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Paper summary
The authors analyze a two-layer ReLU network trained on modular addition. They explain why test accuracy initially falls below chance through the similarity between training and test inputs. They then study how learned Fourier-like features change this behavior, derive an approximate final-loss law, and relate the sharpness of grokking to the number of contributing neurons.
Critical strengths
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The explanation of early anti-generalization is the main strength. Section 3.1 shows why input collisions give some incorrect labels larger expected scores than the correct label. This is a specific, testable mechanism supported by the authors' experiments. I verified these results by rerunning some of the experiments myself.
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The final-loss prediction in Section 4.1 is also useful. Under the stated feature and equilibrium assumptions, it gives a loss of approximately , where is regularization strength and is the modulus, which matches their Fig. 3.
Critical weaknesses
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The paper does not predict the timing of the grokking transition. The late-time calculation assumes properties of the residuals and learned features whose development is not predicted. Figure 16 shows that the approximate kernel model generalizes substantially later than the network. Improving the onset estimate requires measurements of the evolved state. The analysis explains early failure and conditional final loss, but does not predict the transition from initialization.
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The effective-width argument is mainly an independence approximation. A constructed check during this review makes the limitation explicit. In this bias-free ReLU network, replace each neuron by identical copies, scaling both layers by . This leaves the network function and SGD dynamics unchanged while multiplying the proposed participation ratio by . The copies violate the paper's independence assumption, so this does not refute the conditional calculation. It does show why that assumption needs checking in learned features before the ratio can explain transition sharpness.
Questions for authors
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Can the authors explain the discrepancy in Figure 16 and measure correlations between neuron contributions during the transition? Please also identify which experiments use the Gaussian initialization assumed in the theory and which use the trainer's default uniform initialization.
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I believe some existing relevant works are missing from the related work section:
- Prieto, Barsbey, Mediano and Birdal, Grokking at the Edge of Numerical Stability, ICLR 2025.
- Xu, Vardi and Safran, To Grok Grokking: Provable Grokking in Ridge Regression, ICML 2026.
- Levi, Beck and Bar-Sinai, Grokking in Linear Estimators — A Solvable Model that Groks without Understanding, ICLR 2024.
- Beck, Levi and Bar-Sinai, Grokking at the Edge of Linear Separability, ICML 2025.
4 comments
W2. Effective width, the neuron-duplication counterexample, and neuron correlations
We thank the reviewer for the insightful counterexample. We agree that is an energy participation ratio, not a parameterization-invariant count of independent neurons. Replacing each ReLU neuron by copies with incoming and outgoing weights scaled by preserves the network function but multiplies by at corresponding parameter states. The copies are perfectly correlated: their off-diagonal covariances exactly compensate for the reduced diagonal variance sum, leaving the total margin fluctuation unchanged. We therefore clarify that the relation is an empirical, conditional scaling estimate requiring control of cross-neuron covariances, not a universal consequence of participation alone.
We tested this construction on modular addition (), comparing a width-256 base network, its fourfold-duplicated width-1024 counterpart, and an independently initialized width-1024 network. The base and duplicate were trained independently without parameter tying, using identical minibatches and hyperparameters. Their accuracy trajectories closely track one another, whereas the independently initialized width-1024 network generalizes earlier. This directly illustrates why width obtained by exact copying is not equivalent to independently initialized width.
We also measured off-diagonal Pearson correlations of neuron-level kernel-score contributions across test samples, using both centered score differences and maximum-wrong-class margins at grokking onset and test accuracies 0.5 and 0.9. The base and independently initialized networks have distributions concentrated near zero, while the duplicate has an additional peak at correlation from identical copies. These measurements distinguish duplication but do not establish independence or negligible aggregate covariance: many small correlations can accumulate, and perfectly correlated copies can be diluted in global averages.
The construction, variance decomposition, experimental settings, and correlation results are now presented in Appendix B.3.4. We have correspondingly qualified the effective-width interpretation.
Q1. Initialization settings: uniform versus Gaussian
We thank the reviewer for prompting this clarification. The random-initialization kernel analysis uses independent Gaussian first-layer weights and . In contrast, the standard modular-addition training experiments, including the duplication experiment, use PyTorch's default uniform initialization, , with zero-initialized readout. Direct kernel visualizations and Fourier-initialization experiments use their explicitly specified feature ensembles. We now distinguish these settings in the manuscript.
We have added an exact uniform-initialization ReLU calculation in Appendix A.3.6. At matched weight variance, its diagonal, collision, and background coefficients are , close to their Gaussian counterparts . Both preserve , so the input-collision anti-generalization mechanism is unchanged. The smaller variance of PyTorch's default uniform initialization rescales the kernel without changing this ordering.
Finally, the late-time equilibrium loss relation is conditional on the learned Fourier/square-wave feature statistics and radial weight-decay balance. It has no explicit dependence on the initialization distribution once that regime is reached, although initialization can still affect the preceding dynamics or accessibility of that regime.
