The Synthetic-to-Real Exchange Rate of Physics-Constrained Operator Learners

Scientific machine learning mostly trains on simulated data. A neural operator is a network that learns to map an input function, such as a permeability field, to an output function, such as a pressure field. These models are fitted to thousands of cheap simulator runs and then asked to work on real measurements. Those measurements are noisy and sparse, and they come from physics the simulator only approximates. Two questions follow, and both are currently answered by guesswork: how many simulations is one real measurement worth, and does building the governing equations into the network make each simulation worth more or less?

We propose to measure this "exchange rate" directly in operator learning, and to show that the equations' residual on a handful of real measurements predicts it cheaply before any large simulation budget is spent. The residual here is the amount by which the idealized equation fails to hold on smoothed data. The central hypothesis is a crossover. When the simulator's physics matches reality, hard physical constraints make simulations more valuable and the model more robust to noise. When reality contains physics the simulator omits, the same hard constraints remove the true signal along with the noise. Synthetic data then stops substituting for real data at all, and no amount of extra simulation fixes it.

Core Claim

Three bodies of work each hold part of this picture, and none connects them. Hard-constraint methods show that projecting predictions onto the solution set of the governing equations filters observational noise. Theory-guided hard constraint projection (HCP) applies the projection $P = I - A^T(AA^T)^{-1}A$ to the network's outputs and reports stability up to 40% observation noise on subsurface flow. Symplectic encoders cut Duffing-oscillator MSE from 231.10 to 101.72 under 10–20 dB noise. Both results assume that the constraint is the true law.

Work on synthetic-data reliance shows that this assumption breaks in deployment. Hinder et al. survey how systematic drift defeats pipelines built on idealized noise models. Rosenberg-Kima and Pardos find real student data settling into parameter regimes that simulation assumptions had dismissed as implausible. The only systematic measurement of substitutability in the file, Chang et al., finds roughly 30 synthetic frames per real frame in multi-person tracking. It also finds that synthetic pretraining plus 20% of the real data matches training on 100% real data. That study concerns bounding-box trackers, not physics.

Work on generation overhead shows that simulations are not free. PDEBench cites about 60 seconds per 3D solve and up to 10,000 runs per equation. Whether that spend beats collecting more real data is never computed.

Our claim is that the exchange rate is a measurable, predictable quantity in physical operator learning. It depends jointly on constraint hardness and on how far the simulator's physics departs from reality. That departure can be estimated from roughly ten real samples. This differs from Chang et al. in domain, in the variable under study (constraint structure rather than photorealism or behavioral diversity), and in offering a predictor rather than only a post-hoc curve. It differs from PDEBench, which evaluates entirely inside the simulator, because we evaluate under controlled physics mismatch and non-Gaussian sensor corruption.

The Quantity Being Measured

Let $E(n_s, n_r)$ be the test error on real measurements of a model pretrained on $n_s$ simulations and fine-tuned on $n_r$ real samples. The exchange rate at a given operating point is the marginal rate of substitution, the number of extra simulations that compensate for removing one real sample at fixed error:

$$\rho(n_s, n_r) = \frac{\partial E / \partial n_r}{\partial E / \partial n_s}.$$

Both derivatives are negative when data helps, so $\rho$ is positive. We estimate it from iso-error contours of a measured grid over $n_s$ and $n_r$, not from fitted derivatives. If $c_s$ is the cost of one simulation in solver-seconds and $c_r$ is the cost of one real measurement, buying simulations pays off exactly when $\rho\, c_s < c_r$. This break-even rule is what connects exchange-rate measurement to the overhead literature.

The crossover hypothesis predicts how $\rho$ behaves for each constraint type. For hard-projected models, $\rho$ should be small at zero mismatch and grow without bound once $\partial E/\partial n_s \to 0$, which happens when the error hits a floor set by mismatch. Soft-penalty and unconstrained models should show a larger $\rho$ at zero mismatch but a gentler rise.

