Does Elastic Augmentation Bias Activation Energies Measured From Images?

Chemists and materials scientists increasingly measure reaction progress by segmenting images instead of weighing samples or reading spectra. Examples include the fraction of a film that has crystallized, the thickness of an oxide scale, or how many lipid droplets have merged. A neural network that labels each pixel produces a conversion curve at each temperature. A rate constant is fitted to each curve, and the activation energy (the energy barrier that sets how fast the rate rises with temperature) is read from the slope of log-rate against inverse temperature, the Arrhenius plot. Annotated microscopy is scarce, so these segmenters are trained the way medical segmenters are: with elastic deformation augmentation, which randomly warps training images and their labels with smooth displacement fields so the network learns not to care about shape. This note asks whether that standard trick quietly corrupts the physical quantity the pipeline exists to measure. It also asks how to design and choose augmentation by error in the activation energy rather than by pixel overlap.

The concern is specific, and an augmentation scored by Dice (pixel overlap) can miss it entirely. A segmentation error that is the same at every temperature shifts every log-rate by the same amount and leaves the Arrhenius slope untouched. Only errors that change with temperature bias the barrier. Elastic warping is known to damage thin and small structures when it is resampled onto a pixel grid: Byrne et al. call this the "resampling trap" and show it tears thin cardiac walls. In nucleation-and-growth kinetics, the share of small nuclei and thin boundaries in an image changes systematically with temperature, so augmentation-induced errors on small features could feed directly into the slope. We propose to measure this effect on simulations where the true barrier is known, and to test a fix: warps that preserve topology and size, chosen by kinetic error.

Core Claim

For image-derived kinetics, the error budget that matters is temperature-dependent measurement bias, not average segmentation accuracy. Write the fitted log-rate at temperature $T$ as $\ln \hat k(T) = \ln k(T) + b(T)$, where $k$ is the true rate constant and $b(T)$ is the bias the segmenter introduces. The recovered barrier is then

$$\hat E_a = E_a - R\,\frac{d\,b(T)}{d(1/T)},$$

where $R$ is the gas constant. This follows from differentiating the Arrhenius line $\ln k = \ln A - E_a/(RT)$. Any bias that varies with $T$ is converted into barrier error, and the matching error in the pre-exponential factor $\ln A$ is anticorrelated with it.

We hypothesize three things. First, standard elastic augmentation lowers Dice error but can increase $|d b/d(1/T)|$, because its interpolation damage falls on early-stage, small-feature images whose prevalence depends on temperature. Second, a variant that preserves topology and local area removes most of this bias at little cost in Dice. Third, Dice ranks augmentation schemes differently from activation-energy error, so method selection in this regime should use kinetic error.

Where This Sits in Prior Work

The augmentation side supplies both the methods and the mechanism of concern. Roth et al. used thin-plate-spline warps, which interpolate smooth displacements from a sparse set of control points, to raise pancreas CT Dice in Deep convolutional networks for pancreas segmentation in CT imaging and DeepOrgan. Tang et al. restricted warps to the modes of a statistical shape model in An Augmentation Strategy ... Statistical Shape Model and 3D Thin Plate Spline. Neither paper asks whether the warps change a quantity measured downstream.

Topology-preserving augmentation for CNN-based segmentation of congenital heart defects is the work that motivates this proposal most directly. It shows that warping breaks thin structures, and it fixes the problem by transforming a one-pixel skeleton alongside the label and running a fast-marching correction. We reuse that correction as a component. Our evaluation target differs: Byrne et al. count topological defects in anatomy, while we measure bias in a fitted physical constant.

The kinetics side supplies the constraint. Integral methods such as Coats-Redfern can fit a wrong reaction model with $R^2 > 0.99$, as used in co-firing combustion kinetics (Combustion characteristics of cattle manure and pulverized coal co-firing under oxy-fuel atmosphere in non-isothermal and isothermal conditions). A high-quality-looking Arrhenius line therefore cannot vouch for the measurement behind it.

From free-energy profiles to activation free energies shows that the barrier, unlike the reaction free energy, is acutely sensitive to how the system is projected onto a coordinate. We take this as a warning that barrier estimates are fragile to representation choices. In our setting the "coordinate" is the segmenter's conversion measurement.

DeepEMs-25 shows that the physically meaningful conclusion, a trade-off between $E_a$ and $A$ that sets stability, depends on getting both parameters jointly right. That is why we report errors in both.

We deliberately do not use the "energy" in Pseudo-Non-Linear Data Augmentation via Energy Minimization. That energy is an information divergence on a statistical manifold with no spatial or kinetic meaning. Borrowing the word would add nothing to this problem.

Research Program

We first build a ground-truth benchmark, because no dataset in our file pairs kinetic images with known barriers. We simulate isothermal nucleation-and-growth in 2D at six to eight temperatures. Conversion follows the Avrami form $\alpha(t) = 1 - \exp(-(kt)^n)$, where $\alpha$ is the transformed fraction, $n$ is the Avrami exponent, and $k$ obeys Arrhenius with a chosen $E_a$ and $A$. Nucleation density and growth velocity each get their own barrier, so morphology (many small grains versus few large ones) changes with temperature, as it does in real crystallization and oxidation. Frames are rendered with blur, shot noise, uneven illumination, and low boundary contrast tuned to resemble optical and electron micrographs. A second family simulates parabolic thickening of a thin layer, the oxide-scale case studied by Jiang et al., where thin structures dominate early frames. Annotation scarcity is imposed by giving the segmenter only 5–20 labeled frames, mirroring the small cohorts in the medical work.

