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Attributing Preprocessing Invariance in Spectral Foundation Models
Dongjun Wei, Hongyi Wu, Yinuo Zou
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Summary
This paper challenges the attribution of preprocessing invariance in spectral foundation models, arguing that observed invariance often stems from the model's initial normalization step rather than learned parameters. Using a Raman foundation model as a case study, the authors demonstrate that standard normal variate and similar normalizations mathematically remove positive affine transformations (scaling and offset). Experiments show that the normalization alone performs comparably to the full model in cross-preprocessing transfer tasks, suggesting that claimed 'learned' invariance is often pre-existing. The study proposes comparing the model against its normalization alone to isolate true learning gains.
Entities (6)
Relation Signals (5)
Raman Foundation Model (RFM) → uses → Robust Normal Variate (RNV)
confidence 98% · Its first operation on every input is robust normal variate normalization, written RNV
Robust Normal Variate (RNV) → removes → Positive Affine Transformation
confidence 97% · for normalizations of this kind the positive affine maps are exactly the transformations that preserve the normalized representation.
Raman Foundation Model (RFM) → doesnotoutperform → Robust Normal Variate (RNV)
confidence 95% · On six Raman evaluation datasets, the model does not measurably outperform its own normalization.
Cross-Preprocessing Transfer → measures → Normalization Invariance
confidence 93% · A transfer grid therefore measures two things at once: the invariance the normalization already supplies, and whatever the encoder adds on top of it.
Multiplicative Scatter Correction → isremovedby → Robust Normal Variate (RNV)
confidence 92% · Multiplicative scatter correction belongs to this class precisely on spectra whose fitted slope is positive.
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Abstract
Abstract:Preprocessing invariance is an appealing goal for spectral foundation models: a frozen model should remain useful when laboratories preprocess spectra differently. It is usually measured by training a classifier under one preprocessing pipeline and testing it under another, with preserved accuracy read as evidence of learning. We revisit that reading, using a Raman foundation model as a case study. Such models normalize their inputs before any learned parameter is applied. If that normalization maps two differently preprocessed spectra to the same vector, the encoder receives identical inputs, so the invariance cannot be attributed to learning. For a normalization that uses each spectrum's own statistics, this happens exactly when one spectrum is a positive multiple of the other plus a constant. Several standard preprocessing operations take that form. The encoder should therefore be measured against the normalization alone, which has no learned parameters. On six Raman evaluation datasets, the model does not measurably outperform its own normalization. It improves on raw spectra, but so does the normalization alone. Training does improve the encoder over random initialization, and a controlled experiment shows that it learns to ignore a transformation only when that transformation reaches it. A numerical test settles which transformations a given normalization removes. Across released systems in five modalities, most normalizations already remove transformations of that form, and several of those systems claim that invariance as learned. Replicating the comparison on two of them shows no gain either.
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- Source: https://arxiv.org/abs/2608.14227v1
- Canonical: https://arxiv.org/abs/2608.14227v1
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Attributing Preprocessing Invariance in Spectral Foundation Models Dongjun Wei dongjun@connect.hku.hk gabrielwei@opluxcare.com Affiliation: ESCP Business School, Paris, France Affiliation: OpluxCare Co., Ltd. Hongyi Wu wuhyi@connect.hku.hk waynewu@opluxcare.com Affiliation: The University of Hong Kong, Hong Kong, China Affiliation: OpluxCare Co., Ltd. Yinuo Zou zouynn@nju.edu.cn Affiliation: Nanjing University, Nanjing, China Abstract Preprocessing invariance is an appealing goal for spectral foundation models: a frozen model should remain useful when laboratories preprocess spectra differently. It is usually measured by training a classifier under one preprocessing pipeline and testing it under another, with preserved accuracy read as evidence of learning. We revisit that reading, using a Raman foundation model as a case study. Such models normalize their inputs before any learned parameter is applied. If that normalization maps two differently preprocessed spectra to the same vector, the encoder receives identical inputs, so the invariance cannot be attributed to learning. For a normalization that uses each spectrum’s own statistics, this happens exactly when one spectrum is a positive multiple of the other plus a constant. Several standard preprocessing operations take that form. The encoder should therefore be measured against the normalization alone, which has no learned parameters. On six Raman evaluation datasets, the model does not measurably outperform its own normalization. It improves on raw spectra, but so does the normalization alone. Training does improve the encoder over random initialization, and a controlled experiment shows that it learns to ignore a transformation only when that transformation reaches it. A numerical test settles which transformations a given normalization removes. Across released systems in five modalities, most normalizations already remove transformations of that form, and several of those systems claim that invariance as learned. Replicating the comparison on two of them shows no gain either. 1 Introduction Foundation models are increasingly built for scientific signals. Yet those signals vary from one laboratory to the next because each prepares its data in its own way. Preprocessing invariance is therefore an appealing goal: a frozen model should remain useful whichever laboratory produced its input. The problem is especially sharp for Raman spectra, which are one-dimensional signals widely used in medical diagnosis, microbiology, forensics, materials science, and environmental analysis. Raw spectra carry strong backgrounds, scattering effects, and instrument-specific variation, so they are almost always preprocessed before being used for machine learning. One laboratory removes a baseline, another divides spectra by their area, another takes a first derivative. A model developed under one of these pipelines can therefore perform poorly when it receives spectra processed in another way. One way to train for invariance is to show the model the same spectra under two different preprocessing pipelines and encourage it to treat the results as equivalent (Chen et al. 2020; Zbontar et al. 2021). The matching evaluation is to fit a simple classifier, or probe, on the model’s frozen features under one pipeline and test it under another. Doing this for every pair of pipelines gives a cross-preprocessing transfer grid. Preserved accuracy is then interpreted as evidence that the model has learned to ignore preprocessing differences, and spectral foundation models are built and motivated in these terms (Eranti et al. 2026; Xue et al. 2025). However, we find that this evaluation can over-attribute invariance to learning, because part of the measured invariance may already be imposed before any learned parameter is applied. The reason is algebraic rather than empirical. Many spectral foundation models normalize every input before the encoder sees it, for example by rescaling spectra by their own mean and standard deviation. Write such a model as f(x)=g(R(x))f(x)=g(R(x)), where R is the normalization and g is the learned encoder. Suppose some preprocessing transformation T leaves normalized spectra unchanged, so that R(T(x))=R(x)R(T(x))=R(x). Then the encoder receives the same input with or without T, and returns the same output, so f(T(x))=f(x)f(T(x))=f(x). This holds for every encoder g, trained or randomly initialized, so transfer across T is already guaranteed by the normalization and cannot be attributed to the encoder. The argument does not depend on the dataset, the architecture, or the training procedure. A direct consequence is that observed invariance alone does not show learned invariance. A transfer grid therefore measures two things at once: the invariance the normalization already supplies, and whatever the encoder adds on top of it. Our contribution is neither the algebra above, which is elementary, nor the classical observation that centering and scaling spectra by their own statistics removes additive and multiplicative variation (Barnes et al. 1989; Geladi et al. 1985). It is the evaluation principle that follows from them. Given a model and a transformation, first ask whether the normalization already removes it, then measure what the encoder adds by comparing the model against the normalization on its own. We apply that principle in three parts. First, we identify what normalization already removes. For a normalization that centers and scales spectra by their own statistics, two spectra map to the same vector if and only if one is a positive multiple of the other plus a constant (Theorem 3.1). Standard normal variate normalization, area normalization, and multiplicative scatter correction with positive fitted slope all have this form, so applying any of them before the model leaves its normalized input unchanged. A numerical test settles the same question for any other normalization, and we run it on ECG time series as well as Raman spectra. Second, we compare the model with its normalization alone. Because the model is a normalization followed by an encoder, the way to isolate the encoder is to delete it and keep the normalization, using the normalized spectra themselves as the frozen representation in the same evaluation. On six Raman evaluation datasets, each evaluated on its own, the normalization alone matches the model: mean cross-preprocessing accuracy differs by 1.51.5 points in the normalization’s favor, and two robustness measures show no detectable difference. The trained encoder therefore adds no measurable gain over normalization alone, although training improves the encoder over random initialization (Section 4.5). The same analysis explains an earlier internal result, where an 18-point advantage over raw spectra vanishes once we drop the comparisons whose transfer the normalization already guarantees. Third, we test the mechanism directly. A randomly initialized encoder shows the same invariance as the trained one on the transformations the normalization removes, exactly as the algebra predicts. Conversely, across five paired seeds, the same training objective produces invariance to a gain and offset transformation only when the transformation is applied after normalization and so reaches the encoder at all. We do not claim that every spectral foundation model behaves like the one studied here, or that the encoder is without value. Training measurably improves the encoder over random initialization, and the trained encoder brings spectra from two different derivative pipelines about three times closer together in feature space than the untrained encoder does. All results are measured within a dataset, because the six datasets have disjoint label spaces. This leaves cross-dataset transfer, the setting these models are built for, untested here. In the setting we do test, we find no measurable gain in cross-preprocessing transfer beyond the normalization. The transferable contribution of this paper is the comparison with the normalization alone, and the test that supports it. The Raman case study shows why both matter. 