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Under review as a conference paper at ICLR 2027

Beyond One Epoch: Uncertainty-Weighted Sensitivity Regularization for Recommendation Models

Abstract

Recommendation models with sparse embeddings and a shared consumer often exhibit the one-epoch phenomenon: a second epoch lowers training loss while sharply degrading generalization. We present a view based on the violation of the prequential principle. On the first epoch, an example's label has not affected the embedding rows used to score it. On later epochs, those rows contain a displacement induced by the labels earlier update. This creates an incentive for the shared consumer to exploit this displacement in subsequent epochs, which fails to generalize. We call this self-influence asymmetry. Using an exact scalar model and local influence analysis, we connect this mismatch to the uncertainty in the embeddings and the consumers incentive to exploit it in subsequent epochs. We verify this hypothesis using an embedding-consumer-update interventions in deep recommendation models and propose uncertainty-weighted sensitivity regularization (UWSR) which counteracts this mismatch by augmenting the loss function to penalize the consumer for relying on uncertain embeddings. Unlike existing remedies, UWSR preserves the learned embeddings and across three benchmarks, four-epoch UWSR reduces test cross-entropy by 1.38%–6.78% and improves AUC by 0.0058–0.0231 relative to one-epoch training.

Primary area:
optimization
Keywords:
Recommendation Systems, sparse embeddings, one-epoch phenomenon, multi-epoch training

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Paper summary

This paper investigates the one-epoch phenomenon in recommendation models, where additional training reduces training loss but worsens generalization. The authors propose self-influence asymmetry as an explanation: previously observed labels affect sparse embeddings, allowing the shared consumer network to exploit information that is unavailable when predicting fresh examples. The paper develops an exact scalar model and a local influence analysis to characterize this effect. Based on these observations, it introduces Uncertainty-Weighted Sensitivity Regularization (UWSR), which penalizes the consumer's sensitivity to uncertain embedding representations. Experiments on MovieLens-20M, Amazon Electronics, and Avazu compare UWSR with existing multi-epoch training methods and report improvements in test performance.

Critical strengths
  1. The paper provides a useful perspective on the one-epoch phenomenon.

The connection between repeated training, self-influence, and the prequential principle offers a meaningful explanation of why sparse embeddings may encourage overfitting. The scalar model provides an exact characterization under simplified assumptions, while the local influence analysis extends the intuition to neural recommendation models. This goes beyond treating the phenomenon as ordinary overfitting.

  1. The update-order intervention provides evidence for the proposed mechanism.

Section 3.3 directly examines the interaction between embedding updates and consumer updates. Table 1 shows that updating embeddings before the consumer substantially increases score sensitivity and worsens validation performance, while reversing the order produces much smaller changes. This intervention provides useful evidence that same-label self-inclusion can contribute to generalization degradation.

  1. The proposed method achieves competitive results against relevant baselines.

The evaluation includes MEDA, AdamAR, embedding dropout, and other training strategies. UWSR achieves clear improvements on Amazon Electronics and Avazu, with paired confidence intervals reported in Appendix D. The comparisons with uniform sensitivity regularization and expected-Fisher weighting also provide evidence that uncertainty weighting contributes to the observed gains.

Critical weaknesses
  1. The proposed mechanism is not sufficiently established as the primary explanation for multi-epoch generalization degradation.

The scalar analysis uses a simplified two-stage model, while the neural analysis relies on local approximations and row-wise effects. The update-order intervention in Section 3.3 shows that self-inclusion can induce sensitivity inflation, but it does not quantify how much of the degradation during ordinary multi-epoch training is caused by this mechanism. The intervention also changes the optimization sequence, making it difficult to isolate the effect of label reuse from other changes in training dynamics. The experiments support self-influence asymmetry as a contributing factor, but not necessarily as the dominant cause of the one-epoch phenomenon.

  1. The connection between the theoretical uncertainty measure and its practical approximation remains insufficiently validated.

The theoretical formulation relies on inverse row information derived from a local generalized Gauss-Newton model. In practice, UWSR uses normalized, row-wise accumulated squared gradients as an approximation. This approximation does not directly measure the covariance assumed in the analysis, and the paper does not establish how accurately it captures the uncertainty or self-influence of individual embedding rows. Although the expected-Fisher and uniform-weight comparisons are useful, they do not directly validate the proposed uncertainty estimates. It remains unclear whether the improvements follow from the specific theoretical mechanism or from an effective form of frequency-dependent sensitivity regularization.

  1. The empirical evidence for generalization across model architectures is insufficient.

The main experiments use a compact WuKong-inspired consumer architecture with 32-dimensional embeddings. The effectiveness of sensitivity regularization may depend on the consumer structure, embedding dimension, and interaction patterns. The paper refers to additional architecture experiments in Appendix G, but these results are absent from the supplied manuscript. Without this evidence, it is difficult to determine whether UWSR addresses a general limitation of sparse-embedding recommendation models or performs particularly well under the evaluated architecture.

  1. The computational cost of the proposed method is not adequately substantiated.

UWSR requires second-order automatic differentiation to compute the sensitivity penalty, which introduces additional computation beyond standard first-order training. The paper claims minimal overhead and refers to wall-clock measurements in Appendix H, but this appendix is not included in the supplied manuscript. No directly verifiable comparison of training time, peak memory usage, or throughput is available. Since the method targets recommendation systems with potentially very large embedding tables, computational efficiency is important for assessing its practical contribution.

