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Under review as a conference paper at ICLR 2027

Why Larger Models Learn More: Effects of Capacity, Interference, and Rare-Task Retention

Abstract

Larger models learn tasks smaller models do not. What drives this phenomenon? We develop a simple phenomenological argument that power-law scaling already suggests that a larger model will be able to learn a part of the data distribution that a smaller model fails to learn, even with infinite training data. To validate this claim and identify its causes, we study the effects of model scaling on a synthetic setup consisting of a mixture of tasks that show monotonic scaling curves. The results point to a data-induced competition over resources (neurons). Specifically, smaller models allocate their neurons to high frequency or low complexity tasks, and so they learn solutions that perform poorly on rare and complex tasks. Moreover, this happens even when solutions capable of expressing the desired task exist. We then assess how a larger model circumvents this data-centric bottleneck, finding that it traces to a reduced interference mechanism: larger models can allocate enough resources to common tasks that the gradient updates for those tasks become weak, which means that they do not overwrite rare-task features as they slowly accumulate. Finally, to further validate these claims, we pretrain OLMo models (4M to 4B parameters) on novel tasks of varying frequency and complexity. The results mirror those from our synthetic data experiments: only the larger OLMo models learn the infrequent and complex tasks, and these larger models embed more task features in their representations and show less gradient interference between tasks. Overall, we offer a data-centric account of why larger models learn tasks that smaller models fail to. This helps explain why larger models are better in practice, and it can inform practical questions concerning model sizing and training data mixtures.

Primary area:
interpretability and explainable AI
Keywords:
scaling laws, learning dynamics

Reviews

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1234this paper, Top 15%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_wS14OpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper investigates why large models can learn low-frequency or complex tasks that small models ignore in mixed training distributions, attempting to distinguish sample efficiency gains from persistent task learning bottlenecks. The authors establish a linear regression mixture model for orthogonal tasks, prove that the optimal shared representation selects features according to the product of task frequency and feature spectral strength, and use gradient bounds and a local competition model to explain the preservation of rare signals. Subsequently, the authors pretrain OLMo models of different sizes on Dolma, inject comparison and modular addition tasks with controllable frequencies, and analyze task performance, internal features, and gradient relationships. The results show that scale is associated with rare task learning, feature formation, and retention after updates.

Critical strengths
  1. The research question is important, and the control approach is clear. Through random token mapping and controllable injection frequency, the authors circumvent some of the difficulties in estimating natural task frequencies, making it easier to study the relationship between scale and long-tail learning.
  2. The theoretical model is easy to interpret and has testable predictions. The utility πkλk,j\pi_k\lambda_{k,j} provides a clear mathematical basis for ranking optimal representations, and the task boundaries and residual losses can be directly compared with experiments.
  3. Rich Experimental Analysis. The authors examine test accuracy, DAS sequential features, Fourier representations, and trajectories before and after injection. In particular, modular addition separates training fitting from generalization, providing extensive empirical evidence for mechanistic analysis.
Critical weaknesses
  1. Existing experiments do not adequately distinguish between forward transfer and subsequent forgetting. Although the authors controlled for the amount of training data and task frequency, large models may still obtain more useful representations from common tasks or learn more from each rare-task observation. The representational differences in Fig. 5 and the absolute loss decrease in Fig. 6a cannot distinguish among these explanations, and identical language model loss does not mean identical transfer ability. We suggest that the authors selectively supplement the analysis by freezing representations after common-task training and testing tail learning, by matching initial learning gains and then comparing forgetting rates, or by changing the task-sharing structure and adding update-protection controls, to further distinguish these mechanisms.
  2. Uniform hyperparameters mask differences in effective update speed across scales, so less forgetting may not entirely stem from weaker task interference. Appendix C.2 uses the same learning rate and training schedule for different scales, but these settings are not necessarily equally suitable for models of various scales, nor do they guarantee the same effective update magnitude. Large models may make smaller changes to existing representations during non-task updates, thereby exhibiting less forgetting at the same number of steps. We recommend that the authors discuss this alternative explanation, and if time permits, consider adding learning rate sensitivity analyses for representative scales, and compare retention ability under conditions matching initial task ability and non-task learning progress or output changes.
  3. The gradient cosine results for LLMs do not prove harmful interference. Sec. 4.4 treats nonzero cosine of non-task gradients as interference, and reports 0.10±0.090.10\pm0.09 for 20M and a near-zero value for 1B. However, under standard gradient descent, the first-order change in task loss is −ηgr⊤gnt-\eta g_r^\top g_{nt}, a positive inner product is usually beneficial to the task, and only a negative inner product indicates harmful conflict. Cosine also ignores gradient magnitude, Adam's actual update, and curvature, and the tendency toward orthogonality across scales may involve high-dimensional geometric effects. Therefore, it cannot show that nonzero cosine of non-task gradients is a form of interference. In addition, Sec. C.5 does not specify the KK for the top-KK neurons or the selection process.
Questions for authors
  1. How do you distinguish better transfer and larger learning gains from reduced forgetting? Could you compare forgetting after matching the initial rare-task learning gain?
  2. Do the retention differences persist across learning rates and after matching non-task learning progress or output changes?
  3. Why is the positive cosine similarity between non-task and task gradients interpreted as harmful interference? Could you measure rare-task loss changes caused by actual non-task optimizer updates?
  4. What value of KK is used for neuron selection, and how are these neurons selected? Does the cross-scale cosine trend persist with matched dimensions or randomly selected neurons?
5 comments