2 Related Work Spectral preprocessing. Normalizing spectra by their own statistics is long established in chemometrics. Standard normal variate normalization centers and scales spectra by their own mean and standard deviation (Barnes et al. 1989), robust normal variate normalization replaces those with robust statistics (Guo et al. 1999), and multiplicative scatter correction removes offset and scale relative to a reference (Geladi et al. 1985). The links between the first and the last have been studied since the 1990s (Dhanoa et al. 1994). Asymmetric least squares baseline removal (Eilers & Boelens 2005) and Savitzky–Golay differentiation (Savitzky & Golay 1964) change spectra in ways this family does not. Which of these a laboratory chooses measurably changes what a downstream Raman model learns (Liu et al. 2017; Storey & Helmy 2019; Poth et al. 2022). Reducing dependence on preprocessing. A parallel line of work reduces dependence on handcrafted pipelines, by training convolutional models on near-raw spectra (Liu et al. 2017), by augmenting over preprocessing pipelines rather than committing to one (Bjerrum et al. 2017), or by learning the preprocessing itself, with mixed results (Helin et al. 2022). View-based self-supervision (Chen et al. 2020; Zbontar et al. 2021), which trains on differently preprocessed copies of the same input, supports preprocessing-invariance training directly, and the invariances it produces have been analyzed for image models (Ericsson et al. 2021). RSPTE applies it to Raman, pretraining an encoder on physically motivated transformations including intensity rescaling (Eranti et al. 2026), and recent spectral foundation models are motivated partly by generalization across devices (Xue et al. 2025). Generalization across datasets nevertheless remains difficult in current Raman benchmarks (Koddenbrock et al. 2026; Pan et al. 2026). Invariance supplied or acquired. Prior work asks how models acquire preprocessing invariance. We ask whether observed invariance was acquired at all. The issue is sharpest for view-based objectives: if the normalization already maps two differently preprocessed spectra to the same vector, their agreement cannot be attributed to learning. The same attribution problem has been raised in neighboring modalities, where EEG foundation models have been stress tested against random initialization (Zare 2026). That control needs a trained model, but the test here does not. We are not aware of prior work in spectral representation learning that asks which evaluated transformations a model’s own normalization already removes, or that uses that normalization alone as the comparison against which a learned invariance is scored. 3 Attributing Preprocessing Invariance 3.1 Why the normalization is the right comparison We study a length-agnostic Raman foundation model with 2.68M parameters, a transformer pretrained on 815k spectra with masked reconstruction (He et al. 2022), a redundancy-reduction objective over differently preprocessed spectra (Zbontar et al. 2021), and a domain-adversarial head on preprocessing labels (Ganin et al. 2016). We write RFM for the deployed checkpoint, which stays frozen throughout, and which uses native spectral positions so that it can process spectra of different lengths and resolutions. Its first operation on every input is robust normal variate normalization, written RNV, so the complete model is f(x)=g(R(x)),R(x)=clip(x−median(x)s(x)+ϵ,−8,8),ϵ=10−6,f(x)=g(R(x)), R(x)=clip\! ( x-median(x)1s(x)+ε,-8,8 ), ε=10^-6, where s(x)s(x) is half the distance between the 16th and 84th percentiles of the input. RNV is therefore not an external baseline chosen for its performance, but the deterministic part of the model before any learned parameter, which is what makes it the comparison that isolates the encoder. Comparing f with R removes the learned component and leaves everything else fixed. It therefore asks a precise question: does g contribute preprocessing robustness beyond R? PCA, smaller encoders, and unrelated architectures answer different questions, so we use them only as supporting controls in Section 4.5. Two limits should be stated at the outset. RNV at full width is not a drop-in replacement for the model. It produces one feature per channel of whichever instrument produced the spectra, so it cannot support a probe shared across datasets, which is what a length-agnostic encoder is built to provide. It is an attribution comparison, not a proposed deployment substitute. Every comparison in this paper is therefore made within a dataset, on its own native axis, because the six evaluation datasets have disjoint label spaces: cell lines, sample types, dye brands, chloroform presence, serum processing, and disease status. Training a probe on one and evaluating it on another is not a defined task here, so the regime in which only the encoder can compete remains untested, and our claim is scoped to within-dataset cross-preprocessing transfer. The decomposition also separates comparisons that a single transfer score conflates. Comparing R(T(x))R(T(x)) with R(x)R(x) asks what the normalization already removes. Comparing g0(R(x))g_0(R(x)) with R(x)R(x), for an untrained encoder g0g_0, measures the effect of adding the encoder. Comparing gθ(R(x))g_θ(R(x)) with g0(R(x))g_0(R(x)) measures the effect of training. Our main comparison, gθ(R(x))g_θ(R(x)) against R(x)R(x), asks whether the trained encoder improves on normalization alone. Training improves the encoder over random initialization, but the trained encoder does not measurably outperform normalization alone. 3.2 Which transformations the normalization removes The median and the percentile spread are both equivariant under a positive affine map T(x)=ax+bT(x)=ax+b1 with a>0a>0, so T(x)T(x) and x become identical after normalization. The converse also holds, and for normalizations of this kind the positive affine maps are exactly the transformations that preserve the normalized representation. Theorem 3.1. Let m and s be statistics computed from a single spectrum that satisfy m(ax+b)=am(x)+bm(ax+b1)=a\,m(x)+b and s(ax+b)=as(x)s(ax+b1)=a\,s(x) for all a>0a>0 and b∈ℝb , and define R~(x)=(x−m(x))/s(x) R(x)=(x-m(x)1)/s(x) on the set where s(x)>0s(x)>0. Then R~(y)=R~(x) R(y)= R(x) holds if and only if y=ax+by=ax+b1 for some a>0a>0 and b∈ℝb . Proof. In one direction, R~(ax+b)=a(x−m(x))/(as(x))=R~(x) R(ax+b1)=a(x-m(x)1)/(a\,s(x))= R(x). In the other, suppose R~(y)=R~(x)=z R(y)= R(x)=z. Each input can be reconstructed from its normalized form as x=s(x)z+m(x)x=s(x)z+m(x)1 and y=s(y)z+m(y)y=s(y)z+m(y)1, so y=s(y)s(x)x+(m(y)−m(x)s(y)s(x)).y= s(y)s(x)\,x+ (m(y)-m(x) s(y)s(x) )1. Since s(x)s(x) and s(y)s(y) are positive, the coefficient of x is positive. ∎ Corollary 3.1. A transformation T satisfies R~∘T=R~ R T= R if and only if it acts pointwise as T(x)=α(x)x+β(x)T(x)=α(x)\,x+β(x)1 with α(x)>0α(x)>0. The transformations that do not depend on the input are then exactly the fixed positive affine maps. Multiplicative scatter correction belongs to this class precisely on spectra whose fitted slope is positive. Any transformation that changes the normalized profile of at least one input lies outside it, including derivatives, baseline removal, smoothing, per-channel gain, and negative scaling. We call R~ R the ideal normalization, because it omits the stabilizer ϵε and the clipping of the deployed operator R. RNV, z-scoring, and min-max normalization all satisfy the assumptions of the theorem. Normalization by the L2L_2 norm does not, because it has no location statistic, which is why it removes positive scaling but not offsets. Standard normal variate normalization and area normalization with a positive divisor apply a positive affine map to each input, so the ideal normalization removes both exactly. Throughout the paper, removed means exact removal by the ideal normalization, and a comparison linked by an exactly removed transformation is fixed before learning begins. For the deployed R, the stabilizer and the clipping mean we verify removal numerically rather than assume exact equality. The stabilizer generally breaks the identity when the scale factor differs from one, since R(ax+b)R(ax+b1) divides by as(x)+ϵa\,s(x)+ε rather than by a(s(x)+ϵ)a(s(x)+ε). Clipping acts in the opposite direction, and can introduce collisions between inputs that are not positive affine images of one another. We report the residual in Section 4.2 and Appendix B. 3.3 Testing removal without a closed form Removal can also be tested without a closed-form derivation. We normalize a sample and its transformed version, take the largest deviation over spectra and channels, and divide by the standard deviation of the normalized representation over the sample. A transformation counts as numerically removed when this quantity falls below 10−310^-3. Dividing by the spread of the representation rather than by the magnitude of the input matters, because a signal with a large dynamic range can otherwise make a real offset look negligible. The test depends only on the normalization and the transformation, not on the encoder or on training, so it can be run before training to check whether an intended augmentation reaches the encoder. 4 Evaluation and Analysis 4.1 Setup Datasets and preprocessing. We evaluate on six public Raman classification datasets covering cancer cell lines, blood and skin, forensic dyes, environmental chemistry, serum, and saliva. They hold 3,291 spectra in total, between 230 and 1,050 per dataset, with two to twelve classes. Spectra are not resampled onto a shared wavenumber grid, so every representation operates on the native channels of its dataset. We apply six preprocessing pipelines. Three are transformations RFM saw during pretraining, which we call in-family: raw spectra, the rolling-minimum baseline step as released, and a central first difference. Three are out-of-family: asymmetric least squares baseline removal, multiplicative scatter correction against the dataset mean, and a Savitzky–Golay first derivative. Standard normal variate normalization is excluded because the ideal normalization removes it exactly, and the deployed RNV removes it to a small numerical residual (Appendix B). Dataset details and exact parameters are in Appendix A. Representations and probing protocol. We compare raw spectra, PCA, RNV alone, RNV followed by PCA, and RFM, with the PCA basis fitted on raw spectra and shared across pipelines so that no pipeline receives its own coordinate system. For each dataset and representation we build a cross-preprocessing transfer grid, where cell (i,j)(i,j) reports balanced accuracy for a probe trained under pipeline i and evaluated under pipeline j, so the diagonal holds the case where the two agree. The probe is feature standardization followed by multinomial logistic regression, with five-fold stratified cross-validation over three seeds and one fixed penalty for every representation. Standardization is fitted on the training fold of the source pipeline only and applied unchanged to the target. Three protocol choices could favor one representation over another, and Appendices H, I, and J relax each in turn: the fixed penalty, folds formed over spectra rather than physical samples, and two dataset-level statistics fitted on all inputs. Metrics. We report off-diagonal balanced accuracy as our primary measure of cross-preprocessing transfer, alongside two robustness measures taken relative to a representation’s own on-diagonal accuracy. Degradation is the absolute drop when preprocessing changes, on-diagonal minus off-diagonal accuracy, and retention is the fraction that survives, off-diagonal divided by on-diagonal. A weak representation can score well on both while transferring little, so we lead with off-diagonal accuracy. Intervals are paired bootstraps over the six datasets, treated as descriptive at that sample size, and we give every per-dataset effect alongside every aggregate. Because chance balanced accuracy ranges from 5050 to 8.38.3 percent across these datasets, absolute column means are descriptive only, so we also report each dataset rescaled by its own chance level, (accuracy−chance)/(1−chance)(accuracy-chance)/(1-chance). 