-->PCOMPBIOL-D-25-02227

The curriculum effect in visual learning: the role of readout dimensionality

PLOS Computational Biology

Dear Dr. Bakhtiari,

Thank you for submitting your manuscript to PLOS Computational Biology. After careful consideration, we feel that it has merit but does not fully meet PLOS Computational Biology's publication criteria as it currently stands. Therefore, we invite you to submit a revised version of the manuscript that addresses the points raised during the review process.

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Tim Christian Kietzmann, Dr. rer. nat.

Academic Editor

PLOS Computational Biology

Marieke van Vugt

Section Editor

PLOS Computational Biology

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Reviewers' comments:

Reviewer's Responses to Questions

Comments to the Authors:

Please note here if the review is uploaded as an attachment.

Reviewer #1: In this paper the authors show significant evidence that readout dimensionality relates to transfer learning performance and that this may explain the impacts of curriculum order on perceptual learning. While I generally find the argument compelling, I have some questions about methods and results.

Methods Questions:

Regarding the transfer task for the model: why do the authors test transfer across spatial frequency in the model when this is not what is done in the humans? I understand the point about not testing spatial transfer in a CNN but why not also use a different reference orientation for the transfer test rather than different spatial frequency? Having the transfer test be of the same dimension as the learning itself (i.e. changing the reference orientation in an orientation judgement task) seems perhaps significantly different than performing an unrelated transfer task (i.e. changing spatial frequency in an orientation judgement task).

When training readouts, does every individual unit in a readout layer get its own weight or is there some kind of global pooling over feature maps such that weights are one per channel?

These descriptions are inconsistent (I assume the first is correct):

228: "We used the mean of the absolute gradient values as a measure of the learning signal

that drives the changes in a model’s performance."

744: "the absolute value of the mean was taken over all the gradients

of the model’s training loss with respect to the model weights for the full model."

The authors use "mean accuracy on the first n easy trials minus the mean accuracy on the first n hard trials [as] a proxy measure of each observer’s implicit curriculum". But as n goes to zero this clearly is just a measure of the definition of hard versus easy trials (i.e. before training there will be a large difference between hard and easy trials). It seems like a measure of implicit curriculum would need to include some measure of the rate of change of learning for easy versus hard trials. The authors go on to note that their measure indeed does not predict learning for small n, and only does so for medium n (by including later trials the difference in learning rate is more detectable). I'd like more clarity on why the authors chose this metric to begin with.

The authors say "For Fig. 4C, neurons were lesioned incrementally 10 at a time based on the absolute weight value, i.e. first the largest 10 weights were lesioned, then the largest 20 weights, etc". Are the neurons actually lesioned or just their weights to the readout? I.e. can the neural activity still propagate to the next layer in the network or not?

How was figure 5B made? The methods say "PCA was calculated on the final activations

of the 150-neuron readout subspace for a representative model". But aren't these 150 neuron subspaces different for each style of learning? Does this mean that the PCs are actually different for each different color of dot and therefore the axes are not actually shared?

Results Questions:

The authors largely focus on transfer accuracy when reporting results, but it would be helpful, to contextualize those results, to know about any differences in accuracy on the trained task for these same models. For example, do the models that have worse transfer performance have higher performance on the trained task?

The authors should plot the same behavioral analysis as done for humans in 3A for the models, in addition to the weight analysis as it is the more direct comparison.

The authors focus on the finding of how much readout dimensionality can predict transfer learning, but they say less about what features are actually being represented or used. Of course low dimensionality alone is not sufficient to induce good performance if the wrong dimensions are chosen. When the authors test if enforcing low-dimensional readout during training on hard tasks leads to better transfer performance, they restrict learning to the neurons already known to contain the needed information, so this still conflates low-D representations with also using the correct features. I would, in particular, be interested to know if the models trained on hard-only tasks are using a different set of features than the low-D models or are instead using the same low-D set of features plus many more. In the first case, poor transfer is explained by having mismatched features but in the second it would be explained more by having extra features that contribute noise. These differences could also help predict the extent to which one can recover from poor initial training (e.g. do you need to completely relearn or just prune the extra, noisy dimensions). As far as I can tell the current analyses don't speak to this, but given that all models are based on the same AlexNet it would be potentially straightforward to determine if the same neurons are in the top 150 for different learning approaches. I wouldn't say such an analysis is technically required to support the claims of the paper, but I do feel like a part of the story is missing here.