We thank the reviewer for the positive assessment and the detailed feedback. Several of the questions can be explained by one design choice that we should have stated more prominently, so we would like to clarify it first and then address each point.

A key design choice: no feature sharing between rare and common tasks. Both of our settings are built so that rare-task learning cannot benefit from features learned on common tasks:

  • Linear regression setting (Section 3): Task features occupy orthogonal blocks. Learning one task feature will not help another task.
  • OLMo setting: the injected tasks are built from 100 randomly sampled vocabulary tokens and arbitrary label tokens (App. C.3). The two tasks require the model to learn specific feature geometry (shown in Figure 5) from the randomly sampled token embeddings, i.e., relative magnitude and Fourier modes. It is unlikely that a model would learn such features from pre-training data, for example, if “ address”, “ analyze”, “pony” are the surface form of the random chosen token (L 1173), it is extremely unlikely a model would ever need to compute Fourier features from these token embeddings in pre-training examples. In fact, evaluating pre-trained OLMo checkpoints on this task or probing the features would give an accuracy at chance. As a result, we can assume that all batches between injections contain no task signals.

W1 / Q1: Distinguish between forward transfer and subsequent forgetting

We note that “forward transfer” is a term from the continual learning literature that seems to have little to do with the paper: we study a multi-task learning setting that does not involve curriculum. We hence interpret the reviewer’s concern as whether larger models learn the rare task better because they share more useful features from common tasks, rather than because they forget less.

Large models may still obtain more useful representations from common tasks or learn more from each rare-task observation. The representational differences in Fig. 5 and the absolute loss decrease in Fig. 6a cannot distinguish among these explanations, and identical language model loss does not mean identical transfer ability.

This would indeed be a concern if features can be shared between tasks. However, as we explained above, the necessary task features cannot be learned from common tasks. This is true both for the linear regression setting and the OLMo setting.

We suggest that the authors selectively supplement the analysis by freezing representations after common-task training and testing tail learning, by matching initial learning gains and then comparing forgetting rates, or by changing the task-sharing structure and adding update-protection controls, to further distinguish these mechanisms.

Thanks for the suggestions! In particular, we believe the suggested freezing experiment has an analytic answer in the linear regression setting. A representation trained only on common tasks spans the common block, so the rare-task loss stays at the mean-predictor baseline. Consistent with this, when the common-task residual is large, the rare-task signal is no better than random (App. F.2).

Moreover, varying the task-sharing structure is an interesting extension that we discussed in our response to Reviewer WUwi W1.

W2 / Q2: Uniform hyperparameters and effective update speed.