4.2 What the normalization removes in practice We first check the numerical test against Theorem 3.1, then apply both to the preprocessing pipelines of our evaluation, to the deployed normalization, and to the augmentations used during pretraining. In most cases part of the variation the encoder is credited with handling never reaches it. Two comparisons in the grid are fixed before learning. Raw spectra and their scatter-corrected version become identical after the ideal normalization whenever the fitted slope is positive. That holds for every spectrum in four of the six datasets and for about 9494 percent in the remaining two, where Section 4.3 shows the conclusion does not depend on how the rest are handled. Area normalization satisfies the same condition, since its divisor was positive for all 3,291 spectra. In the four-by-four grid of the earlier internal evaluation (Section 4.4), two of the twelve off-diagonal cells compare preprocessing states that the ideal normalization collapses. We call these the removed cells and the rest the remaining cells. Excluding the two lowers the reported retention from 6767 to 5757 percent. The numerical test agrees with the theory. On a synthetic suite of transformations, the largest deviation among those the theory calls removed is 3.4×10−53.4× 10^-5, and the smallest among those it calls surviving is 5.375.37. The partition is therefore identical for every threshold between 10−410^-4 and 10−110^-1 (Appendix B). Running the same test on 4,998 ECG heartbeat time series, with no Raman data or model involved, gives verdicts that agree on all forty combinations of normalization and transformation. The deployed normalization is close but not exact. The stabilizer and the clipping mean Theorem 3.1 describes R only approximately. Over all 3,291 evaluation spectra, the transformations removed by the ideal normalization agree to machine precision for the median spectrum and stay below 10−310^-3 for more than 9999 percent. The small tail falls where the percentile spread makes the stabilizer non-negligible. Scatter correction with negative slope is the boundary case the corollary predicts, and its residual is six to nine orders of magnitude larger. The downstream conclusions therefore do not depend on treating R as exact, and Appendix B gives the distributions. Two pretraining augmentations barely reach the encoder. An augmentation the normalization removes cannot teach the encoder about that variation. The sampler that builds training pairs avoids this, since it always pairs spectra from one positive affine equivalence class with a transformation outside that class, and none of the 60 sampled pairs fell within one class. The separate physics augmentation does not. Two of its six components are positive affine per spectrum and reach the encoder only through residuals of 4.9×10−64.9× 10^-6 and 2.0×10−62.0× 10^-6. The other four survive, with residuals of 0.0280.028 for shot noise, 0.120.12 for scatter slope, 4.64.6 for fluorescence baseline, and 5.45.4 for wavenumber shift. The training gradient therefore does not vanish, but the intended gain and offset variations are almost entirely removed before the encoder. 4.3 The learned encoder does not measurably improve on its normalization Main finding. RFM does not measurably outperform its own normalization. We report that comparison on absolute transfer and on two robustness measures, then check it against every protocol variation we could run. All numbers are percentages of balanced accuracy, and all differences are in points. Normalization is ahead on and off the diagonal. Table 1 gives the result and Figure 1 shows the underlying grids. Normalization alone reaches 52.052.0 off-diagonal against 50.550.5 for RFM, and it is also higher on the diagonal, at 94.094.0 against 90.990.9. The paired off-diagonal difference is −1.5-1.5 points with a 95% interval of [−4.6,+3.3][-4.6,+3.3], so RFM does not reliably outperform its own normalization. The grids show a similar pattern across most cells. The exception is the derivative block, where RFM is weaker. Because the datasets carry two to twelve classes, we also rescale each by its own chance level, which leaves the ordering unchanged at −1.3-1.3 (Appendix G). Figure 1: Transfer grids. Balanced accuracy (%) for a probe trained on pipeline i and evaluated on pipeline j, averaged over six datasets. Asterisks mark out-of-family pipelines. Normalization reproduces most of the transfer structure of RFM, which is much weaker on derivative transfer. Table 1: Main comparison. Cross-preprocessing transfer (%) averaged over six datasets and three seeds, best per row in bold. The right block gives RFM minus RNV in points, its 95% bootstrap interval, and datasets won, with – where we do not report them. ALS, MSC, and SG denote asymmetric least squares, multiplicative scatter correction, and Savitzky–Golay. Contrast Raw PCA RNV RNV+PCA RFM RFM−-RNV 95% interval Wins In-family 50.9 37.2 51.3 39.8 49.6 −1.7-1.7 [−4.9,+1.9][-4.9,+1.9] 2/6 Out-of-family 33.2 36.0 41.0 35.2 40.6 −0.4-0.4 [−5.4,+6.2][-5.4,+6.2] 3/6 ALS vs raw 31.6 46.8 56.0 43.0 61.7 +5.7+5.7 [−12.9,+23.3][-12.9,+23.3] 3/6 MSC vs raw 59.0 47.0 93.4 60.3 90.0 −3.3-3.3 [−7.8,+0.8][-7.8,+0.8] 2/6 SG vs crude 81.1 82.4 77.8 84.5 56.1 −21.7-21.7 [−39.2,−8.8][-39.2,-8.8] 0/6 Baseline on/off 63.0 46.7 82.7 55.5 70.7 −12.0-12.0 [−21.0,−1.8][-21.0,-1.8] 1/6 Off-diagonal 43.2 41.3 52.0 43.0 50.5 −1.5-1.5 [−4.6,+3.3][-4.6,+3.3] 1/6 On-diagonal 91.9 82.5 94.0 83.2 90.9 −3.1-3.1 – – Robustness and transfer point in different directions. Absolute accuracy alone would hide that RFM degrades slightly less under a change of pipeline than the normalization does. Table 2 separates the three quantities. RFM is behind on transfer and nominally ahead on both robustness measures, and each difference is small relative to its interval. The supported reading is no measurable gain in either, which is weaker and more accurate than reading the transfer deficit as a robustness deficit. Table 2: Robustness measures. The three quantities separated (%), averaged over six datasets and three seeds. Transfer is off-diagonal accuracy, degradation is on-diagonal minus off-diagonal accuracy, and retention is off-diagonal divided by on-diagonal. Quantity RNV RFM RFM−-RNV 95% interval Transfer 52.0 50.5 −1.5-1.5 [−4.6,+3.3][-4.6,+3.3] Degradation 42.0 40.4 −1.6-1.6 [−5.4,+1.8][-5.4,+1.8] Retention 55.3 55.6 +0.2+0.2 [−2.9,+4.6][-2.9,+4.6] The result does not depend on which cells are excluded. Whether an MSC comparison satisfies the positive-slope condition can depend on the sample, so we repeat the comparison while excluding the raw and scatter-corrected cells in the four datasets where the condition holds for every evaluated spectrum. The result is unchanged, at 49.849.8 against 48.348.3, giving −1.5-1.5 with an interval of [−4.8,+3.5][-4.8,+3.5]. Excluding no cells gives −1.5-1.5 and excluding these cells everywhere gives −1.6-1.6, so the three rules agree to within 0.10.1 points. On the removed cells the two representations are near ceiling and nearly identical, at 94.794.7 against 94.494.4, which is the internal check the theory predicts. The comparison has limited power for smaller effects. The paired standard deviation across the six datasets is 5.75.7 points, so at 8080 percent power and a two-sided level of 0.050.05 the comparison requires a difference of about 8.18.1 points. It therefore does not rule out smaller effects, and a gain of 33 points could easily go undetected. Separating effects that small needs more evaluation datasets rather than more spectra. No individual contrast reverses it. None of the seven contrasts in Table 1 shows RFM reliably ahead. The largest is derivative transfer, where the mean difference is −21.7-21.7 and the sign is negative on all six datasets, at −62.2-62.2, −23.8-23.8, −21.1-21.1, −14.3-14.3, −5.1-5.1, and −3.6-3.6. We do not claim significance for it. The sign test gives 0.0310.031, which would not survive correction for seven comparisons, and a paired t interval is [−44.2,+0.8][-44.2,+0.8]. What we rely on instead is the consistent sign, a magnitude an order larger than the other contrasts, and a mechanism in Section 4.6 that predicts it. The contrast between spectra with and without baseline removal is negative on five of six datasets and much smaller, so we treat it as suggestive only. Asymmetric least squares is the only contrast with a clearly positive point estimate for RFM, and its interval also includes zero. The ordering is stable under every variation we tried. Normalization is ahead on five of the six datasets. The exception is the environmental dataset, a two-class task on which RFM is substantially ahead. That exception deserves a caveat cutting against the encoder: it is also the smallest at 230 spectra and one of the most replicate-heavy, with 87 of those 230 in near-duplicate clusters (Appendix I). It is the weakest of the six datasets and the only one carrying the encoder’s win. Four changes to the protocol leave the ordering intact. A radial-basis support vector machine in place of the linear probe gives −0.3-0.3. Selecting the probe penalty inside each training fold gives −1.2-1.2. Keeping repeated measurements of one physical sample together gives −1.2-1.2, although grouping lowers absolute accuracy for every representation. Refitting the scatter-correction reference and the PCA basis inside each fold leaves the difference at −1.5-1.5. The breakdowns are in Appendices F, H, I, and J. 4.4 Where the apparent advantage came from An earlier internal evaluation of this model reported an 18-point advantage over raw spectra. Recomputing it under four changes to the protocol shows where that advantage came from, and it is not the encoder. The evaluation is our own, carried out before the analysis in this paper and not previously published. Its protocol was a four-by-four grid over raw spectra, standard normal variate normalization, baseline removal, and a crude derivative, scored as retention, on six datasets of which five were also in the pretraining corpus. We recompute rather than quote it, so every row of Table 3 comes from the released code and the same checkpoint. Three properties of that evaluation could explain the gap. Five of its six datasets