Same Data, Different Order: Testing Representational Similarity Metrics on Curriculum-Trained Networks

Researchers compare neural networks by scoring how similar their internal activations are. The scores come from formulas such as Centered Kernel Alignment (CKA), which compares the pairwise-similarity structure of two sets of activations, and orthogonal Procrustes distance, which measures how far apart two activation clouds remain after the best rotation. A growing body of work shows these scores can be badly wrong about function. Harmless shifts of the activations can drive CKA very low, and two networks can look geometrically alike while relying on different cues. The tests used to expose these failures share a weakness, though: the networks being compared differ in many things at once, including training data, augmentation, architecture or random seed. We propose a cleaner test. We train networks on exactly the same set of training examples and vary only the order in which those examples arrive, using curricula over geometric transformations such as rotation, translation and scaling. Ordering alone can change what a network learns. Curriculum studies show order can decide whether a skill is learned at all. So the order-matched pairs are both data-matched and accuracy-matched, yet they may differ functionally. That makes them the hardest fair case for a similarity metric.

On this testbed we also evaluate a cheap metric aimed at the specific blind spot of static scores. Instead of comparing where two networks place each input, it compares how each network's representation moves when the input is rotated or shifted. Our claim is that this response-based comparison tracks transformation-conditioned behavior better than static Procrustes or CKA when data and clean accuracy are held fixed. If the claim fails, the testbed still tells us which existing metric to trust when monitoring curriculum training.

Core Claim

Curricula over geometric transformations can produce network pairs that saw the same multiset of (image, transformation) training pairs and reach the same clean accuracy, but differ in how they behave on transformed inputs. Static geometric metrics will partly miss these differences, because the differences live in how representations respond to transformations, not in where clean inputs land. A Procrustes distance computed on transformation-induced displacements will close much of that gap at the cost of one extra forward pass per transformation.

Let $Z_A$ be network A's activations on $n$ clean inputs at some layer. Let $Z_A^{g}$ be its activations on the same inputs after applying transformation $g$ (for example a 30° rotation). The response similarity between networks A and B over a family of transformations $\mathcal{G}$ is

$$ d_{\text{resp}}(A,B;\mathcal{G}) = \frac{1}{|\mathcal{G}|}\sum_{g\in\mathcal{G}} \frac{\| (Z_A^{g}-Z_A)\,Q^{*} - (Z_B^{g}-Z_B)\|_F}{\|Z_A^{g}-Z_A\|_F + \|Z_B^{g}-Z_B\|_F}. $$

Here $Q^{*}$ is the orthogonal matrix that best aligns the clean activations $Z_A$ to $Z_B$. The score asks a specific question: once we find the rotation that matches the two networks' static geometry, do the networks then move the same way under transformations? Two networks that place clean images identically but differ in invariance get a large $d_{\text{resp}}$. A network that is invariant to $g$ has near-zero displacements, so the normalization makes the score sensitive to who is invariant and who is not.

Why This Gap, and Which Prior Work Plays Which Role

Several papers motivate the proposal by showing that static metrics fail. Deceiving the CKA Similarity Measure in Deep Learning proves that translating a subset of activations can push linear CKA below 0.2 while CIFAR-10 accuracy stays at 85–90%. On the Inadequacy of CKA as a Measure of Similarity in Deep Learning extends the problem to general affine changes. Grounding Representation Similarity Through Statistical Testing finds that CKA stays high after deleting up to 97% of principal components and that PWCCA (projection-weighted canonical correlation analysis) separates seeds more than layers. Not all solutions are created equal proves that in deep linear networks hidden representations can drift freely while the input-output map stays fixed. This predicts specificity failures for any static metric when training paths differ. All four perturb representations directly or compare models trained differently. None hold data fixed and vary only the path, which is what we do.

Two papers supply the strongest existing comparators. Evaluating Representational Similarity Measures from the Lens of Functional Correspondence finds Procrustes correlates best with behavioral similarity across 19 vision models and 20 behavioral datasets. Grounding Functional Similarity by Invariance-Aware Model Stitching argues that functional similarity must include shared invariances, not just the ability to reuse features. It tests this with metamers, which are distinct inputs a network maps to identical activations, and each metamer costs a per-sample optimization. Our response metric targets the same "shared invariance" question. It replaces optimized metamers with known input transformations, so it is cheap enough to compute at every checkpoint. We compare against both papers' methods directly.

Two papers constrain the design. Functional Alignment Can Mislead shows that ordinary linear stitching can join clustered noise into an ImageNet ResNet-50 at over 96% top-1 accuracy. Ordinary stitching therefore cannot be our ground truth; it is only a competitor. Bridging Functional and Representational Similarity via Usable Information shows that similarity scores rise monotonically as the allowed alignment family grows from orthogonal to affine. We therefore fix the alignment family to orthogonal for all Procrustes-type scores, so differences between scores are not artifacts of alignment flexibility.