  1. The reported improvements are not equally reliable across the three benchmarks.

The results on Amazon Electronics and Avazu are encouraging, but MovieLens-20M provides weaker evidence. Appendix D reports that the 95% confidence intervals for both the AUC and cross-entropy improvements at epoch four include zero. Moreover, UWSR reaches its highest MovieLens AUC at epoch two, after which performance declines. Thus, the method does not consistently prevent degradation during additional training epochs. The results support substantial benefits in some settings, but the evidence for robust improvement across all three datasets is less convincing than the main conclusions suggest.

Questions for authors

Can the authors quantify how much of the ordinary multi-epoch generalization degradation is attributable to self-influence asymmetry? How can the effect of label reuse be separated from the optimization changes introduced by the update-order intervention?

Is there empirical evidence that the accumulated squared-gradient weights accurately reflect embedding uncertainty or generalized leverage? How strongly do these estimates correspond to the quantities used in the theoretical analysis?

Can the authors provide the additional architecture experiments referenced in Appendix G? In particular, does UWSR retain its advantage across consumer architectures with different interaction structures and embedding dimensions?

What are the training-time and peak-memory overheads of UWSR relative to MEDA and AdamAR under identical hardware and training settings? Can the authors provide the wall-clock measurements referenced in Appendix H?

How should the MovieLens-20M results be interpreted given that the confidence intervals include zero and that AUC declines after the second epoch? Does the method consistently outperform the strongest baseline when each method is selected at its best validation checkpoint?

11 comments

Thank you for reviewing our manuscript. Please find our response below and let us know if there are any other concerns we can address.

1. On causal attribution

Can the authors quantify how much of the ordinary multi-epoch generalization degradation is attributable to self-influence asymmetry?

Unfortunately, this is difficult to quantify. Validation-loss change across an additional epoch is a net effect: e.g. beneficial optimization during epoch two can offset harmful overfitting effects. The one epoch phenomenon describes a loss curve pattern, which is the sum of all effects.

We establish self-influence asymmetry as a contributing mechanism, without claiming it is the dominant cause in the manuscript.

Our contribution is the exact scalar model, mechanistic analysis, its experimentally tested predictions, and the theoretically motivated regularizer we propose, which compares favorably with existing methods such as AdamAR (Li & Lyu, ICLR 2026) and MEDA (Fan et al., 2024) in our experiments.

How can the effect of label reuse be separated from the optimization changes introduced by the update-order intervention?

This was an interesting question to think about.

Self-influence describes the effect of a label on its own fitted prediction, studied in the context of statistical optimism (Efron, 1986; 2004). Our manuscript defines self-influence asymmetry as the resulting change in the effective training objective and its optimum from a model’s fit on an example. Appendix B develops this connection to classical optimism.

A causal attribution requires a specified counterfactual and a quantity whose contribution is being measured. By necessity, testing label self-inclusion requires a comparison with and without the label-dependent model state. We cannot hold the consequences of the sample’s influence on the model and optimizer fixed while measuring the effect of removing that training label from the training procedure. A nontrivial intervention must therefore change the label-dependent state in one way or another.

Our update-order intervention supplies a non-trivial way to test label inclusion, and optimizing the labels before the network is the independent variable being tested.

Both staged arms and the standard training control match initialization, examples, minibatches, optimizer configuration, and update counts. The arms differ in whether embeddings were already updated using the labels the rest of the model is then being fit on. The consumer-first ordering arm controls for the split training procedure. We have clarified this motivation and the reverse-order control’s role in Section 3.3 of the revised manuscript (Figures 2–3).

Zhang et al. found that training the embeddings for multiple epochs after freezing the consumer prevented the one-epoch phenomenon, demonstrating that the issue is not intrinsic to training the embeddings for multiple epochs. Additionally, our benchmarks show that freezing the embeddings until the last pass, while not competitive, prevents catastrophic degradation, demonstrating that it is not intrinsically caused by training the downstream network for multiple epochs.

Our intervention, however, shows that degradation is triggered when the embeddings are updated on the labels before the rest of the network in a single epoch. Our analysis predicts this, alongside a rise in the embeddings’ gradient magnitudes, which is observed in both multi-epoch training and our intervention (Figures 2–3 and 5).

In the spirit of the question, we draw a comparison of magnitudes: the MovieLens contrast between the staged arms is approximately 180% of the ordinary validation-BCE increase from the first to the second epoch in the archived benchmarks. This shows that self-inclusion can induce a penalty large enough to explain the observed net increase, and the effect is non-trivial.

Please refer to the predictive test reported to Reviewer 1 under “Explanatory power of Self-Influence Asymmetry,” now included in Figure 7 and Appendix B of the revised manuscript. Your question also motivated it.

On the accuracy of our uncertainty approximation

Is there empirical evidence that the accumulated squared-gradient weights accurately reflect embedding uncertainty or generalized leverage? How strongly do these estimates correspond to the quantities used in the theoretical analysis?

Our weighting makes several simplifications, each with established precedent:

  1. A local quadratic/Laplace approximation and diagonal precision. We model the embeddings' posterior as Gaussian with precision I\mathcal I and approximate the precision matrix by its diagonal. Elastic Weight Consolidation (EWC; Kirkpatrick et al., 2017) uses these same two approximations. Our manuscript focuses on one embedding row for clarity; the same quadratic formulation can be written jointly over the parameters.