Appendix C.2 uses the same learning rate and training schedule for different scales, but these settings are not necessarily equally suitable for models of various scales

This is a fair point about possible suboptimal convergence, and we agree that the best way to isolate the effect of convergence is to conduct an exhaustive hyperparameter sweep. However, even with the optimal hyperparameters, the retention effect likely will persist: For any finite learning rate, there is a gap beyond which the rare-task signal is overwritten between injections. The critical gap scales roughly as 1/(η⋅cN)1/(\eta \cdot c_N), where the erasure rate cNc_N shrinks with width (Theorem 4, Corollary 5). The learning rate rescales the critical gap but wider models remain better.

nor do they guarantee the same effective update magnitude. Large models may make smaller changes to existing representations during non-task updates, thereby exhibiting less forgetting at the same number of steps.

Thanks for pressing on alternative mechanisms here. The hypothesized competing mechanism, i.e., the same learning rate + larger model ⇒\Rightarrow smaller effective update magnitude, can be largely ruled out by observations in Fig 6a. Learning rate schedule and effective update magnitude universally apply to all gradient updates; if a larger model makes smaller changes on non-task updates, such a model would also learn less from each injection, and we do not observe this: larger models do not have smaller immediate gain (Fig. 6a).

If the reviewer had a different mechanism in mind, we would be glad to hear it and see if we can run a targeted analysis.

We recommend that the authors discuss this alternative explanation, and if time permits, consider adding learning rate sensitivity analyses for representative scales, and compare retention ability under conditions matching initial task ability and non-task learning progress or output changes.

Thanks for the suggestions! App. G.1 might have already provided one piece of such evidence by matching non-task learning progress, i.e., general language modeling loss, as the reviewer suggests. At equal general language modeling loss, rare-task loss is similar across sizes at higher frequencies, but larger models achieve lower task loss at 2.4e-7, where smaller models plateau.

W3 / Q3 / Q4: Does a nonzero cosine indicate harmful interference?

Sec. 4.4 treats nonzero cosine of non-task gradients as interference, and reports for 20M and a near-zero value for 1B. However, under standard gradient descent, the first-order change in task loss is, a positive inner product is usually beneficial to the task, and only a negative inner product indicates harmful conflict.

The reviewer is right that, in general, a positive inner product reduces task loss to first order and indicates transfer. However, as we explained above in our design choice, the injected task shares no structure with the pre-training data, so any alignment between non-task gradients and the task direction is not transfer, but rather interference. Moreover, the net effect of these updates is measured directly in Fig. 6a. If the 20M model’s positive alignment were beneficial, its task loss would continue to fall between injections. Instead, the gain from each injection is lost within ~20 steps.

Cosine also ignores gradient magnitude, Adam's actual update, and curvature, and the tendency toward orthogonality across scales may involve high-dimensional geometric effects. Therefore, it cannot show that nonzero cosine of non-task gradients is a form of interference.

We agree that cosine similarity alone does not establish how large the interference is. It also ignores Adam preconditioning, and curvature, and we will soften our wording in Sec. 4.4 accordingly.

However, our primary goal is to determine whether interference is present, and cosine remains a valuable metric for this. Specifically, our mechanism concerns whether task and non-task losses act on shared parameters, which is a directional property. Dimensionality difference is not a concern here as the gradient is computed on top-N neurons. Moreover, raw inner products are not comparable across model scales and are dominated by non-task gradient norms. Adam’s per-coordinate normalization also largely removes raw gradient magnitude from the actual update. Again, as direct evidence to establish inference, the magnitude of the resulting harm is captured instead by Fig. 6a, which integrates the effect of actual optimizer updates over each injection gap.

What value is used for neuron selection, and how are these neurons selected? Does the cross-scale cosine trend persist with matched dimensions or randomly selected neurons?

We use K = 100 neurons in the first-layer MLP, which has the largest causal effect on the task prediction across all models (App. C.5). Within this layer, we select the neurons with the largest gradient magnitude with respect to the task loss. Task features are represented in a distributed way, so the results are not sensitive to the exact value of K.

Regarding randomly selected neurons, they would not have the same causal effects on model outputs, i.e., the model does not even use these neurons in its task computations, hence it is unclear what is the significance of looking at their gradients cosine similarity.

Reviewer_WUwiOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper studies why larger models can learn tasks that smaller models fail to learn, from a data-centric perspective. It conducts theoretical analysis on linear MTL data and finds that: (1) Larger models learn rarer and more complex data; (2) scaling reduces gradient interference between common and rare tasks; and supports retention of rare task data. The paper then validates the claims by pre-training different-sized OLMo models, with controlled rare task frequency.