were in the pretraining corpus, so the model had seen the evaluation spectra even though pretraining was label-free. Its transformation set reused the augmentation family the model was trained on, which tests robustness to changes the model was explicitly trained to ignore rather than to new preprocessing. And some of its cells compare preprocessing states that the ideal normalization removes. We control the first by removing the dataset overlap and remeasuring, which does not reduce the gap (Table 3, step 1), the second by including out-of-family pipelines, and the third by excluding the removed cells. Figure 2: The gap under successive changes. RFM minus raw spectra (points) at each step of Table 3: 0 the original protocol, 1 without dataset overlap, 2 without the removed cells, 3 without the ratio, 4 out-of-family pipelines only. Step 0 is pale because the prior protocol carries no interval. Steps are cumulative. Figure 3: What each stage contributes. Change in off-diagonal balanced accuracy (points), with dataset-level paired bootstrap intervals. RNV improves clearly on raw spectra, adding RFM on top of it does not, and the third row repeats that comparison on derivative transfer alone. Table 3: Where the advantage came from. The originally measured gap over raw spectra (points), recomputed under a sequence of changes to the evaluation. Steps are cumulative rather than independent, so consecutive rows are not an additive decomposition. Rows 0 to 2 are scored as retention and rows 3 to 4 as absolute accuracy, both in percent. Gaps are differences of unrounded values, so a column difference can differ by 0.10.1. Step Change to the evaluation Metric RFM Raw Gap 0 Original protocol Retention 67.0 49.0 +18.0+18.0 1 Without dataset overlap Retention 65.4 45.4 +20.0+20.0 2 Without the removed cells Retention 54.5 55.7 −1.2-1.2 3 Without the ratio Absolute 49.6 50.9 −1.3-1.3 4 Out-of-family only Absolute 40.6 33.2 +7.3+7.3 The gap disappears at one step. Figure 3 shows the sequence. Removing the dataset overlap does not reduce the gap, which instead rises slightly to +20.0+20.0, so overlap does not explain the gap. The change occurs at the second step, where the gap falls to −1.2-1.2, and switching from retention to absolute accuracy leaves it effectively unchanged. A positive gap over raw spectra does remain on out-of-family pipelines, at +7.3+7.3. Measured against normalization rather than against raw spectra, however, RFM differs there by only −0.4-0.4. Normalization reproduces the effect without the encoder. Figure 3 puts numbers on the separation drawn in the introduction. The removed cells measure invariance the ideal normalization supplies with no encoder at all, and normalization accounts for the rest of the improvement over raw spectra. Normalization alone improves on raw spectra by +8.9+8.9 points, and adding the encoder on top of it changes performance by −1.5-1.5, for a net +7.4+7.4. The complete model does improve on raw spectra, but the original protocol attributes to the encoder an effect that its own normalization reproduces. 4.5 Training helps, but only on what reaches the encoder Three controls test the attribution argument rather than the model. A randomly initialized encoder checks whether the invariance needs learning at all. Width-matched controls check whether the comparison is really about dimensionality. An intervention on where a transformation is injected checks whether the mechanism behaves as the algebra says. Accuracies are percentages and differences are in points, as before, while feature distances are ratios. An untrained encoder shows the same invariance. If a normalization maps a transformed input and the original to the same vector, every encoder is invariant to that transformation, including a randomly initialized one. We measure relative feature distance, the change a transformation makes to a representation divided by that representation’s own norm, for normalization alone, for a randomly initialized encoder on top of it, and for the trained encoder. On the transformations the ideal normalization removes exactly, all three are invariant to within the numerical residual of the implementation, at 1.9×10−51.9× 10^-5, 5.7×10−65.7× 10^-6, and 1.7×10−61.7× 10^-6 for standard normal variate normalization. These shrink monotonically, which is expected and not evidence of learning: each stage averages over its input, first the patch statistics and then the pooled tokens, and averaging contracts a residual already near machine precision. On transformations that survive, all three are clearly nonzero, at 1.6931.693, 0.4450.445, and 0.0920.092 for the derivative. An evaluation reading the first set of numbers as evidence of learning would assign the same evidence to an untrained encoder. The width-matched result depends on the control. Normalization keeps up to 2,928 channels while the encoder outputs 320, so a linear probe on the former may simply have more information available. Against normalization compressed to 320 dimensions by PCA, RFM is ahead by +5.9+5.9 points on the remaining cells. That PCA basis is fitted on raw spectra, so its leading components track the large-amplitude baseline and fluorescence structure that several evaluated pipelines exist to remove. It can therefore transfer poorly for reasons unrelated to the encoder. We therefore add two controls at the same width, each averaged over ten independent draws. Table 4: Controls matched to the output width of the encoder. Accuracy (%) on the remaining cells. The right block gives RFM minus that row, in points, with its 95% interval. The random projection and the untrained encoder are each averaged over ten draws. Representation Learned Dim On-diag. Off-diag. RFM−-this 95% interval RNV, full width no ≤ 2,928 94.0 49.0 −1.6-1.6 [−5.0,+3.4][-5.0,+3.4] RNV + PCA no 320 83.2 41.5 +5.9+5.9 [+0.9,+11.2][+0.9,+11.2] RNV + random projection no 320 93.3 50.6 −3.2-3.2 [−5.9,+0.1][-5.9,+0.1] RNV + untrained encoder no 320 87.8 42.0 +5.4+5.4 [+1.9,+8.9][+1.9,+8.9] RFM, trained yes 320 90.9 47.4 – – The encoder beats its untrained self, not a random projection. The trained encoder outperforms its untrained architecture by +5.4+5.4 points, ahead on five of six datasets and positive on all ten draws. This is the clearest matched-width result, and the only comparison in Table 4 whose paired t interval, [+0.3,+10.4][+0.3,+10.4], also excludes zero. It nevertheless does not beat a learning-free random projection at the same width, where the difference is −3.2-3.2, the encoder is ahead on one of six datasets, and the sign is negative on all ten draws. That interval marginally includes zero, so we read it as no clear gain rather than as a deficit. The spread between the two linear compressions is the informative part, and it is larger than any difference in Table 4. Both reduce the same input to the same 320 dimensions by a linear map, yet one reaches 50.650.6 and the other 41.541.5, a gap of 9.19.1 points, with the trained encoder between them at 47.447.4. The natural reading is not that the encoder is poor but that the PCA control is broken for this purpose, since fitted on raw spectra it discards exactly what cross-preprocessing transfer needs. We report PCA because it is the conventional control and the random projection because it shows how far that convention can mislead. Dimensionality therefore fails to explain the ordering, and the main comparison, RFM against its own normalization, needs no reduction and no random draw. Appendix E sweeps PCA width and probe regularization and finds the width trend to be a property of the representation rather than of the penalty. Moving the injection point changes what can be learned. An encoder cannot learn from variation absent from its input. If the normalization removes a transformation exactly, no learning signal about it reaches the encoder. If the normalization only nearly removes it, only the residual reaches the encoder. We test this inside a real training loop, with the model’s own objective, optimizer, and data. A small encoder is trained for 300 steps under two conditions. They differ only in where a random gain and offset, drawn for each spectrum, are injected: before normalization, where they are reduced to the numerical residual, or after it, where they reach the encoder intact. The outcome is invariance to a held-out affine transformation applied after normalization, measured over five paired seeds that start from identical initialization within each seed. The second condition learns the invariance in every seed, with relative feature distance falling from 0.3340.334 to 0.0410.041, while the first does not, moving from 0.3340.334 to 0.3360.336. The paired difference is 0.2950.295, and the second condition has the lower distance in all five seeds. Training losses nevertheless decline smoothly in both, from 0.660.66 to 0.420.42 and from 0.680.68 to 0.400.40 in a representative seed. In the first condition the affine term is already near its floor, so the visible progress comes from the rest of the objective. A practitioner could apply gain and offset augmentation there, watch a normal loss curve, and conclude that the corresponding invariance was learned. 4.6 Contraction in representation space is not transfer Transformations that survive the normalization add a qualification to the main result, and it cuts both ways. On the pair where the encoder contracts most, it also transfers worst. We measure geometry by relative feature distance, defined for a representation h and a pair of pipelines T1,T2T_1,T_2 as the median over spectra of ∥h(T2(x))−h(T1(x))∥2/∥h(T1(x))∥2 h(T_2(x))-h(T_1(x)) _2/ h(T_1(x)) _2, so that the scale of the representation cancels. The same pair is used for feature distance and for transfer, so both describe the same change. Training does pull the two derivatives together. Between the crude and the Savitzky–Golay derivative, the pair reported in Table 1, the trained encoder reduces this distance to 0.0540.054, against 0.1630.163 for the same encoder untrained and 0.6800.680 for normalization alone. The contraction is not supplied by the normalization. Training reduces the distance by about a factor of three relative to the untrained encoder and places the two about twelve times closer than normalization alone. Taken on its own, this is evidence of learned invariance. The derivative is also where transfer is worst. The derivative is the contrast on which RFM falls furthest behind its normalization, at −21.7-21.7 points. Part of that is representation quality rather than transfer, since accuracy within the derivative pipeline is 85.685.6 for RFM against 91.691.6 for normalization. Quality does not explain the whole gap. Retention over the derivative block, which divides that quality difference out, is still lower for RFM, at 68.568.5 against 75.275.2. The loss is also directional. RFM is comparable to normalization transferring from the crude to the Savitzky–Golay derivative, at 61.261.2 against 59.959.9, but much worse in reverse, at 56.156.1 against 77.877.8. The tokenizer may explain part of the deficit. One alternative explanation deserves stating, because we cannot exclude it. The encoder tokenizes fixed-size patches of native channels and summarizes each by statistics that include its mean and standard deviation, while carrying the patch’s mean wavenumber as a positional input. Differentiation changes those patch statistics drastically, roughly zeroing the patch mean and rescaling the spread, while the positional inputs stay exactly as they were. The derivative deficit may therefore be a property of this tokenizer meeting an input its patch statistics were not shaped for, rather than a general statement about learned invariance. That would not affect the attribution argument, which rests on the comparison with the normalization the encoder is built on, but it does limit how far the derivative result should be read as a claim about representation learning. Distinguishing the two would need an encoder with a different tokenizer, which we do not have. Geometry and transfer are different properties. Pulling two representations together and preserving a decision boundary across them are not the same thing. A representation can bring two closer by discarding the variation that distinguishes them, and if that variation also carries class information, transfer worsens. Feature distance measures geometry, transfer measures whether a fixed probe still applies, and here the two move in opposite directions. We therefore state the main claim at the task level and report geometry separately. Representation-similarity metrics show the same dissociation, since a deterministic normalization can raise both similarity and apparent transfer by collapsing inputs before the encoder. Appendix K gives the numbers. 