  2. An optional substitution of empirical Fisher statistics for expected Fisher. The expected-Fisher variant gives nearly identical results (Table 2; construction in Appendix B.3). RWalk (Chaudhry et al., ECCV 2018) provides precedent for this choice.

  3. An optional reduction to one scalar per embedding row before shrinkage and inversion. This is inspired by sparse embedding optimizers such as row-wise AdaGrad in TorchRec/FBGEMM. Our per-coordinate ablation performs comparably (Appendix F, Table 5). Shrinkage toward the table mean stabilizes the row-information estimates before inversion, following a common strategy for regularizing estimated covariance.

We will update the manuscript to cite these established approximations.

The practical construction is intended as an efficient surrogate for the theory-motivated regularizer, rather than as a precisely calibrated estimator of each embedding row's covariance or self-influence.

It remains unclear whether the improvements follow from the specific theoretical mechanism or from an effective form of frequency-dependent sensitivity regularization.

For the inverse-frequency count ablation, please see the section “Inverse-Frequency Based UWSR Ablation” in our response to Reviewer 1. This includes an experiment demonstrating why inverse-frequency weighting cannot generally be assumed sufficient and where gradient-based information improves on count weighting.

We would like to share our perspective on this framing. Under constant information per occurrence, our theory directly predicts inverse-frequency-weighted sensitivity regularization. It follows from the manuscript’s asymptotic analysis often relating row information and covariance to support count NN.

If a novelty concern rests on treating it as a pre-existing method, or on a prior theoretical account explaining its effectiveness, we would welcome any corresponding references. However, to the best of our knowledge, no prior work has proposed frequency-dependent Jacobian regularization for learned sparse embedding rows, nor are we aware of another prior theoretical account motivating this particular construction.

Performance Benchmarking

What are the training-time and peak-memory overheads of UWSR relative to MEDA and AdamAR under identical hardware and training settings? Can the authors provide the wall-clock measurements referenced in Appendix H.

While the penalty can seem to be computationally expensive, the gradient computation only needs hessian vector products which is an optimized computation in pytorch. Thus, the full hessian is neither computed nor materialized in the training step, resulting in minimal increase in the training time and peak memory. Please find below the implementations benchmarked in our paper, benchmarked serially in isolation on an A100 for Amazon with Wukong:

MethodFour-pass trainingPeak GPU memory
Adam198.6 s0.200 GiB
MEDA198.5 s0.200 GiB
AdamAR207.3 s0.200 GiB
Empirical Fisher196.6 s0.371 GiB
Expected Fisher211.3 s0.377 GiB

The original harness implementation was not been optimized for memory. Our production prototype allocates temporary buffers only for the embedding rows accessed by each minibatch, avoiding an additional buffer the size of the full table.

Update: We adapted the active-row differentiation approach in our productionisation prototype to the test harness. Equivalence checks confirmed that the optimized implementation preserved the original loss to numerical precision. On Amazon Electronics, we expanded the embedding tables 32× to 8.2 million rows, keeping active IDs fixed, to evaluate scaling at larger table sizes.

All methods used torch.compile and ran serially on the same A100 for four full training passes.

MethodFour-pass totalReplay passes 2–4Peak allocated memory
Adam200.6 s134.8 s4.954 GiB
MEDA181.8 s132.0 s4.955 GiB
AdamAR184.6 s137.9 s4.955 GiB
UWSR183.6 s142.7 s5.128 GiB

Movielens Confidence Intervals

Thank you for identifying this issue. Please see our response to reviewer #2 with regards to the Movielens ablations / large percent cold user cohort.

How should the MovieLens-20M results be interpreted given that the confidence intervals include zero and that AUC declines after the second epoch?

We select regularization strengths using validation BCE separately at each applicable epoch in the manuscript. The visualization in our “Architecture Ablations” response makes the comparisons easier to interpret.

Under the validation selection method requested, UWSR or its expected-Fisher variant achieves the best mean test BCE and AUC on all three datasets.

Over 90% of MovieLens test examples contain at least one user or item embedding that was never trained. This helps explain why uniform sensitivity regularization, which reduces reliance on embeddings across all rows, is competitive on this dataset. It is also consistent with embedding dropout’s comparatively strong performance on MovieLens relative to the other two datasets.

Regarding the AUC decline after epoch two, UWSR is a theoretically motivated, computationally tractable regularizer intended to mitigate replay-related overfitting and enable useful additional training. We do not claim that it prevents overfitting indefinitely. AdamAR (Li & Lyu, ICLR 2026) likewise reports settings in which performance peaks after two or three epochs.