Critical strengths
  1. The data-centric perspective for model scaling is interesting and may benefit data curation and model selection for pretraining.

  2. The paper provides both theoretical and experimental analyses for the claims.

Critical weaknesses
  1. The paper studies a data-centric perspective of model capacity. However, the data pattern studied is relatively simple.

    • The theoretical analysis assumes that different tasks occupy orthogonal blocks; MTL data are controlled by task frequency and relative complexity (spectral decay), with a focus on task frequency. In experiments, only task frequency is considered. It is hard to evaluate how well the claim fits in real-world scenarios.
  2. The definition of rare tasks is unclear to me.

    • Do rare tasks only appear less frequently than 'common’ tasks? What if a task appears less frequently, but has data with large magnitude eigenvalues? Does the retention claim still hold? Is the interference between rare and frequent tasks still reduced?
  3. Some experiments do not clearly support the claims:

    • In Figure 4 (a) (b), both smaller and larger models have improved performance when the rare task appears more frequently. In this case, how to disentangle the factor of data scaling?
    • In Figure 6(a), larger models have less loss after the task injection, but the loss also increases faster when training without the injected task (especially in the first 200 steps). It seems like a learning more, forgetting more pattern. How does it support the ‘retention’ claim?
Questions for authors

Please see the weakness.

4 comments

We thank the reviewer for the thoughtful questions, which point out definitions and figure captions that could be made clearer. Below we address each point, mostly by reorganizing existing evidence, as several results are in the appendix and are easy to miss.


W1 “the data pattern studied is relatively simple… hard to evaluate how well the claim fits in real-world scenarios”

The theoretical analysis assumes that different tasks occupy orthogonal blocks

This is a fair point that we focus on a setting where task features are orthogonal. However, orthogonality is a simplification for cleanly attributing task learning to individual features, not a requirement of the core theoretical results. In particular, if we examine the core theoretical results in the paper, Theorem 3, Theorem 4, Corollary 5 do not depend on orthogonality, only Proposition 6’s clean critical width threshold relies on the orthogonality assumption. Based on our theorems, when tasks share features, the shared features pool utility across tasks. This would make a rare task that overlaps with common tasks easier to learn, which is intuitive. Scaling is still needed for the rare task’s unshared or low shared utility residual features.

Below, we provide a sketch of a more general setup: a partially shared setting in which the feature space is divided into orthogonal blocks, but task directions within each block may overlap. This captures a more realistic regime in which task structure is partially shared. We leave a full treatment to dedicated future work.

  • The core of Theorem 3 is unchanged: for arbitrary task covariances, the optimal width-N encoder spans the top-N eigenspace of the aggregate covariance. With overlap, the utility of learned eigenvectors aggregates their frequency-weighted benefit across tasks. Scaling is still needed for the rare task’s unshared or low-collective-utility residual features.
  • Theorem 4 and Corollary 5 remain valid without orthogonality as they depend only on the aggregate common-task covariance and its unexplained residual. Under feature sharing, the norm bound in Theorem 4 still holds, but a common-task gradient is no longer necessarily harmful: it can be decomposed into positive transfer and destructive interference. This produces a two-stage learning: Early on, common-task gradients can provide positive transfer by constructing shared features useful to the rare task. Once those shared features have been learned, their gradients vanish, but the transferred features remain in the representation. The remaining common-task gradient acts on unresolved features and can still overwrite the rare task’s non-shared residual. Increasing width reduces this residual gradient and therefore primarily reduces destructive interference with unshared rare-task features, rather than eliminating all cross-task interaction.
  • Proposition 6’s critical width threshold does rely on orthogonality: If the rare direction lies in the occupied common subspace, its representation is already available. If it partially overlaps that subspace, the optimum generically rotates toward it for any nonzero rare-task weight, yielding graded positive transfer rather than a clean threshold.

In experiments, only task frequency is considered.

Experiments in the main text are focused on frequency. However, we do provide experiments on complexity in appendix E: Further Experimental Results: Complexity Sweeps.