Reviewer #2: The manuscript "The curriculum effect in visual learning: the role of readout dimensionality" by Volk et al. presents a compelling theoretical study of how readout dimensionality influences visual learning and transfer. The authors propose that easy-to-hard curricula promote the learning of low-dimensional solutions, which can then support improved transfer to harder tasks. The study offers an elegant explanation for curriculum learning effects in both artificial neural networks and human learners. Overall, I find the central claim convincing and the work conceptually valuable. That said, I have several methodological questions and points for clarification - If addressed, this would further strengthen the paper.

Major comments

1. Interpretation of curriculum order and interleaving (line 58)

The manuscript states that "interleaving different task conditions can also enhance generalization," but the subsequent discussion emphasizes that task order matters. The cited literature does not clearly establish that order effects differ between interleaved and sequential training. It would be helpful if the authors could clarify whether they are suggesting that both interleaved and sequential curricula enhance generalization, but that the effect is stronger for sequential curricula. If so, this claim may require additional justification or references.

2. Human generalization across sequential and shuffled conditions (line 99)

The observation that humans show similar average generalization improvements in both sequential and shuffled conditions is described as "interesting." This result does seem unexpected given the authors' interpretation that order matters, but it is also consistent with the literature cited earlier (line 58) regarding interleaving benefits. A brief discussion reconciling these two interpretations would improve clarity.

3. Differences between human and model test sets (lines 125, 129)

Humans are tested on different angles at different spatial locations, whereas ANNs are tested on different frequencies. While the authors provide reasonable arguments for these choices, it seems that testing both humans and models on a shared or more closely matched test dimension (e.g., different angles) would have been feasible. Using more comparable test sets could strengthen cross-system comparisons and help isolate whether observed differences arise from distinct learning strategies rather than task design. Perhaps the authors could elaborate a bit more why this was not done or perhaps it could still be done with a reasonable amount of effort.

4. Initialization of readout weights and learning dynamics (lines 156, 646)

The authors argue that learning in the models occurs predominantly through changes in readout weights. However, since the readout weights are initialized to zero and the models are trained via backpropagation, earlier layers cannot receive gradient updates until the readout weights become non-zero. This setup may introduce a bias toward readout-driven learning early in training. To rule out this possibility, it would be informative to repeat key analyses with randomly initialized readout weights matched in scale to other network weights.

5. Identifying influential neurons via readout weights vs. functional contribution

To support the claim that readout subspace dimensionality determines generalization, the authors identify influential neurons by lesioning units with the largest absolute readout weights and measuring the resulting drop in transfer accuracy (ll 310). While this approach is intuitive, large readout weights do not necessarily imply large functional importance for task performance or generalization. A more principled measure of neuron importance would be to assess each neuron's contribution to training or validation loss, for example, by quantifying the increase in loss when a neuron is dropped or masked as done in standard gradient-based attribution techniques. Such an analysis more directly captures functional relevance rather than reliance on weight magnitude alone. Incorporating (or at least discussing) this alternative lesioning criterion would strengthen the link between readout dimensionality and generalization.

6. Correlation between effective rank and transfer accuracy (line 336, Fig. 4E)

The manuscript reports a strong positive correlation (r = 0.95) between effective rank and transfer accuracy. However, according to the stated hypothesis, this relationship should be negative, as is reported elsewhere (e.g., line 332) and as appears visually in Fig. 4E. It is possible that the reported correlation refers instead to the relationship between the easy:hard ratio and transfer accuracy, as described in the figure caption. Clarifying this point and, if necessary, correcting the text would avoid confusion.