Requested Test Performance at the Best Validation Checkpoint

Amazon Electronics (5 seeds)

MethodTest BCETest AUCΔBCE vs one epoch
Adam0.4757370.8568+0.28%
MEDA0.4573530.8658+4.14%
Freeze until final pass0.4773340.8517-0.05%
Active-row AdamW0.4757370.8568+0.28%
Embedding dropout0.4736390.8567+0.72%
AdamAR0.4601000.8661+3.56%
UWSR Uniform0.4685530.8591+1.79%
UWSR0.4447860.8753+6.77%
UWSR Expected Fisher0.4440160.8756+6.93%

Avazu (5 seeds)

MethodTest BCETest AUCΔBCE vs one epoch
Adam0.3897320.7405+0.00%
MEDA0.3885560.7414+0.30%
Freeze until final pass0.3889970.7414+0.19%
Active-row AdamW0.3910820.7348-0.35%
Embedding dropout0.3897320.7405+0.00%
AdamAR0.3841690.7486+1.43%
UWSR Uniform0.3845340.7474+1.33%
UWSR0.3799380.7558+2.51%
UWSR Expected Fisher0.3798730.7561+2.53%

MovieLens-20M (15 seeds)

MethodTest BCETest AUCΔBCE vs one epoch
Adam0.6524410.6684+0.05%
MEDA0.6432720.6768+1.44%
Freeze until final pass0.6460410.6714+1.01%
Active-row AdamW0.6468490.6758+0.89%
Embedding dropout0.6437870.6798+1.36%
AdamAR0.6430600.6804+1.47%
UWSR Uniform0.6372890.6881+2.35%
UWSR0.6357960.6896+2.58%
UWSR Expected Fisher0.6359040.6891+2.57%
Reviewer_vJm9OpenReview ↗
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3(+1)
Confidence
3
Informativeness
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2
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Paper summary

The paper studies why additional training epochs can harm generalization in sparse-embedding recommendation models. It attributes this partly to self-influence asymmetry: replayed examples exploit information their own labels previously introduced into embeddings. The authors support this explanation with theoretical analysis and an update-order intervention, then propose uncertainty-weighted sensitivity regularization (UWSR) to discourage reliance on poorly determined embeddings during later epochs.

Critical strengths

S1. Addresses an important and demonstrable problem. Naïve multi-epoch training substantially degrades performance in the evaluated settings. Enabling useful additional training without resetting learned embeddings is a practically meaningful objective.

S2. Provides an informative mechanistic explanation. The scalar model explicitly characterizes the mismatch between replayed and fresh examples. The embedding-first versus consumer-first intervention strengthens the evidence beyond correlation by manipulating whether the consumer encounters representations already updated using the same labels.

Critical weaknesses

W1. The neural theory does not fully justify the practical claims. Proposition 1’s expected identity requires local correct specification—an assumption stated in the proof but omitted from the proposition. Moreover, the analysis describes an isolated quadratic row update rather than joint Adam training. Thus, it supports a local explanation, not a general guarantee that UWSR restores the missing prequential penalty.

W2. The regularizer’s intended effect needs clarification. Although framed as consumer rather than embedding regularization, Algorithm 1 updates both through the full regularized loss. For nonlinear consumers, the penalty can therefore also modify embeddings unless gradients are explicitly blocked. Additionally, frozen uncertainty weights raise a potential rescaling issue: in rescalable embedding–consumer interfaces, the penalty can decrease without changing predictions. These concerns weaken the interpretation of reduced sensitivity as reduced harmful reliance.

W3. Key experimental evidence remains incomplete. The weighting ablations lack a simple inverse-frequency-weighted sensitivity baseline, leaving unclear whether Fisher-based uncertainty estimation improves over merely regularizing rare rows more strongly. Furthermore, MovieLens confidence intervals cross zero for both BCE and AUC, so statistically supported improvement is not established across all three datasets.

Questions for authors

Please refer to Weaknesses.

6 comments

We thank the reviewer for their thorough analysis of our paper.

Q2/W2:

Potential Scaling Issue

W2. The regularizer’s intended effect needs clarification. Although framed as consumer rather than embedding regularization, Algorithm 1 updates both through the full regularized loss. For nonlinear consumers, the penalty can therefore also modify embeddings unless gradients are explicitly blocked. Additionally, frozen uncertainty weights raise a potential rescaling issue: in rescalable embedding–consumer interfaces, the penalty can decrease without changing predictions. These concerns weaken the interpretation of reduced sensitivity as reduced harmful reliance.

Yes, this is a perceptive point. If JJ represents the Jacobian of the logit with respect to the embedding (previously denoted ss), we can consider a change in the embedding value using a Taylor expansion around the zero vector: f(x⃗)≈f(0)+Jx⃗f(\vec{x}) \approx f(0) + J\vec{x}. We could achieve a lower loss on our regularizer ∥∥s∥∥I−12\|\|s\|\|_{\mathcal{I}^{-1}}^2 by multiplying JJ by some a<1a<1 and xx by 1/a1/a to yield the same result.

Can we reconcile this? Let us consider the scalar example in our paper, y=wey=we. If we consider the optimal solution wfreshw_{\mathrm{fresh}} and fit the embeddings, we could set w′=aww' = aw and e′=e/ae' = e/a for all scalar embeddings e∈R1e \in \mathbb{R}^1, and the solution's predictions would still be the same.

As the reviewer has pointed out, our construction freezes the information weights, so they may be miscalibrated and fail to account for this change in scale.

However, we can indeed offer a reconciliation: the information weights need not be frozen.

We previously found empirically in informal ablation that keeping an EMA like Adam’s, with a proper construction in which decay happens every step, achieved slightly worse performance in our earlier informal ablations. For large embedding tables, this may be done efficiently by keeping an integer recording the last time a row was updated and, whenever an embedding is used, applying Adam's β\beta as βcurrent step−last access step\beta^{\text{current step} - \text{last access step}} to properly amortize the decay without requiring all embedding second moments in the table to be updated.

