Einstein-crystal example directly illustrates trapping. In contrast, Figure 2(a) shows small held-out force errors alongside increasing finite-trajectory sampling discrepancy and eventual escape in harmonic argon. Appendix A.3 correctly states that this is not a direct verification of Theorem 4.3. The remaining empirical connection to the theory is therefore qualitative: the reported diagnostics do not directly characterize how the learned potential differs from the reference along the escape trajectories. Such information would strengthen the proposed connection to off-distribution energy-landscape errors without requiring a claim about stationary behavior.

  3. Energy accuracy and optimization convergence are incompletely documented. The argon experiments report held-out force errors without corresponding energy-error results, leaving the simultaneous energy–force accuracy premise insufficiently documented numerically. Appendix A.2 specifies 30,000 optimization steps with batch size 4096, but provides no convergence diagnostics for the dataset-size sweep. Figure 2(b) is explicitly restricted to the tested training protocol; the unresolved question is whether its limited improvement with additional data persists after adequate optimization. Fixed update counts alone establish neither convergence nor undertraining.

Questions for authors
  1. Practical interpretation. Building on the discussion of competing structures and repulsive priors in Sections 4.3–4.4, could the authors give a focused example of how the analysis would inform a specific validation or modeling choice in an atomistic application beyond the harmonic examples? A discussion is sufficient; a new large-scale benchmark is not necessary. As a supplementary scope clarification, it would also help to distinguish implications for configuration coverage within a given chemical system from implications for coverage across compositions.

  2. Energy errors during trajectory escape. Since the harmonic argon reference potential is known analytically, could the authors compare the learned and reference energies along a representative trajectory before and during escape? This would help assess how potential errors outside the training distribution relate to the observed instability, without interpreting escape as evidence of an incorrect stationary distribution.

  3. Joint prediction accuracy and convergence. Please report the held-out energy errors alongside the force errors, with normalization specified. Under the reported training protocol, what evidence indicates adequate optimization across the dataset-size sweep? Learning curves or an extended-training check for the largest dataset would help assess whether the prediction errors and sampling diagnostics have stabilized.

  4. Time-step robustness. Appendix A.2 reports a BAOAB time step of 10 fs for the harmonic argon simulations. Do the observed escape behavior and sampling discrepancies persist with a smaller time step, using the same trained model and physical simulation duration? A check on a representative large system would help assess the contribution of numerical integration error to the reported failures.

1 comment

We thank the reviewer for their assessment. We have addressed all three empirical concerns and added a discussion on the practical interpretation of our analysis and theoretical results. Please find our responses below

Practical Interpretation: Our results suggest four considerations for developing and validating MLIPs:

  • Validation: By Theorem 4.6(ii), the equilibrium can go wrong only if the model is inaccurate where the system spends most of its time, or underestimates the energy elsewhere. MAE and RMSE hide biases because they ignore whether energies are overestimated or underestimated and how errors change over time. Our analysis shows that small, systematic underestimation along parts of an MD trajectory can change relative Boltzmann weights and hence physical properties. Instead of validating randomly sampled frames from a trajectory, we suggest sampling frames at regular intervals and plotting the signed error against simulation time to identify systematic underestimation.

  • Simulation stability: A stable MD simulation with small prediction MAE is often taken as evidence of physical accuracy. Surprisingly, our results show that this can be misleading when competing structures are possible. Our new argon example (Appendix A.4) illustrates this. Despite an energy error of just 2×10−42\times10^{-4} meV/atom, the constructed potential produces a stable, dimerized solid instead of the correct fcc crystal.

    A simple check is to compare relative energies when a simulation transitions between different structural states. Even if prediction errors in both states are small, they can cancel or add up when taking their difference. Since relative Boltzmann weights depend exponentially on energy difference, a small error in the difference alters which structures are favored. For simulations involving structural transitions, the error in relative energies are more informative than individual energy errors.

  • System-size effects: For local models, per-atom errors stay the same as the system grows, but the equilibrium error can grow exponentially with the number of atoms (Remark H.8). The reason is that the error can be small on the configurations used for validation, while a per-atom energy under-estimation for a competing structure is multiplied by the number of atoms. It can be negligible in a small cell and add-up in a large one. Our results suggest additional observable-based validation should also be done at the size used in production.

  • Independent runs: Kinetic trapping can occur even without energy underestimation, making trajectories appear converged when they are not. Comparing observables across simulations started from different configurations can help detect such failures.