Moreover, for OLMo experiments, we do not emphasize complexity because a precise definition for a natural language task remains an open research question. However, loosely speaking, the two injected tasks, i.e., comparison and modular addition, do have a complexity contrast: The two injected tasks differ in the number of features they require, as shown in Section 4.3. Comparison requires a single direction feature that encodes the relative magnitude, while modular addition requires a set of Fourier bases. Following our definition of task complexity in Theorem 3, the modular addition task would require more feature directions than the comparison task, and hence more complex. This complexity ranking indeed is consistent with the empirical observations: given the same task frequency, i.e., 2.4e−5, the comparison is better learned at all model sizes (Figure 4 (a) first row vs. Figure 4 (b) last row).

It is hard to evaluate how well the claim fits in real-world scenarios.

We hope that the clarification above on the orthogonality assumption and empirical evidence on complexity help tighten the connection between our theoretical and empirical results.

Additionally, we would like to point out that apart from OLMo pre-training with injected tasks, we also study two reference tasks directly observed from pre-training data RCMPR_{CMP} and RADDR_{ADD}. This validates that our setup reflects a real pre-training pipeline: the injection frequency and injected tasks are both naturally occurring in the OLMo pre-training data.

W2 Definition of rare tasks

We thank the reviewer for pointing out a terminology that we should have been more precise about. In particular, the comment made us realize that in Section 3, we use “rare task” and “common task” to broadly refer to low-utility and high-utility tasks. We have updated these instances in the pdf to explicitly say low-utility and high-utility.

Do rare tasks only appear less frequently than 'common’ tasks?

For experiments in the main text, we use “rare” to refer to “infrequent” and “common” to refer to “frequent”, so yes, rare tasks appear less frequently than common tasks.

As we explained above, what makes things a bit confusing is that in Section 3, our theorems concern both frequency and complexity, yet we still use “rare” to generically refer to low-utility tasks in a few places. To disambiguate, we have updated all such instances in Section 3 to use the term “low-utility tasks” instead.

What if a task appears less frequently, but has data with large magnitude eigenvalues? Does the retention claim still hold? Is the interference between rare and frequent tasks still reduced?

With the clarification of “rare task” above, we believe the tension between less frequent but lower completely should be resolved: both factors contribute to the notion of utility (Theorem 3). Similarly, the retention and inference claims in Section 3 are both made in terms of utility.

W3 How Figure 4 and 6 support claims

In Figure 4 (a) (b), both smaller and larger models have improved performance when the rare task appears more frequently. In this case, how to disentangle the factor of data scaling?

This is a good observation. Higher frequency helping every model is expected: Theorem 3 predicts that increasing frequency increases the task’s utility regardless of model size.

In terms of disentanglement, several existing results separate the effects of model size from the amount of task data:

  • Fixed model size, varying task frequency: Within each column of Fig. 4(a) and (b), we vary task frequency but hold model size fixed, this isolates the effect of task frequency.
  • Fixed data, varying model size: Within each row of Fig. 4 (a) and (b), all models see the exact same training data, while larger models have higher task accuracy, i.e., they can learn lower utility tasks compared to smaller models.
  • Training on more data does not close the gap for small models. In the linear regression setting, with 10x longer training (1M steps, App. F.4, Fig. 18), above-capacity tasks stay at the mean-predictor baseline. In OLMo, plotting task loss against general LM loss (App. G.1, Fig. 19) shows two regimes: at higher frequencies (2.4e-6 to 2.4e-5), all sizes follow the same trajectory; this is the “learnable via data scaling” regime of Def. 1. At 2.4e-7, smaller models plateau one by one at different values, matching the “requires model scaling” regime of Def. 2. These show that data scaling explains part of the improvement (Def. 1). However, there is a residual gap that only model scaling closes.

In Figure 6(a), larger models have less loss after the task injection, but the loss also increases faster when training without the injected task (especially in the first 200 steps). It seems like a learning more, forgetting more pattern. How does it support the ‘retention’ claim?