The chain rule then gives s′=ass'=as, g′=agg'=ag, where ss is the logit Jacobian and gg is the BCE gradient with respect to the embedding. Squared-gradient information therefore scales as I′=a2I\mathcal{I}'=a^2\mathcal{I}, and its inverse scales as Σ^′=a−2Σ^\hat{\Sigma}'=a^{-2}\hat{\Sigma}. Consequently, s′⊤(Σ^′)s′=s⊤Σ^ss'^\top (\hat{\Sigma}') s' = s^\top \hat{\Sigma} s.

To make the paper more approachable, we chose to present the Adagrad + freeze construction. We have included this transformation alongside the EMA construction in Appendix C.2 of the revised manuscript.

Clarification Of Algorithm

Likewise, in our introduction, we emphasized for layman understanding that we regularized the consumer rather than annealing the embedding norm directly, leaving it otherwise unconstrained. As you point out, for nonlinear consumers, the Jacobian depends on the embedding values, so differentiating the sensitivity penalty can also update the embeddings. Indeed, they are implicitly affected by the loss through their effect on the Jacobian. We have added a footnote in Section 4 to clarify the nuance of leaving the embedding “otherwise” unconstrained and a note in Appendix C.2 on the implications of freezing and the alternative EMA construction.

Q1: Optimizer Generalization / Approximation

The neural theory does not fully justify the practical claims. Proposition 1’s expected identity requires local correct specification—an assumption stated in the proof but omitted from the proposition. Moreover, the analysis describes an isolated quadratic row update rather than joint Adam training. Thus, it supports a local explanation, not a general guarantee that UWSR restores the missing prequential penalty.

We thank the reviewer for their careful reading and helpful comment on the missing condition. The local correct-specification condition was included in the proof but inadvertently dropped from the proposition statement during formatting. We have corrected Proposition 1 and expanded the exposition to make the connection to joint training clearer.

The proposition describes the difference between stationary solutions of a fixed quadratic surrogate of the loss, and is explicitly scoped to that local model. Additionally, the difference is independent of the optimizer used to solve that quadratic, as is conventional in influence analysis. We recognize how it might be interpreted that the statement relies on the chosen optimizer approximating a GGN update during training, and we have clarified this point in Appendix A.

While these approximations are indeed local, the Laplace and Fisher approximations UWSR makes have strong precedent in the field, and similarly, influence analysis is a well established framework. One such example of the Laplace and Fisher approximations is Elastic Weight Consolidation (EWC; Kirkpatrick et al., 2017). Its quadratic penalty measures parameter displacement in the information metric:

REWC=(θ−θ0)⊤I(θ−θ0).R_{\mathrm{EWC}} =(\theta-\theta_0)^\top\mathcal I(\theta-\theta_0).

Under the exact same style Laplace / Gaussian posterior approximation as EWC, UWSR uses the corresponding dual metric on gradients:

RUWSR=g⊤I−1g.R_{\mathrm{UWSR}}=g^\top\mathcal I^{-1}g.

Finally, to make the joint interpretation easier to follow, we have also added the joint-parameter interpretation in Appendix A. Here, ϕ\phi denotes the joint parameter vector, including both embeddings and the shared consumer, with g=∇ϕzg=\nabla_\phi z. Our derivation applies with the notation extended to the joint parameters. In Appendix C.2, we have also cited well established prior work that uses each corresponding approximation we take advantage of.

Edit: Empirical results

We have copied results testing our proposition, and testing our ability to reconstruct validation loss without any labels from the validation set. Please see replies to other reviewers , What observations can the proposed self-influence asymmetry explain that these existing accounts cannot? for more context.

Predicted versus measured example-removal effects [Proposition 1 test]

We individually removed 838 real-label training examples from a compact Amazon Electronics cohort and retrained, matching initialization, example order, and minibatch boundaries. At epoch four, we compare predicted optimism O^i=pi−(1−pi−)∑(F,r)∈A(xi)sF,r,4(xi)⊤Σ^F,rsF,r,4(xi)\widehat O_i=p_i^-(1-p_i^-)\sum_{(F,r)\in\mathcal A(x_i)}s_{F,r,4}(x_i)^\top\widehat\Sigma_{F,r}s_{F,r,4}(x_i) with measured centered optimism Oi=(yi−pi−)(zi+−zi−)O_i=(y_i-p_i^-)(z_i^+-z_i^-).

Here zi+z_i^+ and zi−z_i^- are the full-data and deleted-fit logits, and pi−=σ(zi−)p_i^-=\sigma(z_i^-). The sum is UWSR's sensitivity penalty over active embedding rows, using full-fit logit derivatives and frozen first-epoch inverse-information weights.

Their Spearman correlation is 0.832. Neither one million unrestricted pairing shuffles nor one million within-user shuffles reached this correlation

The one-sided Monte Carlo p =1 / 1,000,001 approx 1e-6 under both schemes. our proposition describes expected optimism, whereas these deletions measure realized effects.

Fixed-scale Validation loss reconstruction on independent training runs

We fixed each reconstruction scale on a separate calibration run and applied it to a new run with independent initialization and example order. The reconstruction does not refit the scale to subsequent validation losses. Across the three datasets, reconstruction RMSE is 72–87% lower than for training loss plus the first-epoch validation–training gap.