7. Performance when training only on the easy task (Fig. 5C)

In Fig. 5C, training exclusively on the easy task appears to yield higher mean transfer accuracy (~0.95) than either the sequential or shuffled curricula. This result is somewhat surprising given the emphasis on curriculum learning. A discussion of why training only on the easy task outperforms the proposed curricula, or whether this difference is statistically reliable, would be valuable.

Minor comments and clarifications

- Terminology: implicit vs. explicit curricula (line 271)

The distinction between a "forced implicit curriculum" and an "explicit curriculum" is unclear, and the terminology appears somewhat inconsistent across the paper. A brief clarification or standardization of terms would improve readability.

- Reporting correlation strength and significance (line 332)

The phrase "negatively correlated" would benefit from a quantitative report of the correlation coefficient and its statistical significance.

- Section references (line 377)

The manuscript refers to "Section 3.5," but the sections are not numbered. Please revise the reference to avoid confusion.

- Figure labeling (Fig. S1B)

The x-axis in Fig. S1B appears to be labeled "Angle separations," but, based on the description, it may be more accurately labeled "Steps."

Reviewer #3: Overall the premise of the paper is interesting. The human data on learning curriculum is a strong part of the paper and the analysis on dimensionality changes with learning curriculum is novel. However, the major weakness lies in the modeling details. The experiments are conducted with a single convolutional ANN architecture, and it is not obvious that the results would generalize to other models. The discussion mentions that testing other model architectures is beyond the scope of this work, however, if the observed changes in representation due to learning are a common motif that will happen in any learning system, then it *should* replicate across other architectures. For this type of study, showing that the results generalize across models is critical – small changes such as learning rate choice, optimizer choice, initialization choice, etc. can have a large effect on the model representation. Given the VPL task and the small number of training steps required, training additional models to verify generalization seems feasible and would significantly strengthen the work. If the authors decide that additional models are infeasible for the study, then the language throughout the paper, including abstract, introduction, etc should be changed to avoid talking about “ANNs” generally and instead talk about the specific model (and architecture) that was used.

128-131: The difference between the types of generalization that are tested in humans and models seems like a confound if the goal of the paper is to directly compare generalization in humans and machines. This is especially concerning given that the reason given is variability across observers, but later on observer variability is highlighted as an interesting feature of the learning curriculum.

127: “convolutional ANNs are equivariant to spatial location” – as far as I can tell from the methods, this is incorrect for the model architecture used for the following reasons: (1) with the described AlexNet-style architecture, the final stage before the fully connected readout layer maintains some spatial information, so the actual readout will not be equivariant to location (2) typical boundary handling operations, like padding, break perfect shift-equivariance (3) operations such as strided convolutions and max pooling result in non-equivariance to small transformations (see https://arxiv.org/pdf/1904.11486 & https://arxiv.org/abs/1805.12177). I understand that this is not the focus of the paper and the text describes what seems like a somewhat minor modeling choice, however given that this is a study primarily about modeling, it is critical that the description of the ANN properties and training setups is technically precise.

154-156: I am concerned that the change in the L2 norms of the weights may be confounded by underlying different scales for the feed-forward convolutional layer weights and the skip connection weights, or potentially the number of parameters that go into the L2-norm. It might be better to normalize the change in weight magnitude by something like the final weight norm. Additionally, how does the learning change if the skip connection weights are initialized at different values other than exactly zero? It is a bit non-standard in deep learning to initialize to exactly zero (small non-zero values can help break symmetries and prevent the network from getting “stuck”) so I was a bit surprised by this choice.

207: Please describe how multiple points for the model results are obtained (I believe that each point corresponds to a different random trial order and different random noise applied during training, but I could not find this detail). Going back to my request at the beginning of the paper regarding different architectures, the results would be much stronger if there were multiple architectures included in the results, for instance if each point were a different pre-trained neural network backbone (including transformers, different CNNs, etc).

300: Additional details on how PCA was performed should be given in the methods. Was any whitening performed on the weights? Were the weights flattened? How were the weights from different readout layers combined?