Composition: Our theorems concern coverage within a single chemical system. Other compositions do not cover its configurations directly. However, for local MLIPs, similar local atomic environments can occur in different compositions, so data from one material can improve predictions for another.

Energy errors during trajectory escape: We tracked the true and learned energies along 2,304 trajectories (4 models, N = 128, 3 ns). The 15 walkers that escaped had normal energy errors until they reached the edge of the training data. Beyond it, the true energy rose above 1,000 k_BT within picoseconds, while the learned energy fell by thousands of k_BT (Figure 3). The model badly underestimates the energy just outside the data, and the walkers drift away.

Joint prediction accuracy and convergence: Below are the errors on 8,000 test samples

NNnnForce RMSE (eV/Å)Energy RMSE (meV/atom)
1610k2.6×10−42.6\times10^{-4}0.005
6440k7.6×10−47.6\times10^{-4}0.008
11270k1.05×10−31.05\times10^{-3}0.008
12880k1.14×10−31.14\times10^{-3}0.008

We trained on the largest dataset (500k samples) for 200k steps and the errors didn’t change, and walkers from all four models still escaped.

Time-step robustness: We reran the simulations with a 1 fs time step using the same trained models and simulation length. The number of escaping walkers is unchanged within statistical error (16/2304 at 1 fs vs. 15/2304 at 10 fs), and the median escape time is similar (1.9 vs. 1.65 ns).

Comments on the paper

7 comments

Thank you for the response and for acknowledging the additional analyses. As is standard for theory papers, our main contribution is the analysis in the main text, and the appendix experiments are intended as controlled illustrations of it. We also appreciate the reviewer highlighting the strengths of our theoretical contribution in their initial review, including the substantive constraints our constructions satisfy, and noting in Question 1 that “a discussion is sufficient; a new large-scale benchmark is not necessary.”

We would also like to note that the question we study is theoretical. Our results are existential and characterize what the energy-and-force matching objective permits, how this changes when physical constraints such as conservativity, locality and symmetry are imposed, and what is required to guarantee accurate sampling. As stated in the Introduction, “Our results are adversarial/worst-case in nature. They do not imply that any particular MLIP fails. Rather, they show that the learning objective does not preclude such failures.” We would therefore be grateful if the reviewer could assess the paper based on its primary theoretical contribution.

We nonetheless agree that an additional example with a GNN MLIP would strengthen the connection to practice. We will try to run an experiment on a GNN architecture, NequIP, and use our analysis to identify the relevant energy-landscape error. Given the limited time remaining in the discussion period, a complete study, including a targeted correction and testing whether it improves sampling and physical observables compared with the original model, may not be possible. We will report whatever results we obtain here. In the meantime, we would be glad to address any concerns the reviewer might have about the theorems, proofs, or main text.

As promised, we report the GNN example suggested by the reviewer, now added as Appendix A.6 (full setup, protocol and statistics are given there).

Setup: We trained NequIP on the alanine dipeptide data of Fu et al. (2023) (two seeds, two checkpoints each) and ran 48 independent 1 ns Langevin replicas per model at 300 K, following their protocol.

Failure: Both seeds fail, at both checkpoints and in very different ways, although their validation errors are nearly identical (force MAE 51–52 meV/Å). Seed 0 collapses into a compact structure with heavy-atom bonds far outside the training range, while seed 1 collapses within picoseconds and then breaks apart.

Diagnosis: By Theorem 4.6(ii), a model accurate on the data can shift the equilibrium only by underestimating the energy outside it. Because the reference holds all bonds rigid, the training data contain no bond stretching, and this is where the learned energy is too low. Seed 0 has an unphysical energy well, absent from the reference, 34-44 kBTk_BT below the physical structure, analogous to the mechanism of Theorem 4.3. For seed 1, energy minimization does not converge, with the energy falling below -1,271 kBTk_BT relative to the physical structure.

Correction: We add a flat-bottomed wall, built only from the training data, that is exactly zero over the distances seen in training and rises steeply outside them, imposing condition (a) of Theorem 4.6(ii) where the data run out. Validation error is unchanged by construction.