Repeating the paper's temporal test, we removed each epoch's mean and linear trend from both series. None of 20,000 within-epoch circular-shift controls reached the observed detrended correlation on any dataset

The one-sided Monte Carlo p = 1/20,001, approximately 0.00005.

The accompanying appendix material are on pages 15-17 of the updated manuscript in red.

Predicted validation loss graphic: https://i.imgur.com/8CRwpTo.png

Q3 / W3 MovieLens Confidence Intervals

W3. Key experimental evidence remains incomplete. The weighting ablations lack a simple inverse-frequency-weighted sensitivity baseline, leaving unclear whether Fisher-based uncertainty estimation improves over merely regularizing rare rows more strongly

For the inverse-frequency count ablation, please see the section “Inverse-Frequency Based UWSR Ablation” in our response to Reviewer 1. This includes an experiment demonstrating why inverse-frequency weighting cannot generally be assumed sufficient and where gradient-based information improves on count weighting. The revised manuscript includes these comparisons in Figure 6 and Tables 10–11 (Appendix J).

The authors would like to share our perspective. Under constant information per occurrence, our theory directly predicts inverse-frequency-weighted sensitivity regularization. It follows from the manuscript’s asymptotic analysis often relating row information and covariance to support count.

If a novelty concern rests on treating it as a pre-existing method, or on a prior theoretical account explaining its effectiveness, we would welcome any corresponding references. However, to the best of our knowledge, no prior work has proposed frequency-dependent Jacobian regularization for learned sparse embedding rows, nor are we aware of another prior theoretical account motivating this particular construction.

Furthermore, MovieLens confidence intervals cross zero for both BCE and AUC, so statistically supported improvement is not established across all three datasets.

Thank you for raising this. With respect to confidence intervals on MovieLens, we have investigated. We postulate that weaker confidence intervals on this dataset are partially to do with the disproportionate amount of cold embeddings found in the test set, making this dataset noisier / less discriminatory; ~90% of test examples had either a cold user or cold item ID.

To resolve this, we ran 10 more seeds on MovieLens under a protocol fixed before the new runs, which we share below.

With 15 seeds, both improvements are significant for UWSR, with two-sided paired p-values at most 0.00128 for BCE and 0.026 for AUC for the confidence intervals in question.

These results are now included in Table 1 of the revised manuscript, with confidence intervals in Table 3 and paired tests in Appendix F.

MethodAUC E1AUC E2AUC E3AUC E4ΔBCE E2ΔBCE E3ΔBCE E4
Adam0.66970.64090.59170.5173−1.68%−6.20%−29.32%
MEDA0.66970.67630.67300.6726+1.19%+0.99%+1.02%
Freeze until final pass0.66970.66950.65980.6536+0.49%−0.21%−0.43%
Active-row AdamW0.66960.68310.67850.6729+0.81%+1.21%+0.28%
Embedding dropout0.66970.67990.65770.6393+1.38%−0.08%−1.66%
AdamAR0.66980.67100.66640.6793+0.67%+0.35%+0.90%
UWSR Uniform0.66970.68640.69390.6853+1.60%+2.14%+1.36%
UWSR0.66970.69360.68780.6790+2.42%+2.30%+1.73%
UWSR Expected Fisher0.66970.69330.68800.6786+2.40%+2.28%+1.77%
Reviewer_a1YsOpenReview ↗
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Informativeness
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Paper summary

This paper investigates the “one-epoch phenomenon” in recommendation models with sparse embeddings, where additional training reduces training loss but degrades generalization. The authors propose self-influence asymmetry as an explanatory mechanism: after an example’s label has influenced its embedding, subsequent replay allows the shared downstream network to exploit this label-dependent information, creating a training advantage that does not transfer to fresh examples. The paper develops an exactly solvable scalar model and a local neural-network analysis, supported by intervention experiments that reverse the update order of the embeddings and the downstream network. Building on this analysis, the authors introduce uncertainty-weighted sensitivity regularization (UWSR), which uses gradient statistics accumulated during the first epoch to estimate embedding-row uncertainty and penalizes prediction sensitivity to uncertain representations in subsequent epochs. Experiments on three recommendation benchmarks, supplemented by baseline comparisons, ablations, cross-architecture evaluations, and computational cost measurements, demonstrate the method’s potential to mitigate multi-epoch degradation and improve predictive performance.

Critical strengths

1.The paper addresses a practically important problem. Recommendation models can suffer substantial generalization degradation when training data are reused, limiting the benefits of additional training. The paper directly investigates this issue with a clear research objective.

2.The paper offers a concrete mechanistic explanation for the one-epoch phenomenon. The proposed explanation centers on how an example’s label influences its own embedding, allowing the downstream network to exploit this label-dependent information during replay. Compared with broad explanations based on embedding overfitting or distribution shifts, self-influence asymmetry provides a more specific mechanism to analyze and yields experimentally testable predictions.

3.The experimental evaluation is reasonably comprehensive. The paper evaluates the method on three recommendation datasets with different characteristics, comparing against single-epoch training, standard multi-epoch training, and several representative remedies. Update-order intervention experiments further probe the proposed mechanism.