The curriculum side supplies the reason order should matter. How does Multi-Task Training Affect Transformer In-Context Capabilities? reports that a GPT-2 model trained only on quadratic in-context regression converged 0% of the time, while 60% of models trained with a mixed curriculum succeeded. The same paper finds that strictly sequential schedules forget earlier tasks. A Task-centric Theory for Iterative Self-Improvement with Easy-to-Hard Curricula gives conditions under which easy-to-hard ordering beats a fixed mixture. Bridging Critical Gaps in Convergent Learning finds that alignment across independently trained networks largely forms in the first epoch, but studies only uniform-batch training. This suggests a concrete hypothesis: whatever a curriculum shows first may fix the network's geometry. If so, order-matched networks should differ, and the difference should be visible early.

Research Program

Vision testbed. We train ResNet-20 networks on CIFAR-10 with one transformation family at a time: rotation from 0° to 180°, translation up to 8 pixels, or scaling between 0.6 and 1.4. Before training, for each family we pre-sample a fixed list of (image, transformation-magnitude) pairs covering the whole run. Each schedule then presents exactly this list in a different order:

  • Uniform: fully shuffled, which is standard augmentation.
  • Easy-to-hard: sorted by magnitude in five stages.
  • Hard-to-easy: the reverse order.
  • Sequential: stages with no replay of earlier stages.
  • Mixed: each stage adds new magnitudes while keeping earlier ones, following the anchor design of the function-class study.
  • Loss-paced: examples admitted by low training loss, in the style of Self-Paced Learning for Latent Variable Models.

Every schedule gets the same optimizer, learning-rate schedule and total number of steps. We train five seeds per schedule per family, about 90 networks in total, and save a checkpoint every epoch. We add two positive controls that change the data rather than the order: a network trained with no augmentation, and a network trained only on large magnitudes.

Sequence testbed. We reuse the function-class setting from the in-context learning study: a 22.4M-parameter GPT-2 trained on linear, quadratic and cubic Hermite-polynomial regression under Sequential, Mixed and Random schedules. We match the total sample multiset across schedules. The "transformation" here is a rescaling or shift of the input $x$, and representations are read from the model's hidden state at each layer. This extends functional grounding beyond vision classification, which is the domain-scope gap the file identifies.

Behavioral ground truth. For each pair of networks we measure two things on held-out data. The first is prediction disagreement on transformed test inputs, swept across transformation magnitudes. The second is the absolute difference between the two networks' accuracy-versus-magnitude curves. For intermediate layers we measure the same quantities with linear probes trained on clean data and evaluated on transformed data. For the sequence testbed, ground truth is per-function-class error and its change under input rescaling. These quantities are behavior, not geometry, so they are the reference every metric is scored against.

Metric scoring. Following the sensitivity/specificity protocol of the statistical-testing paper, we score each metric on two properties:

  • Sensitivity: Spearman rank correlation with behavioral difference across all pairs from different schedules.
  • Specificity: for pairs with no behavioral difference beyond seed variance (same schedule, different seeds), whether the metric's score stays within the seed-to-seed range rather than falsely flagging them as different.

We also report discriminability ($d'$), the separation between same-schedule and different-schedule score distributions, in the style of the functional-correspondence paper.

Baselines

Static Procrustes. This is the orthogonal Procrustes distance between clean activations. It is the strongest existing competitor. Evaluating Representational Similarity Measures from the Lens of Functional Correspondence reports a behavioral-alignment correlation of r = 0.70 for Procrustes, the highest among its metrics, and a $d'$ of 3.73 for separating trained from untrained models. Grounding Representation Similarity Through Statistical Testing reports a rank correlation with functional behavior of about 0.30 on vision and 0.580 on MNLI language benchmarks. These numbers come from different setups and are context, not targets we can compare against directly. We compute static Procrustes on exactly the same activation matrices, layers and input sets as our metric. It uses the same rotation $Q^{*}$, so the only difference from our metric is whether displacements are compared. The response metric beats it if its sensitivity rank correlation exceeds static Procrustes by a margin outside the bootstrap 95% interval computed over network pairs, with specificity no worse.

Linear CKA and PWCCA. These are the naive reference points the field actually uses. Linear CKA reaches r = 0.66 in the functional-correspondence study, close behind Procrustes. We compute both on the same activations and score them identically. We expect CKA to show the outlier and principal-component failures documented by Deceiving the CKA Similarity Measure in Deep Learning.