Results: Full results are in Tables 6 and 7 in Appendix A.6. The table below reports the fraction of collapsed replicas and the Jensen–Shannon (JS) divergence of the backbone-angle distribution from the reference:

ModelCollapsed (no wall → wall)JS to reference (no wall → wall)
Seed 0, epoch 398% → 0%0.090 → 0.033
Seed 0, epoch 3246% → 0%0.069 → 0.019
Seed 1, epoch 3100% → 0%0.579 → 0.019
Seed 1, epoch 32100% → 0%N/A → 0.014

With the wall, none of the 192 replicas fails, and the spurious αL\alpha_L population is removed. As Theorem 4.6(ii) predicts, the wall does not correct the model's error on the data. Seed 0 still over-favours αR\alpha_R, and all models remain above the reference sampling floor (JS 0.005).

This experiment has several important limitations, and many further ablations are possible, so we present it only as an illustration. We would again like to emphasize that, as stated in the manuscript, our paper is theoretical, and its results hold independently of this experiment, since they concern the population-level learning objective rather than any particular trained model. We hope this addresses the reviewer’s remaining concern, and we would be glad to address any further questions about the theorems, proofs, or main text.

AuthorsOpenReview ↗

Summary of Discussion

We would like to thank all reviewers for their assessments. We would especially like to thank Reviewers FVkt and HjH2 for their engagement during the discussion period. We appreciate that all reviewers recognized the value of our theoretical contributions and did not raise any fundamental concerns about the main results. While we had hoped for a more detailed technical discussion of the theorems and proofs, we understand that our paper lies at the intersection of sampling, learning theory, and atomistic ML, which may make it challenging to evaluate from any single disciplinary perspective. We hope that the Area Chair and reviewers will consider the value of our theoretical results and the foundational understanding they provide. We summarize the discussion below:

Reviewer HjH2: The reviewer recognized the significance of separating kinetic trapping from equilibrium mismatch and the substantive mathematical constraints satisfied by our theorems. They initially raised concerns about the convergence and robustness of the illustrative experiments in the appendix and requested a discussion of the practical implications. We provided additional analyses and added a new discussion section, after which the reviewer acknowledged that their earlier concerns had been resolved. They subsequently requested an additional study involving a representative GNN-based MLIP to diagnose simulation failures, design a targeted correction, and evaluate improvements in sampling and physical observables. We carried out this study using NequIP on alanine dipeptide and added the results to the revised manuscript (Appendix A.6), but have not received a further response from the reviewer.

Reviewer 9dG2: The reviewer recognized the relevance of our work, the technical soundness of the proofs, and the concrete design target provided by Theorem 4.6(ii). Their main concerns were about the relationship to prior work in the generative modeling literature, the connection between theory and illustrative experiments, the relevance of Boltzmann-distributed training data, and the physical significance of total variation distance. We clarified our new theoretical contributions and explained why the arguments from the score-matching literature cannot be directly extended to kinetic Langevin dynamics in MLIPs. We also added experiments verifying exponential trapping across different well stiffnesses, provided additional evidence from trained MLIPs, clarified the applicability of our trapping results to other training distributions, and established a new theorem providing guarantees for intensive physical quantities. All these changes have been incorporated into the revised manuscript, but we have not received a response from the reviewer.

Reviewer FVkt: The reviewer recognized the importance of the problem and the value of formally understanding the relationship between prediction errors and sampling accuracy. They raised six concerns regarding the physical significance of our results, their applicability to local MLIPs, the feasibility of reference-data coverage, the practical interpretation of our sufficient conditions, and the distinction between equilibration and dynamical accuracy. We addressed all six concerns through detailed explanations, additional theoretical clarifications, a new atomistic example demonstrating equilibrium mismatch with a local potential, and an experiment using NequIP on alanine dipeptide.

The reviewer acknowledged our responses and subsequently questioned the significance of theoretical results and design targets that may not directly lead to new practical method or improvements over existing approaches. We clarified that advancing understanding of learning objectives, their limitations, and their mathematical guarantees in a predominantly empirical field is an important theoretical contribution even without new architectures or improvements in state-of-the-art empirical performance, and that such work falls within the scope of ICLR.

The reviewer later acknowledged the value of our theoretical results and clarified that their assessment was primarily from the perspective of atomistic simulations and MLIP development. They raised further questions about the relevance of Boltzmann-distributed training data, the effectiveness of broader sampling, and additional insights from the analysis. We addressed these questions by clarifying the applicability of our results to other training distributions, the limitations of improved data coverage in high-dimensions, and the quantitative theoretical insights underlying our practical recommendations. We also clarified that our paper was submitted under Probabilistic Methods / Sampling as its primary area, reflecting its focus on the theoretical foundations of sampling with learned potentials. The discussion took place only during the final two days of the discussion period, and we have not received a further response from the reviewer to our latest clarifications.

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