4.7 The same potential confound in released systems The attribution issue is not specific to this model. It arises whenever a deterministic normalization removes a transformation that is also the subject of an invariance claim. To show that the two occur together in released systems, and that the numerical test separates positive from negative cases, we ran it over the preprocessing code of eighteen configurations of seventeen systems across five signal modalities. Appendix C gives the verdicts and the evidence behind each one, and Appendix D then runs the comparison of Section 4.3 on two of these systems, using their own released weights. Twelve supply the invariance, and four carry a matching claim. Twelve of the eighteen normalizations remove at least part of the positive affine variation by design. In four of those, the released code places the normalization between the transformation and the learned parameters, so the published evidence alone does not isolate a learned contribution. The other eight carry no matching claim we could identify, and the remaining six do not supply the invariance. A verdict of permits confounding does not mean a claim is false or that a model lacks robustness. It means the published evidence does not include the comparison needed to separate normalization from learning. Placement determines whether the augmentation reaches the encoder. Per-sample normalization is common across spectral, audio, ECG, EEG, and PPG pipelines. Where an affine augmentation is present as well, the relevant distinction is where it is applied. One PPG model applies gain augmentation after normalization, where it reaches the encoder, while device gain arriving before normalization at inference is removed. 5 Conclusion We revisited what a cross-preprocessing transfer grid measures. High transfer is not by itself evidence of learned preprocessing invariance, because a deterministic normalization can impose part of that invariance before any learned parameter is applied. For an ideal normalization that subtracts a location statistic and divides by a scale statistic, two inputs have the same normalized representation if and only if they differ by a positive affine map. Transfer across such a pair cannot be attributed to the encoder. For the Raman model studied here, evaluated within each dataset, normalization alone matches RFM on cross-preprocessing transfer, including the improvement over raw spectra, and the difference remains −1.5-1.5 points after excluding the cells the ideal normalization removes. Training does have a measurable effect. It improves the same encoder over random initialization and pulls surviving transformations closer in representation space. What we do not find is a gain in transfer or robustness beyond the normalization, against effects of 8.18.1 points and larger. The regime the encoder is built for, one probe shared across instruments, is untested here, since the six datasets have disjoint label spaces. The recommendations are simple, and apply to any model whose first operation is a fixed normalization. Recommendations 1. Identify the deterministic operations applied before any learned parameter, and test which evaluated transformations they already remove. 2. Do not treat transfer across an exactly removed transformation as evidence of learning, and report the residual where removal is only approximate. 3. Report the normalization alone as a comparison with zero learned parameters, so that what the encoder adds is visible. 4. Run the same numerical test before training, since an augmentation the normalization removes cannot teach the encoder about that variation. We hope this encourages the field to report what a model’s own normalization already supplies before crediting its encoder. Limitations. The main comparison has 8080 percent power for a difference of about 8.18.1 points, so it does not rule out smaller effects. Several contrasts whose bootstrap intervals exclude zero do not do so under a paired t interval. The finding is not confined to one model, since two released systems behave the same way, but it rests on six evaluation datasets and some intervals remain wide. Width-matched controls depend on the reduction method, frozen probes measure something different from fine-tuning (Kumar et al. 2022), and three protocol choices are relaxed in Appendices H, I, and J without changing the ordering. The absolute numbers should therefore be read as transfer under this protocol, not as estimates for an unseen specimen. The audit reads released preprocessing code and shows that the two ingredients co-occur in released systems, but beyond the two systems of Appendix D it establishes possibility rather than occurrence. Finally, the theorem applies to an ideal normalization, and the deployed stabilizer and clipping break exact equality, so we keep symbolic and numerical removal separate. Broader impact. This work uses public, de-identified spectral datasets released for research under their stated licenses and introduces no new human-subject data. Several are clinical or diagnostic in origin, so overstated preprocessing robustness could encourage deployment across laboratories or acquisition pipelines without appropriate revalidation. Code, results, the numerical test, and figure scripts are released to support independent verification (Appendix L). References Baevski et al. (2020) A. 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Barlow Twins: self-supervised learning via redundancy reduction. In ICML, 2021. Appendix A Experimental Details A.1 Datasets We use six public Raman classification datasets. Four are distributed through RamanBench (Koddenbrock et al. 2026), and two were curated separately from their original public releases. The forensic dye and serum datasets are surface-enhanced, and are released under C BY 4.0. The blood and skin dataset is released by AIT brainlab and MIT. From each dataset we retain at most 300 spectra per class using a fixed random state and sampling without replacement, and we drop classes with fewer than ten remaining spectra. Table 5 reports the counts after that filtering. Table 5: The six evaluation datasets. Counts are after subsampling and class filtering. Identifier Domain n Classes Channels Axis (cm-1) Source cancer_cell_cooh Cancer cell lines 631 12 2,090 100–4278 RamanBench ait_glucose_blood_skin Blood and skin 435 6 1,999 801–1599 AIT brainlab hair_dyes_sers Forensic dyes 1,050 4 1,340 309–1952 RamanBench chlorinated_samples Environmental 230 2 2,473 350–3500 RamanBench serum_biofluids Serum 370 4 2,928 −310-310–3271 Zenodo 5644790 alzheimer Saliva 575 2 885 401–1598 RamanBench The six datasets differ in channel count by more than a factor of three and in spectral coverage by more than a factor of five, so we do not impose a common grid. Spectra are not interpolated onto a shared wavenumber axis. RFM tokenizes native channels into fixed-size patches and uses the mean wavenumber of each patch as a positional input, so each dataset is processed on its own acquisition axis. The normalization, PCA, random-projection, and raw representations use the same native channels. This removes interpolation as a source of difference between them. A.2 Preprocessing pipelines All preprocessing is applied to the raw intensities, before any representation is computed. The identity gives raw spectra. The baseline step, which is in-family, is the rolling-minimum operation as released, x+(x−min(x,roll(x,8)))x+(x- (x,roll(x,8))) with a shift of eight channels. The released implementation subtracts the rolling-minimum baseline and then adds the original signal back, so the result is not the difference alone. We reproduce the released operation rather than correcting it, because the encoder was pretrained with it and all reported results use it. The crude derivative, also in-family, is the central first difference di=(xi+1−xi−1)/2d_i=(x_i+1-x_i-1)/2 with zero endpoints. Asymmetric least squares baseline removal, out-of-family, uses smoothness 10510^5, asymmetry 0.010.01, ten iterations, a second-difference penalty, and the standard reweighting of each spectrum. Multiplicative scatter correction, also out-of-family, fits x≈b+mrefx≈ b+m\,ref by ordinary least squares with an intercept and returns (x−b)/m(x-b)/m, guarding against a near-zero slope. The reference is the mean over all spectra in the dataset, so held-out spectra contribute to that dataset-level statistic. The coefficients m and b are still fitted on each spectrum itself, so Corollary 3.1 and the removal verdicts are unchanged. Transfer results involving MSC are therefore transductive in the primary protocol, and Appendix J removes that dependence. The Savitzky–Golay first derivative, also out-of-family, uses window length eleven and polynomial order three. Standard normal variate normalization is excluded from the main grid because the ideal normalization removes it exactly, and the deployed RNV removes it to a small numerical residual. A.3 Representations and probing protocol This subsection expands the protocol summarized in Section 4.1. The raw representation is the preprocessed intensities, unchanged. The normalization representation is the model’s own first operation, taking its statistics from each spectrum across channels and using zero learned parameters. PCA is fitted on raw spectra with a fixed random state and then applied unchanged to every pipeline. Its width is capped by the number of channels and samples. It uses no labels, and the same basis is used across pipelines. In the primary protocol the basis is fitted on all inputs of a dataset rather than on the training fold, so it uses held-out inputs. The random projection applies a fixed standard Gaussian matrix to the normalized spectra and is shared across pipelines. The untrained encoder uses the same size configuration and a fixed seed and is never trained. RFM is the frozen checkpoint with mean-pooled 320-dimensional features. Its weights and code are in the accompanying package (Appendix L). Probing uses five-fold stratified cross-validation with shuffling. The fold partition is determined by the seed and shared across all pipeline