Critical weaknesses

1.The manuscript contains several cross-reference, typographical, and presentation issues. Page 13 contains an unresolved “Table ??” reference, and Table 4 appears before Table 3 on page 15. The text also includes errors such as “beyonf,” “grownth,” “comapred,” and “chosen form,” which should be corrected to “beyond,” “growth,” “compared,” and “chosen from,” respectively.

2.The ablations do not establish whether the proposed uncertainty weights outperform simpler alternatives. The analysis repeatedly emphasizes the vulnerability of embedding rows with low training support, yet the experiments do not compare UWSR against a sensitivity penalty weighted by occurrence counts, such as smoothed inverse-frequency weights.

3.The related-work discussion is incomplete and characterizes existing remedies too narrowly. The paper primarily discusses embedding resets and magnitude constraints. However, Hsu et al. (RecSys 2024) address the one-epoch phenomenon through two-stage contrastive ID pre-training, while Qi et al.’s TeMPO (KDD 2026) uses teacher representations to guide multi-pass training. These directly relevant approaches should be discussed to clarify UWSR’s contribution and practical requirements relative to a broader range of existing solutions.

Questions for authors

1.Prior work has examined one-epoch overfitting through feature sparsity, network adaptation, and model complexity. What observations can the proposed self-influence asymmetry explain that these existing accounts cannot? Could targeted experiments demonstrate the additional explanatory value of this perspective?

2.How does UWSR compare with a sensitivity penalty weighted by smoothed inverse embedding-row frequencies? Such a baseline would help assess whether the proposed uncertainty estimates provide benefits beyond occurrence counts alone.

4 comments

Inverse-Frequency Based UWSR Ablation

Q2 How does UWSR compare with a sensitivity penalty weighted by smoothed inverse embedding-row frequencies? Such a baseline would help assess whether the proposed uncertainty estimates provide benefits beyond occurrence counts alone

We agree that this is an interesting comparison. We would like to note that inverse-frequency weighting is a special case of our construction under the assumption of approximately uniform per-occurrence gradient second moments, similar in spirit to a homoscedastic approximation. To the best of our knowledge, no prior work has introduced a gradient norm regularizer with inverse-frequency weights for learned sparse embedding rows, nor are we aware of a theoretical framework outside our own that supports its effectiveness. We therefore view it as an ablation of our method rather than a baseline for purposes of comparison, but would greatly welcome any relevant prior literature discussing this.

We denote this construction as "count-weights", and provide comparison under multiple settings. As count-weights is a special case of UWSR, we find it performs on par with UWSR when the embedding gradient norms are approximately uniform. In general cases, however, it performs poorly compared to UWSR. In the table below, on the Amazon Electronics dataset, count-weights ties with UWSR when all the embeddings are in the first layer; in such a homogeneous architecture, the gradient magnitudes can indeed be similar.

MethodAUC E1AUC E2AUC E3AUC E4ΔBCE E2ΔBCE E3ΔBCE E4
Count-weights0.85230.86840.87220.8753+5.03%+6.07%+7.02%
UWSR0.85230.86870.87350.8754+5.10%+6.43%+6.78%

These results are now included in Table 10 (Appendix J) of the revised manuscript.

In practice, however, real world recommendation systems often use mixed architectures (for example: having both WuKong and attention based user interaction history modules). Thus, uniform gradient magnitudes cannot be assumed; simply inserting embeddings at different layers can cause this assumption to break down. In the experiment on the Amazon Electronics dataset below, we show that by inserting user and item embeddings at the first and last layers respectively, the performance of the count-weights method degrades considerably compared to our proposed UWSR. Moreover, UWSR’s improvement over count-weights grows monotonically as we increase the number of layers in this model. The deeper the model, the higher is the gradient ratio between the embeddings, consequently widening the gap between the performance of count-weights and UWSR.

# LayersAvg Gradient ratioUWSR vs Count-weights BCE improvementUWSR vs Count-weights AUC
23.29+0.73%+0.0030
43.80+0.91%+0.0021
65.04+0.93%+0.0025
85.39+1.17%+0.0042
106.69+1.88%+0.0049
129.00+2.50%+0.0095

The depth results are now included in Table 11 (Appendix J), and a corresponding plot appears as Figure 6 in the revised manuscript (see also https://i.imgur.com/1zRmqJ4.png).

In summary, the inverse frequency count-weighting method is a variant that follows naturally from our theory, and is effective only under the uniform gradient assumption. Our proposed UWSR has comparable computational cost and is more general: it does not require knowing in advance whether the assumption holds on a particular dataset or architecture.

Additional comments

Presentation Errors: We have done a thorough review and corrected the mentioned errors and others.

Literature Comparison Thank you for pointing us towards this relevant literature on the one-epoch phenomenon. We agree that these works provide essential context.

Hsu et al. (RecSys 2024) offer a contrastive pre-training approach to combat the one epoch phenomenon, but this additional training stage requires 10x more engagement data. TeMPO (Qi et al., 2026) proposes distilling from a pre-trained foundation-model teacher through calibrated soft labels and embedding alignment, starting with a teacher-only warm-up before joint training. Their method requires an additional teacher model to mitigate the one epoch problem. Additionally, their proposed architecture does not explain why degradation begins at the second epoch. UWSR, on the other hand, models the phenomenon itself. Our construction yields a regularizer that works inside standard single-stage training, with no teacher, extra data, or pre-training stage. Under this view, both prior methods reduce the leverage a single noisy label has on an embedding. We therefore see UWSR as complementary to them, not competing; UWSR could regularize the multi-epoch downstream stage of either method.