Q2. Related works
We thank the reviewer for identifying these omissions. We have expanded the related-work discussion to include Prieto et al. (2025), Levi et al. (2024), Beck et al. (2025), and Xu et al. (2026), which establish several complementary mechanisms underlying delayed generalization in the Introduction.
In particular, Prieto et al. (2025) identify the role of softmax numerical stability and naive loss minimization. Levi et al. (2024) and Beck et al. (2025) demonstrate delayed generalization in analytically tractable linear or fixed-feature classification settings, showing that nonlinear representation learning is not a necessary condition for all forms of grokking. Xu et al. (2026) further establish quantitative bounds on grokking time in ridge regression and examine their applicability to nonlinear networks.
These works provide important complementary perspectives on grokking. In contrast, our work focuses on the evolving hidden-representation kernels in two-layer ReLU networks, explicitly connecting early input-collision-induced anti-generalization, late feature-kernel reorganization, and finite-width transition behavior.
Dear reviewer,
Have the authors address your concerns in their replies?
I thank the reviewers for their detailed response. I believe the scope and contribution of the paper allows me to retain my positive score, but not to raise it.
We thank the reviewer for the careful evaluation and for independently reproducing our early anti-generalization results. We appreciate the positive assessment of our input-collision mechanism and equilibrium loss prediction. We address the concerns below and clarify the scope of our analytical results and their relationship to the numerical observations.
W1. Scope of the transition analysis and the discrepancy in Figure 16
We agree that our framework does not provide an a priori closed-form prediction of the absolute grokking time from initialization. In particular, the intermediate crossover rate ralign=datv/dt is governed by non-stationary dynamics, which we identify as an open problem in Sections 5.3 and 6. Our framework does not predict the entire trajectory from t=0 but connects the early and late regimes through two analytical characterizations.
(i) Relative early- and late-stage feature-learning drives. The relative scaling of the corresponding label-aligned gradient prefactors is characterized by κ˙=λ/ϵ2 (Section 2.2, Eq. 5). Its quantitative agreement with the measured neuron-direction changing rates (Appendix B.2, Figure 13, κth˙=0.0686 versus κreal˙=0.0680) provides a consistency check for the relative feature-learning drive and explains the slow post-fit feature-learning timescale under weight decay. Importantly, our analysis characterizes the relative scaling of the two gradient contributions at two stages, while predicting the absolute transition time is beyond this scope.
(ii) Positive onset alignment and collision-induced competition. We identify a positive onset alignment atv(t0)>0 at the transition, whose characteristic scale can be related to competition from two-collision wrong-label blocks under the assumptions in Section 5.1 and Appendix B.3.2 (Eq. 98). This provides an analytical characterization of the onset condition instead of a prediction of when the condition will be reached from initialization.
We therefore distinguish these analytical characterizations from our empirical characterization of the transition dynamics.
Regarding Figure 16, the comparison among the actual network (solid), the residual-based kernel prediction StKtv (dash-dotted), and the label-based kernel prediction Yt~Ktv (dashed) reveals two distinct sources of discrepancy.
Why Yt~Ktv lags behind StKtv and the actual network. The label-based prediction invokes the uniform residual-field ansatz St≃ϵYt~. This approximation involves two assumptions: the residual of each training sample is approximately aligned with its label vector, and the residual magnitudes are sufficiently concentrated across samples to be represented by a common coefficient ϵ. More generally, the sample-wise residual can be written approximately as S:μ≃ϵμyμ~, with potentially different ϵμ.
The residual-based prediction retains these sample-dependent weights through StKtv, whereas the label-based prediction replaces them with a common coefficient. Consequently, training samples with larger residual contributions receive greater weight in StKtv, while Yt~Ktv weights the corresponding label contributions uniformly. This can dilute emerging task-aligned signals and provides a natural explanation for the larger discrepancy of the label-based prediction.
The discrepancy between these two predictions becomes substantially smaller as the width increases from N=512 (Figure 16a) to N=2048 (Figure 16b), consistent with reduced finite-width residual heterogeneity.
Why the actual network slightly lags behind StKtv. The residual-based kernel prediction assumes instantaneous readout locking, $ V(t)\simeq \frac{1}{\lambda M}S_t(t)F_t(t)^\top. $ However, the actual readout follows $ \dot V=\frac{1}{M}S_tF_t^\top-\lambda V. $ Its exact solution is $ V(t)=e^{-\lambda t}V(0) +\frac{1}{M}\int_0^t e^{-\lambda(t-s)} S_sF_s^\top,ds. $ Thus, the readout retains an exponentially weighted memory of earlier residual-feature correlations and does not respond instantaneously to the current representation. When the representation evolves during the transition, this finite relaxation time can cause the actual network to lag behind the instantaneous residual-based prediction. The characteristic readout relaxation timescale is λ−1.
These two effects distinguish the residual-field approximation from the finite response time of the readout, and clarify why the kernel approximation does not reproduce the complete transition trajectory.