315, Question: Are the ~150 neurons the same for each of the model instances that are trained, or is a different subset of 150 neurons selected?

746-749: Minor: Even though only one type of trial is used for training, the gradient magnitudes for the other conditions could still be *measured*, but not used for updates.

Line 71 & 109 -- Question: How is a “distinct visual feature” (line 71) or a “dissimilar visual feature” (line 109) defined for the paper? The definition of a “feature” vs. “feature combination” seems important, and from the paper I’m not quite sure what the authors mean.

The authors may want to include a brief discussion on this recent work: https://www.nature.com/articles/s41562-025-02359-3

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Reviewer #1: None

Reviewer #2: No:  The authors wrote "All code necessary to reproduce the results are available at the following link for the initial submission: Link." but the "Link" is not clickable (although underlined). Perhaps this is a problem due to the journal's PDF conversion? It would be great if this worked in the final version or if the actual link was included in plain text. Same problem with the raw data.

Reviewer #3: None

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Reviewer #1: No

Reviewer #2: No

Reviewer #3: No

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PCOMPBIOL-D-25-02227R1

The curriculum effect in visual learning: the role of readout dimensionality

PLOS Computational Biology

Dear Dr. Bakhtiari,

Thank you for submitting your manuscript to PLOS Computational Biology. After careful consideration, we feel that it has merit but does not fully meet PLOS Computational Biology's publication criteria as it currently stands. Therefore, we invite you to submit a revised version of the manuscript that addresses the points raised during the review process.

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We look forward to receiving your revised manuscript.

Kind regards,

Tim Christian Kietzmann, Dr. rer. nat.

Academic Editor

PLOS Computational Biology

Marieke van Vugt

Section Editor

PLOS Computational Biology

Additional Editor Comments (if provided):

Dear all,

I am happy to let you know that all three reviewers have accepted the paper. I will therefore also accept the paper. Before I can do so, however, I would like to ask you to take note of two minor comments raised by R3, which I would like for you to address quickly before we move on to official acceptance.

Best wishes

Tim

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Reviewers' comments:

Reviewer's Responses to Questions

Comments to the Authors:

Please note here if the review is uploaded as an attachment.

Reviewer #1: I appreciate the substantial work the authors put in to update the manuscript.

Reviewer #2: Thanks for addressing all points.

Reviewer #3: The revisions have significantly strengthened the work. I particularly appreciate the addition of the new model architectures, and the results with the reference angle seem much closer to the human behavioral work. It is nice to see that the results generalize in both cases. Overall, the revision has substantially improved the paper. I have two fairly minor suggestions about the architecture results:

Appendix S1: > “However, our results did not extend to other larger and more complex model backbones (see Methods for a complete list of architectures), which are less accurate approximations of visual system architecture and connectivity (24).”

I’m not sure reference 24 is appropriate for this claim, as the paper is about privileged representational axes and not connectivity (and also has a wide range of tests for ResNet50 and ResNets are one of the architecture types that the authors reported as not generalizing).

Lines 739-740: > “We also tried more complex architectures: ConvNeXt, DenseNet121, MNASNet, MobileNetV1/V2, SqueezeNet, ResNet18, and VGG11/16.”

It seems like an additional description of why these results weren’t included would be appropriate, for instance including some of the wording that was given in the rebuttal response. Documenting what didn’t work (and potential reasons why) seems important for reproducibility purposes and future work.

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Reviewer #1: None

Reviewer #2: No:  The authors promise to make the data publicly available upon acceptance for the review they provided Google Drive links.

Reviewer #3: Yes

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Reviewer #1: No

Reviewer #2: No

Reviewer #3: No

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Dear Dr. Bakhtiari,

We are pleased to inform you that your manuscript 'The curriculum effect in visual learning: the role of readout dimensionality' has been provisionally accepted for publication in PLOS Computational Biology.

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Tim Christian Kietzmann, Dr. rer. nat.

Academic Editor

PLOS Computational Biology

Marieke van Vugt

Section Editor

PLOS Computational Biology

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