We then train a fixed U-Net under each augmentation scheme. Every model segments all frames. The pipeline fits $k(T)$ per temperature and recovers $\hat E_a$ and $\ln \hat A$ by Arrhenius regression. We record barrier error and log-prefactor error, along with Dice and the per-temperature bias $b(T)$. Recording $b(T)$ lets us check the decomposition above directly and attribute errors to early versus late conversion.

The proposed augmentation has two parts. The first is Byrne-style skeleton transport with fast-marching correction, so thin boundaries and small nuclei survive resampling. The second is a cap on the local Jacobian deviation of the displacement field; the Jacobian determinant measures local area change. The cap is scaled to the smallest feature size in the image, so warps cannot shrink sub-resolution nuclei out of existence.

Finally, we study label-free selection, because real experiments have no ground-truth barrier. Every augmentation scheme is also scored by two physics consistency checks. The first is Arrhenius-plot curvature. The second is the spread of isoconversional barriers across $\alpha$, which should be flat when a single mechanism is simulated. We test whether these checks rank schemes the way true barrier error does. We treat this part as exploratory, since real multi-step processes legitimately have $\alpha$-dependent barriers.

Baselines

The naive reference is training with no augmentation, alongside classical global thresholding with no learning at all. On simulated images with uneven illumination, thresholding may be biased. Its bias is driven by intensity rather than by augmentation-induced morphology, so it tells us whether a learned segmenter is needed at all.

The standard practice baseline is rigid augmentation only (rotations, flips, scaling). On prostate MRI, Tang et al. report 85.91% Dice for rigid augmentation, against 74.21% without augmentation and 86.85% for shape-model warps. That small gap makes rigid augmentation a serious competitor for kinetic accuracy even if it loses on Dice.

The strongest existing method is unconstrained thin-plate-spline elastic augmentation as used by Roth et al. Roth et al. report that 3D Gaussian smoothing of the network's outputs raised pancreas Dice from 56% to 68% ± 10% in a pipeline trained with TPS warps. That figure is a measure of their pipeline, not an isolated augmentation ablation, and it is the method practitioners would reach for. Byrne et al.'s topology-preserving augmentation is the closest prior fix. It raised myocardium Dice from 0.839 to 0.868 and cut median false-positive defect clusters from 12.0 to 6.5 on HVSMR 2016.

For the actual target metric, there is no reported result on Lacuna for activation-energy error of image-derived kinetics under any augmentation. Every barrier-error number in this study will be new.

All schemes share the same architecture, labeled frames, number of augmented samples, training steps, and a matched hyperparameter search of 20 trials, selected on held-out Dice. That last choice mirrors current practice and is the condition under which we claim Dice misleads.

Two ablations isolate the proposal's ingredients: skeleton correction alone, and the Jacobian cap alone. Beating the strongest baseline means a barrier error reduced by at least half relative to unconstrained elastic warping, with Dice within one point of it, across at least four of the five simulation regimes, over five seeds.

Why not just…?

Why not just use rigid augmentation and avoid warping altogether? Rigid transforms cannot break thin structures, so they may already be kinetically safe. This is a real threat to the "fix" half of the proposal, though not to the "measurement" half. If rigid augmentation matches our method on barrier error, the practical conclusion becomes "do not warp kinetic images," which is itself useful. The matched comparison above settles it. Our expectation that it falls short rests on the scarce-label regime, where the medical results show warping adds accuracy on boundaries. If that added accuracy is temperature-independent it improves Dice without harming the slope; if not, rigid wins.

Why not just pick the model with the best Dice? The equation in the core claim says Dice and barrier error measure different things: a uniform 5% under-segmentation hurts Dice and leaves $E_a$ exact. The decisive check is a rank correlation between Dice and barrier error across all trained models. A weak or negative correlation means Dice-based selection is unsafe here. A strong correlation refutes our premise, and we would report that.

Why not just calibrate the segmenter's bias with a few hand-measured frames per temperature? Post-hoc calibration directly estimates $b(T)$ and could cancel it. This is the strongest alternative. We include it as a baseline given the same 5–20 labels redistributed across temperatures. Calibration needs labels at every temperature, including the hardest early-stage frames, while our method needs none. We will report the number of calibration labels at which calibration matches the proposed augmentation. If that number is small, calibration should be recommended instead.

Proposed Experiments and Decisive Checks

Before running the main study, we replicate Byrne et al.'s HVSMR 2016 comparison with our augmentation code. Recovering roughly the reported 0.839 to 0.868 myocardium Dice gain confirms the topology correction is implemented faithfully.

The main experiment crosses six augmentation schemes, two simulation families, three label budgets, and three morphology regimes. The morphology regimes are strong, weak, and absent temperature dependence of feature size. The decisive prediction is a dose-response relation. Elastic augmentation's barrier bias should grow with how strongly feature size varies with temperature, and should vanish in the regime where morphology is temperature-independent. Seeing bias in the absent regime would mean the mechanism is something other than the one proposed.

A second check plants a known temperature-dependent defect in the labels. It verifies that the measured $\hat E_a$ shift matches $R\, db/d(1/T)$, which validates the error accounting.

Third, we test whether the label-free curvature and isoconversional checks rank schemes consistently with true barrier error. If they do, they offer a usable selection rule for real experiments.

The study succeeds if it either establishes augmentation-induced barrier bias and a cheap fix, or shows convincingly that the bias is negligible, so that practitioners can keep warping their micrographs.