We have added references to these papers and discussion to Section 2 of the revised manuscript.

Q1.1 What observations can the proposed self-influence asymmetry explain that these existing accounts cannot?

Prior work either captures the one-epoch phenomenon empirically (Zhang et al. CIKM 2022) or bounds it theoretically (AdamAR; Li & Lyu, ICLR 2026), but neither derives why validation loss jumps at the epoch boundary nor provides a quantitative construction to describe it.

  • Zhang et al. (CIKM 2022) is an empirical study: they conduct experiments via feature sparsity and network adaptation to show the occurrence/non-occurrence of the one-epoch phenomenon. The authors find that the one-epoch phenomenon disappears when sparse-feature fields (item ID and history item IDs) are not used for training. While they are able to alleviate the one-epoch phenomenon by freezing the MLP layers, it is at the cost of accuracy.
  • AdamAR offers a complementary complexity-based account: a Rademacher-complexity upper bound in terms of embedding norms motivates regularizing those norms. The bound, however, does not offer an explanation for any sudden complexity changes at the epoch boundary, as the embedding norms grow smoothly through the epoch boundary.

Holistically, our self-influence asymmetry accounts for the empirical findings above and predicts the timing and shape of the jump. Our local analysis links the one-epoch phenomenon to classical statistical training optimism / overfitting (Efron, 1983, 1986, 2004).

Our analysis derives locally the expected difference between the model's loss difference on a label it has fit, and on a label it has not. It is p(1−p)p(1-p) (Bernoulli variance) times our proposed regularizer si⊤Σ^sis_i^\top\hat{\Sigma}s_i, where pp is the model's predicted probability. Our regularizer strength is controlled by a constant λ\lambda. This inspires:

Validation loss≈Training loss+λ∑i∈embeddingsp(1−p),si⊤Σ^si\text{Validation loss} \approx \text{Training loss} + \lambda\sum_{i \in embeddings} p(1-p),s_i^\top\hat{\Sigma}s_i

Fitting λ\lambda for effect calibration, and using the same relaxations we use to make our regularizer efficient, this reproduces the validation loss curve trajectory of the one epoch phenomenon in a striking way, including abrupt epoch-boundaries.

Please see Figure 7 in the revised manuscript (also available here): https://i.imgur.com/fyX8Zwk.png, which also includes a more precise but complex predictor.

In Appendix B of the revised manuscript, we present derivations for both formulations and explain their relationship to classical statistical optimism/overfitting in greater detail.

To summarize, neither prior work quantitatively reconstructs the epoch jumps or the trajectory that follows. To our knowledge, we are the first to quantitatively describe the incentive and account for these loss dynamics.

Q1.2 Could targeted experiments demonstrate the additional explanatory value of this perspective?

Yes, our theory directly predicts what happened in Table 11 (Appendix J) of the revised manuscript, also reported in our response to your Q2 [titled Inverse-Frequency Based UWSR Ablation above].

Concisely, our theory suggests the term to regularize is

s⊤I−1ss^\top \mathcal{I}^{-1}s

Here, I\mathcal{I} describes the gradient second moments for all the samples an embedding has been trained on.

If embedding gradient norms are uniform, then row-wise, I≈ frequency counts\mathcal{I} \approx \text{ frequency counts} is a good approximation.

Thus inverse frequency counts work as a reasonable surrogate for I−1\mathcal{I}^{-1} in the regularizer. If gradient norms are not uniform, then generally I≉ frequency counts\mathcal{I} \not \approx \text{ frequency counts}.

We would expect as the uniform gradient assumption becomes less accurate, UWSR's performance advantage should grow over the inverse frequency weighted version.

To illustrate this relationship with the uniform gradient assumption, we have recorded the average gradient ratio between the two embedding groups in the Avg Gradient ratio column. We see this ratio increases as the number of layers in the model grows.

Likewise, we see UWSR's validation loss improvement compared to the count-weights variant grows, exactly as our theory predicts. A corresponding plot appears as Figure 6 in the revised manuscript. We relink the plot here for illustration: https://i.imgur.com/1zRmqJ4.png.

Reviewer_a1YsOpenReview ↗

Official Comment by Reviewer a1Ys

Thank you for the additional experiments and clarifications. Since your responses have addressed most of my concerns, I am raising my rating from 2 to 3.

Thank you for your feedback and for reassessing the paper. Your questions helped motivate the count-weighting / insertion-depth and validation loss reconstruction experiments, which we believe have strengthened the manuscript.

Comments on the paper

1 comment

We’d like to thank all reviewers for their feedback and the time they have spent reviewing our paper.

We have uploaded a revised manuscript incorporating the clarifications and additional experiments described in our responses. Figures 6–7 present the count-weighting/depth study and validation-loss reconstruction. Appendix B connects Proposition 1 to classical statistical training optimism. Figures 8–9 (Appendices H and K) visualize the architecture and embedding-width results. Appendix I reports timing and memory benchmarks. We also expanded the MovieLens evaluation, clarified the theory and algorithm, and updated related work and cross-references. Revisions are highlighted in blue; relocated text is green.

We will shortly update our responses to point to the relevant sections, figures, and tables in the revised manuscript.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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