Ordinary stitching. This is a linear 1×1 stitching layer trained on task loss, following Similarity and Matching of Neural Network Representations. The stitched accuracy is evaluated on transformed inputs, so the stitch has some chance to detect invariance differences. Each stitch is trained for the same number of steps on the same clean data.

Invariance-aware stitching. This is the forward-backward compatibility method with metamers and FuLA, the multi-layer alignment objective from Grounding Functional Similarity by Invariance-Aware Model Stitching. It is the most principled competitor for invariance questions. The file has no reported scalar result for it on CIFAR-10, so it must be run here. Its cost makes it impractical for every checkpoint, so we run it on final networks with a matched wall-clock budget. We also report how its sensitivity changes when the budget is raised. If invariance-aware stitching matches the response metric's sensitivity, the response metric's claim reduces to "equal accuracy at much lower cost," and we will report it that way.

Ablations of the response metric. The first ablation fits a separate $Q$ to the displacements instead of reusing the clean-data $Q^{*}$. This tests whether coupling static alignment to response alignment matters. The second ablation computes the response metric using random, non-geometric perturbations of matched input-space norm. This tests whether the information comes from the specific transformation family or from any input perturbation.

The do-nothing reference. This is clean-test accuracy difference itself. By construction it should be near zero for order-matched pairs. Any metric that beats it shows information beyond what a standard evaluation reveals.

Why not just…?

Why not just measure accuracy on transformed test sets and skip representational metrics? If the only goal is to choose the most rotation-robust model, this suffices, and we use exactly this measure as ground truth. Representational metrics are used where final behavior is not available or not sufficient: comparing intermediate layers, comparing checkpoints mid-curriculum before the readout has settled, and comparing networks that solve different tasks. The proposal earns its keep only if a metric computed at an early checkpoint predicts final transformed behavior better than transformed accuracy measured at that same checkpoint. We test this directly (see the decisive checks). If early transformed accuracy predicts as well, we will say that representational metrics add nothing for curriculum monitoring.

Why not just reuse existing metric-grounding benchmarks built on seeds, fine-tuning and principal-component deletion? Those benchmarks, from Grounding Representation Similarity Through Statistical Testing, change either the data or the representation itself. Order-matched curricula keep the data and clean accuracy fixed, which removes the easy cues a metric could exploit. This is a real threat to novelty: if metric rankings on our testbed match theirs exactly, the testbed adds little. We will report rank agreement between the two benchmarks explicitly, and we treat a ranking reversal, or the response metric's advantage appearing only here, as the result that justifies the testbed.

Why not just compare augmented and unaugmented networks, without curricula? That comparison changes the data. A static metric can then succeed simply by noticing that one network never saw rotated images. We include this pair as a positive control: every metric should flag it. The order-only pairs are the interesting cases, because no metric can succeed by detecting a data difference. If order produces no behavioral difference beyond seed variance, the curriculum conditions become a pure specificity test. In that case the claim narrows to "which metrics stay quiet when they should." The 0% versus 60% contrast in the function-class study makes a full null unlikely in the sequence testbed.

Why not just use invariance-aware stitching everywhere? It is the most direct test of shared invariance, but it needs per-sample metamer optimization, which the file names as its main practical limit. We give it its best shot on final networks and report the cost-sensitivity tradeoff. The response metric is justified only if it gets close to stitching's sensitivity at a small fraction of the cost.

Decisive Checks

The first check is whether ordering alone moves behavior. Across the vision schedules, we test whether between-schedule transformed-input disagreement exceeds within-schedule seed disagreement. For example, we compare easy-to-hard and hard-to-easy rotation curricula at matched clean accuracy. If it does not, the program pivots to specificity, as described above.

The second check is the main metric result: sensitivity, specificity and $d'$ for every baseline and for the response metric, layer by layer. The key comparison is response metric versus static Procrustes on the same activations.

The third check concerns the first-epoch phenomenon in Bridging Critical Gaps in Convergent Learning. We test whether the cross-seed alignment that forms in the first epoch differs by schedule, and whether a network's alignment at the end of the first curriculum stage predicts its final accuracy-versus-magnitude curve. We report this prediction against transformed accuracy measured at the same checkpoint, which is the honest comparator.

The fourth check replicates the main metric comparison in the GPT-2 function-class testbed. Response similarity there is computed under input rescaling, and we test whether the Mixed-curriculum models that learn quadratic regression are separated from the failed runs by representational scores before their loss curves diverge.

A clear positive outcome would be: order-only pairs that differ in transformed behavior, static metrics that miss much of that difference, and a response metric that recovers it cheaply in both testbeds. That combination would give curriculum designers a functionally grounded way to monitor geometry during training, and would give metric designers a harder benchmark than the field currently uses.