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- Informativeness
- 2
- Presentation
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- Soundness
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Paper summary
This paper studies the notion of including real (ground truth; correct) state information back into a model during autoregressive simulation. Studying PDE style problems such as Rayleigh-Benard, acoustics, and several others, it analyzes a very interesting phenomenon where inserting true data into a model during autoregression can actually have deleterious effects. Perhaps helping immediately, it can have a degrading effect longer term as the model rolls out -- or vice versa. The paper provides a theoretical justification (or "existence proof") of this phenomenon even in the most restricted and perhaps counterintuitive case. It then proceeds with an empirical evaluation in several settings.
Critical strengths
- The paper addresses a relevant problem in the field, with autoregressive deep learning approaches being increasingly used as surrogate models for complex physical phenomena. The notion of data assimilation is also interesting and relevant and deserves study, as its implementation can have counterintuitive impacts.
- Providing theoretical justification for a counterintuitive phenomenon, and then following it up with empirical evidence, is a strength. I have a bit of confusion about both the analysis and the connection between theory and experiments as will be shown below; however, this is still a strength because the hypothesis behind the paper is indeed not obvious on its face.
- The paper is generally well organized and well written.
Critical weaknesses
- As mentioned in the Strengths and below, I find the analysis a bit confusing. In a vacuum, the analysis is written clearly and is easy to follow. However, it is unclear how the error dynamics can be treated in a linear fashion and are completely decoupled from nonlinear simulators. I see this with my own eyes and yet for some reason have trouble believing this actually translates to the real problems that are studied in later sections. Perhaps I am just missing something, or perhaps a quick intuitive explanation of this de-coupling (along with the analysis itself) woudl remedy the issue.
- The paper is relatively thorough in terms of benchmarks. However, it is unclear how the methods and/or results "scale" (generalize?) to other simulator architectures.
- It is also unclear if there is a direct (for example monotonic) relationship between how "good" the simulator is and how the corrector dynamics work.
Questions for authors
- It is unclear how the theoretical justification (proof of universal linear compatibility) relates to the problem at hand. The paper does relatively well to then state a more relevant question, eventually arriving to equation (6). This is all well and good but I am still getting lost because the whole discourse is about proving that harm can be done even on exact linear dynamics, with the implication that this of course holds of inexact and/or nonlinear dynamics. However, what does this theory have to do with actually correcting the harm? I suppose this is a proof of the existence of (non)harm, and then seeks to find average case harm. But all of this is in the linear case, which does not seem to be relevant for most machine/deep learning problems.
- At the end of section 2, I believe there is an attempt at answer to the previous point, re: "misspecified learned simulator" and an empirical repair test. What is a misspecified learner? This begs a larger question regarding the approximations of a deep learner: do the paper's conclusions depend on how well a learner has represented the problem? Put in a more simple way, what is the impact of a model's natural prediction error? I assume that more erronous models might be more harmed by corrections than those that are nearly perfect. But is a well-trained and architected model still "misspecified" in the way the authors lay it out? I believe I am missing (or misunderstanding) something fundamental about this approach. The model/simulator itself only "shows up" in the analysis wherever is (e.g. or other variants of ). It is interesting and confusing to me how the analysis could then proceed without "worrying" about . The analysis in section 2 uses predictions (outputs) of the model (which of course become inputs to the model later), such that everything can be linear in , or , or , etc. For some reason this seems like a slight-of-hand, as an of the subsequent predictions are then nonlinear maps from , which are previous . In other words, the analysis depends entirely on (a) the model's output regime and (b) linear correctors; is this the case? How can this be? How can correctors be linear, and a priori known, if the underlying dynamics and/or learned model are nonlinear -- and therefore the error dynamics are nonlinear? I apologize for the long-winded question but I decided to just include most of my notes to give insight into what a first reading might feel like.
- Regular U-Nets and/or ConvNeXt U-Nets are used throughout the paper for evaluation (and correct me if I am wrong on this, perhaps I missed a different architecture somewhere). Do the authors believe the papers' conclusions are invariant to architecture? Why U-Nets, or rather way only U-Nets? Nothing wrong with the choice as these are basically SotA, but it is curious to draw general conclusions from such a fixed architecture.
- The experimental evaluations and benchmarks are not 1:1. I believe they cannot be due to the underlying nature of the differential equations that are being modeled. I believe the paper would be improved by having a localized, self-contained description of the benchmarks, why and how they're evaluated, and why they are slightly different. Perhaps this could just be in the Appendix (and perhaps it already is, but it is unclear if it is). Appendix A sort of gets at this, but perhaps a paragraph up front there to conceptually describe the benchmarks and why the metrics and protocols must be different, and therefore the reporting in the paper is/are different. This does not need to be a treatise but could help a reader who might be interested in surrogate modeling but does not know each of these benchmarks.
2 comments
Do the authors believe the papers' conclusions are invariant to architecture?
Response. No, we do not claim architecture invariance; the Rayleigh harm claim is an existence result for one released checkpoint.