pairs within a seed, so every cell of a transfer grid uses the same split, and results are averaged over three seeds. The probe is standardization followed by multinomial logistic regression with a fixed inverse regularization strength of one and a maximum of one thousand iterations. For each source pipeline the probe is fitted once per fold on the training indices of that pipeline, then applied to the held-out indices of every other pipeline. Each cell reports the balanced accuracy of these out-of-fold predictions. Standardization statistics come from the source pipeline only and are never refitted on the target, which is what makes each cell a test of the representation rather than of test-time adaptation. No hyperparameter is tuned for any representation in the primary protocol. Appendix H repeats the comparison with source-only selection of the penalty. The alternative probe is a support vector machine with a radial basis kernel under the same pipeline and folds. Intervals are paired bootstrap intervals over the six datasets with ten thousand resamples and a fixed seed. We resample datasets rather than spectra because the claim concerns generalization across evaluation datasets rather than across spectra within one. With six datasets the six per-dataset values are the evidence and the interval only summarizes them, which is why we report every per-dataset effect alongside every aggregate. Three choices in the primary protocol could favor one representation over another, and each is relaxed in its own appendix. The probe penalty is fixed at one operating point for all representations, although they differ in width and geometry, and Appendix H selects it inside each training fold from the source pipeline only. Folds are formed over spectra, although several datasets contain repeated measurements of one specimen, strip, or product, and Appendix I states the experimental unit of each dataset and repeats the comparison with those measurements held together. The scatter-correction reference and the PCA basis are fitted on all inputs of a dataset rather than on the training fold, and Appendix J repeats the comparison with both fitted inside the fold. Appendix B Ideal Versus Deployed Normalization For each spectrum we take the largest absolute channel-wise difference between the normalized transformed spectrum and the normalized original, then divide by the spread of the normalized original. Table 6 reports that deviation over all six evaluation datasets, with the deployed output clipped to [−8,8][-8,8]. Table 6: Residual of the deployed normalization. Largest channel-wise deviation per spectrum, divided by the spread of the normalized original, over all six evaluation datasets. The three transformations above the rule are removed exactly by the ideal normalization. The one below is the boundary case the corollary predicts. Transformation n Median p95 p99 Max Above 10−310^-3 SNV 3,291 4.1×10−64.1× 10^-6 2.9×10−42.9× 10^-4 9.6×10−49.6× 10^-4 3.0×10−33.0× 10^-3 0.9% Area normalization 3,291 1.7×10−51.7× 10^-5 3.2×10−43.2× 10^-4 1.0×10−31.0× 10^-3 3.1×10−33.1× 10^-3 1.0% MSC, positive slope 3,233 2.4×10−92.4× 10^-9 9.1×10−59.1× 10^-5 4.5×10−44.5× 10^-4 3.1×10−33.1× 10^-3 0.2% MSC, negative slope 58 6.96.9 9.59.5 13.313.3 14.014.0 100% Two readings follow, and we keep them separate. First, the sign boundary matches the theory. Scatter correction with negative slope has a residual six to nine orders of magnitude larger than the other three cases. The second is a caveat. For the three transformations removed exactly by the ideal normalization, the typical spectrum agrees to machine precision, but the distribution has a small tail. Depending on the transformation, between one spectrum in a hundred and one in five hundred exceeds 10−310^-3, and the maximum is about 3×10−33× 10^-3. Taking the maximum over the sample therefore places all three just above the threshold of the numerical test. These transformations are exactly removed by the ideal normalization and nearly removed by the deployed one, and we do not claim exact numerical collapse for the deployed normalization on these data. The tail comes from the stabilizer and the clipping. It is concentrated in spectra whose percentile spread is small enough that the stabilizer is non-negligible, which is also where the ideal identity is most fragile. Area normalization also requires a positivity check. Its divisor is positive for all 3,291 spectra, with a minimum of 7.6×10−37.6× 10^-3, so the condition holds on these data. The downstream analysis does not require treating these transformations as numerically collapsed. Standard normal variate normalization is excluded using Corollary 3.1, not a numerical threshold, and for scatter correction the three exclusion rules in Section 4.3 agree to within 0.10.1 points. On the synthetic suite of transformations the threshold is not delicate, because the two populations are far apart. Across the eight transformations and both modalities, the largest deviation in the removed set is 3.4×10−53.4× 10^-5 and the smallest in the surviving set is 5.375.37. The resulting partition is unchanged for thresholds from 10−410^-4 to 10−110^-1. Below 10−410^-4 the scale and affine transformations fall outside the removed set, which reflects the numerical floor from the stabilizer and floating-point precision rather than meaningful survival of the transformation. We recommend that users of the test report the deviation rather than only a verdict, inspect the distribution behind it, and check whether their transformations fall in a similarly separated regime. Table 7: Verdicts of the numerical test. Whether each normalization removes each transformation. The suite contains eight transformations, so the test evaluates 5×8=405× 8=40 cases per modality. Derivative, baseline removal, and smoothing receive identical verdicts under every normalization, so they are collapsed into one non-affine column and the table displays 30 of the 40 cells. Normalization axax x+bx+b ax+bax+b −ax-ax Per-channel gain Non-affine None no no no no no no z-score yes yes yes no no no RNV yes yes yes no no no L2L_2 norm yes no no no no no Min-max yes yes yes no no no Table 7 lists the verdicts. The same test on 4,998 ECG heartbeat time series gives verdicts identical to the Raman ones on all forty combinations of normalization and transformation. We also verified the converse numerically. Recovering the implied positive affine coefficients reconstructs affine and positive-slope scatter-corrected spectra with relative error near 10−1610^-16 in both modalities. Negative-slope scatter correction and derivatives fail by many orders of magnitude. Appendix C Audit of Released Preprocessing Code Table 8 covers eighteen model configurations across five modalities. Verdicts describe the configuration, not the correctness of any published result. Permits confounding means the normalization removes a transformation that is also the subject of an invariance claim, so the published evidence alone does not isolate a learned contribution. Supplies only means the normalization supplies the relevant invariance but we identified no matching claim. Does not supply means the normalization does not remove the transformation. Table 8: Audit verdicts. Eighteen configurations of seventeen systems across five modalities. Twelve supply invariance to positive affine variation, and four of those carry a matching claim. Model Modality Normalization as released Verdict RSPTE (Eranti et al. 2026) spectra per-spectrum min-max permits confounding PaPaGei (Pillai et al. 2025) PPG per-segment z-score permits confounding1 BIOT (Yang et al. 2023) EEG divide by 95th pct. of |x||x| permits confounding2 RFM, this paper spectra per-spectrum RNV permits confounding wav2vec2-L (Baevski et al. 2020) audio per-utterance z-score supplies only HuBERT-L (Hsu et al. 2021) audio per-utterance z-score supplies only WavLM-L (Chen et al. 2022) audio per-utterance z-score supplies only ECG-FM (McKeen et al. 2025) ECG per-record z-score supplies only ST-MEM (Na et al. 2024) ECG per-record z-score supplies only HuBERT-ECG (Coppola et al. 2025) ECG per-lead min-max supplies only DSCF (Xue et al. 2025) spectra per-spectrum min-max supplies only BENDR (Kostas et al. 2021) EEG per-trial min-max3 supplies only wav2vec2-base (Baevski et al. 2020) audio none does not supply LaBraM (Jiang et al. 2024) EEG divide by 100 does not supply CBraMod (Wang et al. 2025) EEG divide by 100 does not supply HeartBEiT (Vaid et al. 2023) ECG fixed constants does not supply ecg-selfsupervised ECG global constants does not supply4 Pulse-PPG (Saha et al. 2025) PPG per-person does not supply4 1The augmentation is applied after normalization, so the exposure concerns device gain at inference rather than the training augmentation. 2No location statistic is subtracted, so the normalization is invariant to gain but not to offset. 3A separate scale channel retains gain information until saturation. 4Negative controls, where an affine augmentation survives a normalization that is not per sample, or is declined on domain grounds. Table 9 gives the evidence behind each verdict. Every entry names the normalization first, then the augmentation or robustness claim if we located one, then any caveat. Locations are the file and line range in the public repository as read, or the place in the paper where the evidence is a claim rather than a line of code. The second column records whether we found a matching affine augmentation or robustness claim. Table 9: Sources consulted, by row. Line numbers are as read and may drift as repositories change. Model Matching aug./claim Source consulted RSPTE yes Normalization: per-spectrum min-max to [0,1][0,1], IEEE Access 14:40311–40327 (2026), Fig. 5. Augmentation: random intensity scaling in [0.9,1.1][0.9,1.1], stated as simulating intensity variation. PaPaGei yes Normalization: per 10 s segment z-score, Nokia-Bell-Labs/papagei, dataset.py L64–67. Augmentation: Scaling with gain drawn from (1,σ)N(1,σ), augmentations.py L44–51, reported among the applied augmentations. BIOT yes Normalization: divide by the 0.95 quantile of |x||x|, ycq091044/BIOT, utils.py L28–31. Claim: the paper gives the purpose as alleviating unit and amplitude mismatch across channels and datasets. RFM, this paper yes Normalization: robust_normalize() called inside tokenize(), model.py. Augmentation: physics_augment() applies gain and offset. wav2vec2-L, HuBERT-L, WavLM-L no Normalization: F.layer_norm over the utterance, fairseq, raw_audio_dataset.py L93–95, with normalize: true in the large configs. The three share this preprocessing path. No gain or volume augmentation in the task definition. ECG-FM no Normalization: per-lead per-record z-score, on by default, fairseq-signals, scripts/preprocess/ecg/preprocess.py L181–188. The dataloader normalize flag applies dataset constants instead. ST-MEM no Normalization: Standardize per recording, vuno/ST-MEM, util/transforms.py L140–152, present in both the train and eval transform lists. We read the augmentation registry in full and found no gain and no offset. HuBERT-ECG no Normalization: bandpass 0.050.05–4747 Hz then per-lead min-max, Edoar-do/HuBERT-ECG, hubert_ecg/utils.py L42–88. We read the pretraining path in full and found no augmentation of the signal. SpecAugment masks hidden states, which the normalization does not reach. DSCF unresolved Normalization: per-spectrum min-max, streamflowmaster/DSCF, preprocessing/dataset.py