This is another good observation. The curve does have a drop followed by an increase, and it is tempting to interpret the lowest point purely as how much the model learns. However, this drop already captures the effects of retention: the plot interval is 20 steps, yet the model sees the task data only at the first step. Earlier on in training, the smallest model does have smaller gain at the first step, but this accounts for less than 20% of the gap observed at step 20. As training progress, this difference in initial gain mostly disappears. We will add this analysis to the paper. The gradient plot in 6(b) also provides some evidence: by separating learning and interference into the middle and bottom row, it shows the difference in gradient similarity at the injection step is relatively small, yet there is a big difference in gradient inference at non-injection steps.

Thanks for addressing my concerns. I have raised my score to 3.

Reviewer_dgR6OpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
3
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Paper summary

This paper investigates why larger models can learn tasks that smaller models fail to learn. Through a theoretical argument and experiments, the authors suggest that a key advantage of larger models is their ability to learn and retain rarer tasks, which smaller models tend to neglect in favor of more frequent ones.

Critical strengths
  • A simple and intuitive theoretical argument that helps explain the observed scaling phenomena.
  • Experiments on large-scale language models that provide empirical support for the proposed explanation.
Critical weaknesses

My main concern is the distinction between the effects of model capacity and optimization. The theoretical argument concerns the optimal performance achievable at a given model size, whereas the experiments necessarily also capture the effects of optimization. It is therefore not entirely clear to what extent the observed differences are explained by the proposed theoretical mechanism rather than differences in optimization dynamics.

Questions for authors

Could the authors discuss how to disentangle the effects of optimization from those of model capacity and the task distribution, which are central to their theoretical argument? In particular, to what extent might the observed differences between small and large models persist if optimization were not a limiting factor?

2 comments

“My main concern is the distinction between the effects of model capacity and optimization”

We thank the reviewer for raising an important point on how representational capacity and optimization can interact. Because “optimization” in the question can refer to two aspects: (1) suboptimal convergence under certain optimizer and hyperparameter choices and (2) the dynamics of gradient updates over the skewed data mixture, we would like to address each aspect separately to clarify what is disentangled in our theory and experiments.

“The theoretical argument concerns the optimal performance achievable at a given model size, whereas the experiments necessarily also capture the effects of optimization. It is therefore not entirely clear to what extent the observed differences are explained by the proposed theoretical mechanism rather than differences in optimization dynamics.”

We agree with the reviewer that model capacity alone, i.e., expressivity, does not explain the scaling phenomenon observed (L20 and L58). In fact, both our theory and experiments deliberately capture effects of optimization dynamics.

Our theoretical claims contain two parts: The first part, Section 3.1 theorem 3, describes the optimum at width N containing which features, which is aligned with reviewer’s comment “the optimal performance achievable at a given model size”. The second part, Section 3.2, deliberately makes a mechanism claim about optimization dynamics. Specifically, in theorem 4, corollary 5, and proposition 6, we explicitly construct a regime where the model has sufficient expressivity to represent the task, yet fails to learn it due to gradient interference, where high utility task gradients override low utility task gradients. Thus, optimization dynamics, rather than being a confound in experiments, are a core mechanism of our theoretical claims.

This aspect of optimization is also explicitly shown in the experiments: gradient interference between high and low utility tasks is measured in Figure 3 and Figure 6 for linear regression and LLM pretraining respectively.

“How to disentangle the effects of optimization from those of model capacity and the task distribution. In particular, to what extent might the observed differences between small and large models persist if optimization were not a limiting factor?”

Regarding the convergence aspect, we agree that in the experiments, especially the OLMo experiment, there could be suboptimal convergence. The best way to isolate the effect of convergence is to conduct an exhaustive hyperparameter sweep. However, even with the optimal hyperparameters, the retention effect likely will persist: For any finite learning rate, there is a gap beyond which the rare-task signal is overwritten between injections. The critical gap scales roughly as 1/(η⋅cN)1/(\eta \cdot c_N), where the erasure rate cNc_N shrinks with width (Theorem 4, Corollary 5). The learning rate rescales the critical gap but wider models remain better.

Regarding the optimization dynamics, as we discussed above, this is the mechanism to explain how capacity enables learning. If we remove optimization effects altogether, i.e., an oracle finds the global minima of the entire data mixture, then the difference between smaller and larger becomes their expressivity difference, as shown in Theorem 3.

I thank the authors for their detailed answer, I will keep my score.

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