Research Program

Testbed. Genuine experimental PDE data with matched simulators is not among the resources in the file. We therefore build a "surrogate reality" protocol in which mismatch and noise are separate, controlled dials. The synthetic source is the idealized equation as distributed in PDEBench. We use three problems:

  • 2D Darcy flow on $64\times64$ grids. It is linear in pressure, so HCP's projection is exact and cheap.
  • 1D diffusion-reaction, the setting of the DeepXDE inverse experiments.
  • 1D viscous Burgers.

The "real" target comes from the same family with an added term the simulator omits, scaled by a strength $\varepsilon$:

  • an unmodeled spatially smooth source term, or mild permeability anisotropy, for Darcy;
  • a second, slower reaction pathway for diffusion-reaction;
  • a state-dependent viscosity for Burgers.

Target data are observed on sparse sensor locations and corrupted by four noise types: white Gaussian noise at 10–40%, heavy-tailed outliers, slow calibration drift, and spatially correlated noise.

Learners. The unconstrained operators are the Fourier Neural Operator and the Galerkin Transformer. The latter replaces softmax attention with a linear-cost projection-based attention and reports 30–50% better accuracy than FNO on interface Darcy. We add two constrained variants of the same backbone:

  • a soft residual-penalty version, $\mathcal{L}_{data} + \lambda \mathcal{L}_{PDE}$, tuned over $\lambda$;
  • a hard-projection version that applies HCP's output projection for the idealized discretized operator.

A fourth arm isolates the ingredient we expect to matter under mismatch: hard projection followed by an explicit correction head. This head is restricted to low spatial frequencies, sees only real data, and has an output norm we can inspect. Its purpose is to give the hard-constrained model a place to put physics the simulator lacks, without reopening a channel for high-frequency noise.

Measurement. For every combination of learner, problem, $\varepsilon$ and noise type we measure $E$ on a grid. Here $n_s$ takes the values $\{0, 100, 300, 1000, 3000, 10000\}$ and $n_r$ takes the values $\{5, 10, 20, 50, 100, 200\}$. Each grid point uses the pretrain-then-fine-tune protocol of Chang et al., with five seeds. Error is reported as plain RMSE and as PDEBench's conservation (cRMSE), boundary (bRMSE) and spectral (fRMSE) errors. This matters because PDEBench shows that pixel-wise error hides conservation and high-frequency failures. Exchange rates are read off the resulting surfaces. Synthetic cost $c_s$ is logged as the measured solver wall-clock per sample.

The diagnostic. Before any grid is run, we take ten real samples, low-pass filter them, and compute the idealized equation's residual on them. The cutoff is set from a noise-floor estimate on the highest frequency band. We normalize this residual by the magnitude of the forcing. The reasoning follows the soft-constraint literature's own observation: noise mostly inflates high-frequency derivatives, whereas a missing physical term leaves a structured, low-frequency residual. The prediction is that this single number ranks settings by their measured $\rho$ and locates the $\varepsilon$ at which hard projection stops being the best arm.

Baselines

The naive reference point is training on the real noisy samples alone, $E(0, n_r)$. It defines the denominator of every substitution claim. We also report the opposite extreme, simulation-only training evaluated zero-shot on real data. Every other result is stated relative to these two.

The strongest existing competitor is the plain recipe from Chang et al.: pretrain an unconstrained operator on simulations and fine-tune on real data. We run it with both FNO and the Galerkin Transformer, because the latter is the strongest operator backbone in the file. Cao reports that it improves evaluation accuracy by 30–50% over FNO on 2D interface Darcy flow, and Li et al. report FNO with 60% lower error than the next best learned solver on Darcy. The file gives no absolute error value for either. For synthetic-to-real exchange rates in PDE operator learning, no reported result was found on Lacuna. The only reference exchange rate is the ~30:1 frame ratio on MOT17 from Chang et al., in a different domain.