L104–117. The augmentation description is paywalled, so a matching claim could not be confirmed or excluded. BENDR unresolved Normalization: utils.min_max_normalize per trial, dn3. MappingDeep1010 writes a separate scale channel that retains gain information until clamping, so offsets are removed exactly and gain only partially. wav2vec2-base no Normalization: normalize: false in the base configs, with normalization inside the first encoder layer instead (§4.2). A widely used redistribution ships do_normalize: true, so the verdict is checkpoint dependent. LaBraM no Normalization: data / 100, data_preprocess.py L10–11. A per-sample z-score exists at make_TUEV.py L29–30 but is commented out. CBraMod no Normalization: data / 100, datasets/tuab_dataset.py L31. The curation rule if np.max(np.abs(sample)) < 100 makes which samples are kept depend on absolute amplitude, so the preprocessing is actively gain sensitive. HeartBEiT no Normalization: Normalize(mean=[0.5]*3) with fixed constants, finetune.py L34–45. The waveform-to-image scaling is unverified, because the plotting code is not released. hhi-aml/ecg-selfsupervised yes Normalization: global constants rather than per-sample statistics. Augmentation: ChannelResize scales amplitude between one half and twice the original, so the change is not nullified. Negative control. Pulse-PPG no Normalization: per-person rather than per-sample z-score. The paper explicitly declines scaling augmentation, on the grounds that amplitude is critical for inferring blood volume. Negative control. Two rows are unresolved and are classified conservatively as supplying only, since assigning them to the permitting category would require a claim we did not verify. We record file and line ranges as read rather than commit hashes, so line numbers may drift as repositories change. The audit script reruns the normalization itself, which does not depend on repository state. Readers checking the source evidence should therefore expect to locate the same code, not necessarily the same line numbers. Appendix D Replication on Two Released Systems The main result compares one model with its own normalization, so it could be a property of that model rather than of the comparison. We therefore run the same comparison on two released systems. DSCF (Xue et al. 2025) is a spectral foundation model with 397 million parameters. HuBERT-ECG (Coppola et al. 2025) is an electrocardiogram encoder with 30.5 million parameters. Both appear in Table 8, classified from their released code before these measurements were made. Each normalizes every input before its encoder, as RFM does. DSCF uses a min-max over each spectrum, and HuBERT-ECG uses a min-max over each lead. Min-max normalization satisfies the assumptions of Theorem 3.1, so both remove the positive affine variation that RNV removes. We use the protocol of Section 4.1 unchanged. For each model we fit a probe under one preprocessing pipeline, evaluate it under the others, and report balanced accuracy. We compare each model with its own normalization, and each normalization with raw signals. These are the two comparisons of Table 1. Each model receives the input format it requires. DSCF requires 512 samples, so every input compared with it is interpolated to that length. HuBERT-ECG requires twelve leads of five seconds, and its task is the five-way diagnostic superclass problem on PTB-XL. Both models are frozen here. Their published results, however, come from fine-tuning, so we make no claim about those numbers. Table 10: Replication on two released systems. The main contrasts (points), each model against its own normalization, with 95% intervals. Intervals resample the six datasets for the Raman columns and held-out records for HuBERT-ECG. Contrast RFM DSCF HuBERT-ECG Normalization −- raw +8.9+8.9 [+4.6,+13.8][+4.6,+13.8] +8.9+8.9 [+2.5,+15.9][+2.5,+15.9] +4.4+4.4 [+3.7,+5.2][+3.7,+5.2] Model −- normalization −1.5-1.5 [−4.6,+3.3][-4.6,+3.3] −5.4-5.4 [−12.5,−1.0][-12.5,-1.0] +10.8+10.8 [+9.7,+12.0][+9.7,+12.0] Model −- normalization, retention +0.2+0.2 [−2.9,+4.6][-2.9,+4.6] −1.8-1.8 [−6.8,+2.7][-6.8,+2.7] −19.2-19.2 [−23.6,−15.8][-23.6,-15.8] Both models behave as RFM does. Table 10 gives the result. Each normalization improves on raw signals by +8.9+8.9, +8.9+8.9, and +4.4+4.4 points, and every interval excludes zero. No encoder is measurably more robust to a change of preprocessing than the normalization it begins with, at +0.2+0.2, −1.8-1.8, and −19.2-19.2 points of retention. However, the comparison on accuracy is not uniform, at −1.5-1.5, −5.4-5.4, and +10.8+10.8. What the three models share is therefore the robustness result rather than the transfer result. Two of the three models are released systems, and one of them is not a spectral model, so the pattern is not a property of RFM. The untrained encoder is again level with the normalization. Section 4.5 finds that the invariance RFM shows is already present in a randomly initialized encoder. The same holds for DSCF. A random initialization of its architecture reaches +0.9+0.9 points of retention over the normalization, with an interval of [−2.4,+4.4][-2.4,+4.4]. Training moves that by −2.7-2.7, with an interval of [−7.1,+1.6][-7.1,+1.6]. Training therefore adds nothing measurable here, unlike for RFM, where it does improve the encoder. HuBERT-ECG separates transfer from robustness. It is 10.810.8 points better than its own normalization at the task and 19.219.2 points worse at surviving a change of pipeline, and both intervals exclude zero. It is the better representation and the less preprocessing-invariant one. As Section 4.6 reports the same split for RFM between the two derivative pipelines, we report transfer and robustness separately throughout. Appendix E Dimensionality and Probe Regularization Table 11 sweeps the PCA width. The table is computed on the remaining cells, which is why the entry at 320 dimensions reads +5.9+5.9 here and +7.5+7.5 when all off-diagonal cells are included. The difference is the contribution of the removed cells, on which both representations sit at ceiling. Table 11: PCA width sweep. Accuracy (%) on the remaining cells. Degradation is on-diagonal minus off-diagonal. The right block gives RFM minus that row, in points, with its 95% interval. Derived columns are computed before rounding, so a column difference can differ by 0.10.1. Representation On-diag. Off-diag. Degradation RFM−-this 95% interval PCA 128 90.2 45.5 44.8 +1.9+1.9 [−3.5,+7.5][-3.5,+7.5] PCA 320 83.2 41.5 41.7 +5.9+5.9 [+0.9,+11.2][+0.9,+11.2] PCA 640 73.8 36.7 37.1 +10.7+10.7 [+5.1,+16.7][+5.1,+16.7] PCA 1024 71.2 35.6 35.5 +11.7+11.7 [+7.2,+17.1][+7.2,+17.1] RFM 90.9 47.4 43.5 – – RNV, full width 94.0 49.0 45.0 −1.6-1.6 [−5.0,+3.4][-5.0,+3.4] Increasing the PCA width reduces both on-diagonal and off-diagonal performance. The decrease on the diagonal is at least as large, so the widening gap does not behave like a stable invariance effect. Transfer degradation is similar for RFM and for full-width normalization, at a difference of −1.5-1.5 points. A retention-based comparison at matched width is also not decisive. RFM exceeds normalization followed by PCA by +7.7+7.7 points on the diagonal and by +3.9+3.9 in retention, but against full-width normalization its retention advantage is only +0.2+0.2. Normalization exceeds raw spectra by +8.4+8.4. Re-running the two extreme widths over inverse regularization strengths of 0.010.01, 0.10.1, 11, and 1010 changes off-diagonal accuracy by at most 2.62.6 points at 128 dimensions and 1.21.2 at 1024. The gap between the two widths stays close to 1010 points at every setting, which suggests the width effect is not driven by the probe penalty. That sweep varies the penalty at a fixed width. Appendix H instead lets every representation choose its own. Across ten draws the two random controls are stable. The random projection is 50.650.6 with a standard deviation of 0.50.5, and the untrained encoder is 42.042.0 with a standard deviation of 0.30.3. Neither comparison with the trained model changes sign across draws. The single draw we first examined turned out to be the most favorable of the ten for the random projection, which would have overstated the effect. Appendix F Per-Dataset and Probe-Class Breakdowns Table 12 gives the main comparison one dataset at a time, and Table 13 repeats the three headline contrasts under a second probe family. Table 12: Per-dataset breakdown. Off-diagonal accuracy (%) by dataset, best per row in bold. Dataset n Classes Raw RNV RFM Cancer cell lines 631 12 25.8 45.3 43.2 Blood and skin 435 6 31.0 41.7 36.6 Forensic dyes 1050 4 41.1 52.2 46.7 Environmental 230 2 59.3 61.6 71.2 Serum 370 4 43.4 47.9 46.5 Saliva 575 2 58.4 63.5 58.9 Ahead on 0/6 5/6 1/6 Table 13: Probe family. The main contrasts (points) under a linear probe and under a radial-basis support vector machine. Contrast Linear probe RBF probe RFM −- RNV, off-diagonal −1.5-1.5 −0.3-0.3 RFM −- RNV, retention +0.2+0.2 +1.2+1.2 RNV −- raw, retention +8.4+8.4 +6.3+6.3 Appendix G Chance-Level Rescaling The six datasets carry between two and twelve classes, so chance balanced accuracy ranges from 5050 to 8.38.3 percent, and an average of absolute accuracies mixes quantities on different scales. Each contrast is paired within a dataset, so both representations face the same chance level, but the absolute column means of Table 1 combine datasets on different scales. We therefore repeat the comparison with each dataset rescaled by its own chance level, as (accuracy−chance)/(1−chance)(accuracy-chance)/(1-chance). On that scale normalization reaches 31.231.2 and RFM 30.030.0, against 19.619.6 for raw spectra. Normalization exceeds raw spectra by +11.6+11.6 points with an interval of [+7.3,+16.2][+7.3,+16.2] and is ahead on all six datasets, while RFM differs from normalization by −1.3-1.3 points with an interval of [−7.1,+7.4][-7.1,+7.4]. The ordering is the same as on the unscaled numbers. Appendix H Source-Only Selection of the Probe Penalty The primary grid gives every representation the same probe at the same fixed penalty. That choice is deliberate, since tuning per representation introduces a second difference between the objects being compared. It is also a risk. The representations differ in width and geometry, with normalization keeping up to 2,928 channels against the encoder’s 320, so a single operating point could favor one of them. The conclusion would then be partly a statement about the probe rather than about the representation. We therefore repeat the comparison with the penalty selected per representation, from source data only. Within each training fold, and separately for each representation, the penalty is chosen from 0.01,0.1,1,10\0.01,0.1,1,10\ by a three-fold inner cross-validation that sees only the source pipeline. The selected probe is refitted on the whole training fold of the source pipeline and applied, untouched, to the held-out spectra of every target pipeline. Neither the target pipeline nor any held-out spectrum takes part in the selection, so the grid still measures the representation rather than test-time adaptation. Table 14: Source-only penalty selection. Off-diagonal accuracy (%) at a fixed penalty and with the penalty selected inside each training fold. Changes are computed before rounding. The last column gives how often each of C=0.01C=0.01, 0.10.1, 11, and 1010 was selected. Representation Fixed C=1C=1 Tuned Change Penalty selected (%) Raw 43.2 42.9 −0.3-0.3 