Under prespecified 12-mode validation selection per checkpoint, the original was reselected (mode 9; test −1.29% [−1.80, −0.84]) and harm was confirmed in two descendants (mode 9: −0.39% [−0.54, −0.26]; −0.36% [−0.50, −0.17], one multistep-trained); all three survive Bonferroni over seven checkpoints. Both confirmed descendants share one seed, and mode 9 was known beforehand, so this is a robustness check, not independent discovery. Not confirmatory either way: one descendant not selected as harmful on validation still showed test harm (−0.17% [−0.36, −0.07]); one selected descendant (mode 7) did not replicate.
After submission we screened the other released Rayleigh checkpoints against persistence: the official Classic U-Net (−48.85%, validation), TFNO (−487.80%, validation) and FNO (−360.62%, test) all failed our competence check (not compared with The Well's reported metrics), so their correction signs were not interpreted. Of The Well's four released Rayleigh checkpoints, only the ConvNeXt U-Net beats persistence (test +40.15% [27.06, 52.65]; validation +33.37% [19.60, 46.66]), so it is the only released Rayleigh checkpoint whose correction signs we interpret.
On a different system, a competent released Navier-Stokes FNO (post-submission) was helped on average by all three fixed exact Fourier insertions (+4.46% to +9.36% outside both inserted Fourier pairs; adjusted intervals above zero), though 37, 42 and 6 of 200 trajectories worsened. We then applied the Rayleigh validation-selection protocol to this FNO, prespecified: all 40 single Fourier pairs (|k|∞ ≤ 4) had positive validation point estimates (34 with intervals above zero); the most harmful, +0.04% [−0.24, 0.29], had a validation interval crossing zero; on test, no pair had an interval below zero and 36 of 40 had intervals above zero (unadjusted). So harm did not transfer to this FNO; because the system also differs, this cannot separate architecture from system. A controlled same-system architecture comparison remains open.
The experimental evaluations and benchmarks are not 1:1.
Response. Agreed; they differ because each system admits a different observation pattern. All four come from The Well. Rayleigh-Bénard repeatedly inserts one exact mode and scores the state outside a fixed 12-mode span against the free-running model. Supernova makes one channel-subset insertion and scores full-state error. Acoustic scattering compares two ways of feeding the corrected state back under the same pressure observations. Turbulence with gravitational cooling keeps the reported state fixed and compares feeding a learned adjustment back into the model versus discarding it. Their numerical effects are not pooled. The revised PDF adds, at the start of Sec. 4, a table (Table 2) giving each system's observation, schedule, comparator, score, and question.
Response. They are not linearized. Equation (3) is an exact identity for two actual future rollouts: with baseline future error e and corrected-minus-baseline response r, the squared-error change is 2⟨e,r⟩ + ‖r‖². The realized e and r contain the nonlinear simulator. Only the insertion itself is affine, at the current step; every later step uses the original nonlinear model. Because e needs future truth, this identity diagnoses harm but cannot select an update in advance; hence we recommend validating each feedback route by delayed held-out error, as in our acoustic and turbulence studies (Sec. 4). The separate projector proposition assumes a perfect linear propagator and shows only that exact partial insertion can hurt; it gives no nonlinear guarantee or remedy.
Example: truth (0, 0), forecast (1, −1), next unobserved value (x+y)/2. Autonomy is exact, but correcting x to 0 gives error −0.5. Adding a nonlinear term 0.1x² preserves the harm: squared errors 0.01 versus 0.25.
Response. A learned transition that differs from the true dynamics, even on a true input. Well-trained checkpoints are misspecified in this sense. Section 2 shows harm needs no misspecification: with a perfect transition, replacing a cancelling error suffices. Misspecification only changes the realized e and r in Eq. (3), which already accounts for it.
Response. We claim no monotonic relation; Eq. (3) depends on the signed alignment of e and r, not only on error size. In the nonlinear example above (next y = (x+y)/2 + 0.1x²), adding +0.5 to the learned map raises its one-step error at the true state from 0 to 0.5, yet the same correction now reduces the future error from 0.6 to 0: a worse model can benefit more. Post-hoc (unadjusted), within one checkpoint, across the 35 Rayleigh test files, files with better early autonomous skill had higher correction utility (Spearman 0.364 [0.025, 0.619] and 0.466 [0.188, 0.648] for the two modes), but this is confounded by file difficulty, so we make no causal claim. Post-submission, one-step versus three-step fine-tuning (three seeds, from the released checkpoint) showed no stable difference. On test, mode-6 harm (−1.52%) shrank to at most 0.13% in magnitude, had an interval below zero only in the most competent descendant (58% vs 40% skill), and reversed to help in two (+0.16%, +0.33%; intervals above zero). Mode-9 harm shrank but persisted (−0.10% to −0.39%, versus −1.29%) in four of six descendants (unadjusted intervals below zero); three of six on validation. Descriptively, the least competent (original) checkpoint was most harmed, as you suspected; among the six descendants, harm did not track competence. Competence and fine-tuning are confounded here.