All arms share the same simulations, real splits, noise draws, epoch budget and 20-trial hyperparameter search per arm, including $\lambda$ for the soft penalty. A constrained arm "beats" this baseline in a given regime only under a specific condition. Its exchange rate must be lower, meaning it needs fewer simulations per real sample replaced, by more than the seed-to-seed spread. Its real-data RMSE and cRMSE at matched $n_r$ must also be no worse.

The soft residual-penalty arm, in the style of DeepXDE, is the natural competitor to the correction-head arm, since a soft penalty is also a form of slack. The ablation that isolates our key ingredient compares three models: hard projection with the low-frequency correction head, the same model with an unrestricted correction head, and hard projection with no head. This separates the value of having a slack channel from the value of restricting it to low frequencies.

For the diagnostic, the baseline predictor is the obvious one. We fine-tune the plain FNO on the same ten real samples and use its validation error as the estimate of transfer quality.

Why not just…?

Why not just pretrain an unconstrained FNO on simulations and fine-tune it on real data, and skip constraints entirely? This is a real threat. Fine-tuning on real data may absorb mismatch well enough that constraint hardness barely moves $\rho$. The measurement grid settles the question directly, because this recipe is run under identical budgets at every $\varepsilon$. If it matches the best constrained arm everywhere, we report that constraint structure is irrelevant to substitutability. That would be a useful negative result, given how often hard constraints are motivated by data efficiency. The diagnostic's value does not depend on this outcome, since it predicts $\rho$ for whichever learner wins.

Why not just add realistic noise to the simulations? Noise augmentation addresses the sensor side of the gap but not the physics side. The testbed separates the two dials so that this can be shown rather than asserted. We include a noise-matched augmentation arm. The prediction is that it closes the gap at zero mismatch and leaves the mismatch-driven error floor untouched. HCP already reports that random perturbations do not preserve the governing equations. That finding, however, is about matched physics, and it is why we test augmentation rather than dismiss it.

Why not just generate more simulations? Evidence from other domains shows plateaus under quantity scaling, including DISCO, where 75,000 filtered examples beat over a million raw ones, and Beyond Quantity. Data-driven learning of nonlocal physics finds that data composition, not count, decides whether kernels are identifiable. Our grid runs to 10,000 simulations. The hypothesis is falsified if error keeps falling with $n_s$ at large $\varepsilon$ for hard-projected models.

Why not just hold out some real data and validate? With ten real samples, a validation estimate is noisy, and it arrives only after fine-tuning a model. The residual diagnostic needs no training. We compare the two predictors head-to-head. If validation error ranks settings by $\rho$ as well as the residual does, the diagnostic adds nothing, and we will say so.

Proposed Experiments and Decisive Checks

Three results would decide the proposal.

The first is whether the crossover exists. We check that at $\varepsilon = 0$ the hard-projected arm has the lowest $\rho$ and the lowest cRMSE across noise types, consistent with the noise robustness reported for HCP. We then check that, as $\varepsilon$ grows, it develops an error floor that neither more simulations nor moderate $n_r$ removes, while the soft and correction-head arms degrade smoothly. The heavy-tailed and drift noise conditions test whether this holds beyond the Gaussian noise that most physics-constrained results assume.

The second is whether the ten-sample low-pass residual predicts the measured exchange rates better than the validation baseline. We evaluate this by Spearman rank correlation across all problem, $\varepsilon$ and noise settings, and by accuracy in placing the hard-versus-soft crossover to within one grid step of $\varepsilon$.

The third is whether the break-even rule $\rho\, c_s < c_r$, evaluated with the predicted rather than measured $\rho$, gives the same buy-or-don't-buy decision on simulations as the full grid. That is the practical payoff for anyone deciding how much simulation compute to spend.

The main limitation is that "reality" here is a mismatched simulator rather than a laboratory. The protocol is therefore a controlled necessary test, not proof of transfer to hardware. Any one experimental dataset with a matching idealized simulator, from subsurface flow of the kind HCP models or from diffusion-reaction transport, would be the first external check. We do not assume such data are available.