19 / 16 / 17 / 48 PCA 41.3 41.3 +0.0+0.0 12 / 30 / 30 / 28 RNV 52.0 51.7 −0.3-0.3 25 / 21 / 17 / 36 RNV+PCA 43.0 43.3 +0.2+0.2 22 / 13 / 24 / 40 RFM 50.5 50.5 −0.0-0.0 25 / 25 / 30 / 20 Table 14 reports the result. The selection is not degenerate, since different representations prefer different operating points, and normalization selects the weakest penalty in the grid more than a third of the time while RFM spreads its choices more evenly. Tuning therefore had something to choose, and was free to favor either side of the main comparison. It did not. Every representation moves by at most 0.30.3 points, and the ordering is unchanged. Normalization still exceeds raw spectra by +8.8+8.8 with an interval of [+4.6,+13.7][+4.6,+13.7] and is ahead on all six datasets. RFM is still behind its own normalization, by −1.2-1.2 with an interval of [−4.4,+3.2][-4.4,+3.2] and ahead on one of six datasets. Restricted to the remaining cells the difference is −1.3-1.3. On the two robustness measures, degradation is −2.0-2.0 and retention is +0.6+0.6, both with intervals spanning zero, so the pattern of Table 2 also survives. The encoder is behind on transfer and nominally ahead on robustness, and neither margin is measurable. Two limits of this check are worth stating. The grid covers the penalty of one probe family rather than the probe family itself, so it does not exclude the possibility that some other classifier would favor the encoder. The radial-basis replication in Appendix F is the only evidence we offer on that question. And selection uses inner cross-validation on the source pipeline, which is the appropriate criterion when the target pipeline must remain untouched, but it optimizes within-pipeline accuracy rather than transfer. A practitioner who could see target data would tune differently, and would then be measuring something other than what this grid is for. Appendix I The Experimental Unit and Grouped Cross-Validation Raman datasets commonly contain several spectra of one physical unit: a specimen, a substrate, a culture, a product, or a subject. If those spectra fall on both sides of a split, the resulting accuracy measures recall of a particular unit rather than generalization to a new one. This would matter here even if it inflated every representation, because it need not inflate them equally. What each dataset permits. The six datasets differ in what their redistributions record, as Table 15 shows. Only the serum dataset is redistributed with metadata naming the unit. Its five source figures each record a different one, namely specimen and processing, experimental run, substrate strip, strip and date, or analyte and concentration. We recover the unit of every retained spectrum from those columns, giving 60 groups over 370 spectra, none of which spans more than one class. The file data/groups.json in the code package records them. Table 15: The experimental unit of each dataset. Near-duplicate spectra are those falling in a correlation cluster of two or more, used as a proxy for the unit where identifiers were not released. Dataset Experimental unit Identifiers Near-duplicates Cancer cell lines Cultured cell-line preparation no 0 of 631 Blood and skin Physical sample, measured repeatedly no 9 of 435 Forensic dyes Commercial dye product no 305 of 1,050 Environmental Chemical solution no 87 of 230 Serum Specimen, run, strip, or analyte yes 312 of 370 Saliva Saliva sample from one individual no 52 of 575 For the remaining five, no subject, specimen, or batch column survives redistribution, so true grouped cross-validation is not possible from the released data. Rather than stop there, we use a proxy. Repeated measurements of one unit are near-identical, so we cluster spectra whose correlation is at least 0.9990.999 and treat each cluster as a putative unit. The last column of Table 15 counts spectra that fall in a cluster of two or more. The proxy over-groups wherever genuinely distinct samples are similar, which makes it conservative. It withholds more from the training fold than true grouping would. The counts are informative on their own. The cancer cell-line dataset contains no near-duplicate spectra at all, and the blood and skin dataset almost none, so replicate leakage cannot be material there. The forensic dye, environmental, serum, and saliva datasets do contain such structure. Grouping lowers accuracy and leaves the comparison intact. Grouping removes a real effect. On serum with its recorded units, off-diagonal accuracy falls by 11.611.6 points for raw spectra, 10.910.9 for normalization, and 8.58.5 for RFM. Under the proxy across the five datasets with detectable structure, the falls are 3.33.3, 2.62.6, and 2.52.5. Spectrum-level cross-validation was therefore optimistic in absolute terms, and we say so. It was optimistic in nearly equal measure for every representation, which is what the comparison depends on, and Table 16 shows that directly. Table 16: Grouped cross-validation. Main contrasts (points) at the spectrum level and under the near-duplicate proxy, on the five datasets with detectable replicate structure. Ahead counts the datasets on which the first term leads. Contrast Spectrum level Grouped (proxy) Ahead RNV −- raw +8.9+8.9 +7.4+7.4 [+4.5,+10.3][+4.5,+10.3] 5/5 RFM −- RNV −1.5-1.5 −1.2-1.2 [−5.3,+4.6][-5.3,+4.6] 1/5 RFM −- RNV, remaining cells −1.6-1.6 −1.4-1.4 [−5.8,+4.8][-5.8,+4.8] 1/5 RFM −- RNV, retention +0.2+0.2 +0.2+0.2 [−3.6,+5.6][-3.6,+5.6] 1/5 On serum alone, with its recorded units rather than the proxy, normalization exceeds raw spectra by +5.1+5.1 points and RFM exceeds normalization by +1.0+1.0. Serum is one of the datasets on which the two are closest, and a single dataset carries no interval. Two conclusions follow, and they have different strengths. The comparison between RFM and its normalization holds at the spectrum level on all six datasets, under grouped cross-validation on serum, and under the conservative proxy on the five datasets where replicate structure is detectable. It is a comparison between two representations evaluated under one shared protocol, and a protocol that inflates both equally does not disturb it. The measurements above show that grouping does inflate them nearly equally. The absolute accuracies are a different matter. They are computed with folds over spectra, and grouping lowers them by between 2.52.5 and 11.611.6 points. They should therefore be read as cross-preprocessing transfer under this protocol, not as estimates of what any of these representations would achieve on a specimen it has never seen. Three of the six datasets carry replicate structure that we could only address by proxy, since their identifiers were not released, and for those the grouping evidence is weaker than for serum. Appendix J Inductive Refit of the Data-Dependent Steps Two steps of the primary protocol are fitted on all inputs of a dataset: the scatter-correction reference, which is the mean spectrum, and the PCA basis. Neither step uses labels. The scatter-correction reference is shared across representations, and the PCA basis is shared across pipelines for the PCA-based representations, so neither can favor one over another. Both are nevertheless transductive, since a held-out spectrum contributes to a statistic that is then used to transform it. We therefore test whether this transductive fitting affects the conclusion. We therefore repeat the comparison inductively. Within each fold, both statistics are computed from the training spectra only, frozen, and applied unchanged to the held-out spectra. Everything else is already computed from each spectrum and needs no refitting, including the identity, the rolling-minimum baseline, the central difference, the asymmetric least squares baseline, the Savitzky–Golay derivative, and the normalization itself. Table 17: Inductive refit. Off-diagonal accuracy (%) with the scatter-correction reference and the PCA basis fitted on all inputs, and with both fitted inside each training fold. Representation Primary Inductive Change Raw 43.2 43.1 −0.1-0.1 PCA 41.3 43.3 +2.0+2.0 RNV 52.0 52.0 +0.0+0.0 RNV+PCA 43.0 46.4 +3.4+3.4 RFM 50.5 50.5 −0.0-0.0 Table 17 reports the result. The PCA-based representations show the largest changes, and both improve, so the transductive basis was slightly hurting the PCA controls rather than helping them. Normalization and RFM are unchanged to one decimal in this experiment. The main contrasts are unchanged. Normalization over raw spectra is +9.0+9.0 points with an interval of [+4.7,+13.8][+4.7,+13.8] and is ahead on all six datasets. RFM over its normalization is −1.5-1.5 with an interval of [−4.6,+3.2][-4.6,+3.2] and is ahead on one of six. Restricted to the remaining cells the difference is −1.7-1.7, and measured as retention it is +0.2+0.2. The transductive step therefore does not change the main conclusion. The PCA controls are the only representations that move materially, and they improve under the inductive refit. Appendix K Representation Similarity Mean linear centered kernel alignment (Kornblith et al. 2019) across the five representations is 0.5580.558 for raw spectra, 0.5760.576 for PCA, 0.7290.729 for normalization, 0.7470.747 for normalization followed by PCA, and 0.6860.686 for RFM. Normalization followed by PCA has the highest similarity but only 43.043.0 off-diagonal transfer, while normalization alone has slightly lower similarity and the best transfer at 52.052.0. Across the five representations the rank correlation between similarity and off-diagonal transfer is +0.20+0.20 with a p value of 0.750.75. This is not a general critique of the metric, whose limitations and sensitivity to design choices are known (Davari et al. 2023; Williams et al. 2021; Ding et al. 2021). The narrower point is that a deterministic normalization can raise both representation similarity and apparent transfer by collapsing inputs before the encoder. The metric alone therefore cannot separate invariance supplied by normalization from invariance acquired by the encoder. Appendix L Code and Reproduction The accompanying package includes the six datasets, the pretrained checkpoint, code, result files, and console output for every run. RFM itself is in the package, so its normalization and weights can be inspected and rerun. Every number and figure outside Appendix D is reproduced by the top-level script in about an hour on a laptop with no GPU, with no external path, download, or configuration. Separate scripts reproduce the transfer grids, the numerical test and threshold sweep, the comparison of ideal and deployed normalization, the untrained-encoder control, and the five-seed injection-point intervention. Further scripts reproduce the sensitivity sequence, the width and regularization checks, the alternative probe, source-only penalty selection, the inductive refit, the pretraining analysis, the audit, the reported contrasts, and the figures. One more script reproduces the replication of Appendix D. That is the only experiment needing a download, since it uses the released weights of the two systems and the PTB-XL recordings. Shared code is separated from the experiment scripts. Dedicated modules contain the encoder and normalization, the preprocessing pipelines, the transfer grid and bootstrap, the dataset loader, and shared paths and settings. Where a number in the text is produced by a script, that script writes it to a result file of the same name, so every value can be traced without rerunning anything.