Response to reviewer MyoH

Dear Reviewer,

Thank you for your feedback and your recognition of the interesting aspects of our paper. We have addressed your highlighted Weaknesses and Questions one by one below:

Weaknesses

1. We acknowledge that when choosing problems to test our approach we used behavioral settings and plasticity rules that were relatively simple. Our choice of problems was inspired by the kinds of behavioral data that our colleagues had available to test our approach on, and it is something that can be expanded upon in the future to include more complex problems. Despite this, we believe that the experiments described in this paper suggest that our approach can in fact be applied to more complex situations. Our reasoning for this is two-fold:
   • First, while we made the theoretical assumption in this paper that the plasticity rule is a function of only presynaptic activity, postsynaptic activity, reward, and the current weight value, our fitting procedures are designed such that additional terms can be added without difficulty. This would allow us to estimate a large variety of plasticity rules.
   • Second, we simulated and were able to retrieve a large number of basically arbitrary plasticity rules (in the Appendix) from neural trajectories. This estimation also showed resilience to noise and sparsity of the input data.

Questions

1. You are correct that the subscripts in Eq (5) had a typographical error. We have updated the text to reflect this. Thank you for pointing this out.

2. Regarding the R-squared calculation in Figures 2E and 2F, we calculated the R-squared score by comparing the weight trajectories of the ground truth rule with the weight trajectories of the inferred rule after the learning rule optimization was completed. In particular, our R-squared comparison was not limited to the final weights, and it instead compared the full trajectories.

3. The Reviewer is correct that our method sometimes infers plasticity rules that poorly approximate the weight trajectories, activity trajectories, and/or behavioral trajectories (Tables 1 and 2). This isn’t surprising because plasticity rules are nonlinear dynamical systems, and their predictions may depend very sensitively on parameters and initial conditions. We would contend that no inference method will ever be able to perfectly recover an arbitrary plasticity rule, and the intention of Tables 1 and 2 is to merely illustrate the range of things that are possible. Nevertheless, we would hypothesize that the rules implemented by biology are less unwieldy than some of the possibilities revealed by the tables. Indeed, our method works very reliably on the canonical rules that were designed to do useful computations and/or capture biological phenomena. We hope that using our framework to fit real data will help us to identify novel, well-behaved rules without necessitating laborious hand design.

4. In Section 5, we fit behavioral data from 18 flies, utilizing the full dataset for our reported results. We acknowledge, however, that incorporating cross-validation would strengthen our analysis. If our paper is accepted for publication, then we commit to implementing this approach and including it in the final version of our manuscript, thereby enhancing the robustness of our model evaluation. It's worth noting that in our simulation experiments, we employ a separate held-out test set to assess model performance.

Response to reviewer 5Cze

Dear Reviewer,

Thank you for your careful reading of our work and insightful comments. We are glad that you found the paper to be “interesting,” and “relevant.” We address each of the comments mentioned in your Weaknesses, Questions, and Limitations sections below.

Weaknesses

1. We have tried to distinguish between a model being non-identifiable, by which we mean that its parameters are impossible to uniquely infer, and sloppy, by which we mean that its parameters are poorly constrained by available data.

2. Regarding sloppiness, we agree that it could be hard to estimate the parameters of the plasticity rule in practice given finite data sets. Multiple terms in the plasticity rule may lead to similar weight changes. Nevertheless, our paper shows that it is empirically possible to infer plasticity rules given reasonable amounts of simulated data. It also identifies a biologically interpretable but previously unknown term in the plasticity rule of the fly mushroom body. This term would not appear consistently in the statistical fits of individual flies if it was too sloppy to be determined. Simply, our method is already useful, regardless of whether it can detect the sloppiest components of plasticity rules.

3. Regarding identifiability, if one could measure every term that enters the plasticity rule, then the identifiability of the plasticity rule would follow from the uniqueness of Taylor series expansions. Since weights are assumed to be unmeasured, then it’s in principle possible that some plasticity rules may be non-identifiable. This seems unlikely to us, because each component of the plasticity rule contributes to weight changes that measurably affect the postsynaptic activity. Nevertheless, we acknowledge that we don’t have a formal mathematical proof that the plasticity rule is identifiable with unmeasured synaptic weights.

4. In our opinion, identifiability is less relevant than sloppiness, and sloppiness is less relevant than our empirical demonstrations. Our method already works well enough to be applied fruitfully to simulated and real-world problems.

5. We acknowledge the reviewer's concern regarding the potential for overfitting due to the absence of cross-validation. We want to clarify that in our simulated experiments we consistently utilized a separate held-out test set to evaluate model performance - we have clarified this in the main text. However, we recognize the value of incorporating cross-validation for fitting the fly experimental data. If the paper is accepted for publication, we will implement a cross-validation procedure and include it in the final version of our manuscript. We agree with the reviewer that this would substantially enhance the robustness of our model evaluation.

Questions

1. We appreciate the reviewer's observation and have removed the statement about energy implications for training LLMs, as upon further consideration the point seemed tangential to the goals of our paper.

2. We have added text to the caption of Fig 4C to clarify that parameter 001 corresponds to the weight decay term, and have listed what each of the terms mean. The 000 term is a bias.

3. We thank the reviewer for pointing us to the literature that focuses on fitting dynamical models from time-series data, especially the idea that regularization penalties can substantially improve model performance. As the reviewer pointed out, we have begun exploring the L1 regularization penalty in our model, and we are familiar with the related SINDy approach. If accepted, we will incorporate a more thorough investigation of the impact of regularization on model performance, and we will move the relevant text discussing this from the Appendix to the main manuscript.

4. We have already addressed this concern in the “Weaknesses” section of our response.

Limitations

1. The reviewer’s comment regarding connectomics is addressed in the general response to all reviewers.

2. We have already discussed identifiability and sloppiness in our response to the Reviewer’s “Weaknesses” comments. Here the Reviewer additionally brings up “model mismatch,” by which we mean that best-fit model parameters are not directly interpretable if the model parameters are out of accordance with the underlying biology. We agree that this is very often an issue with model fitting, and we certainly don’t claim to have a solution to this general problem. We don’t currently see anything that we could add to the study that would alleviate this concern, and our approach has instead been to illustrate related failure modes. Indeed, the Reviewer points to our figures to illustrate the point, which we think indicates that we’ve given it fair treatment. We are happy to make additional revisions if the Reviewer could clarify what they find problematic about our treatment. The quoted text that the Reviewer provides is about “identifiability,” not “model mismatch,” and we think it is important to keep the related issues of identifiability, sloppiness, and model mismatch distinct as these issues are fundamentally different.

Response to reviewer 2Jtn

Thank you for your constructive feedback on our manuscript. We are glad that you found our work to be “creative,” and “clever and convincing.” Below, we address each of the concerns you expressed in your review, and hope that you will find our revised manuscript to be improved.

Clarity

1. We have added conclusions to paragraphs where this was missing and simplified language that was jargon-filled. These changes are highlighted in red. To help readers understand any remaining specialized language, we added a Glossary before the Appendix. If the Reviewer alerts us to additional terms that they found to be jargon, we would be happy to either eliminate or add it to our Glossary depending on its utility.

2. (Also the response for Question 1) One should interpret the percent deviance explained similarly to the R-squared metric. A value of 0% corresponds to chance performance and a value of 100% corresponds to theoretically optimal performance. It’s useful to our paper because it doesn’t assume continuous outputs or Gaussian noise. It thus applies to binary behavior more naturally than the R-squared metric does. A definition of this metric is provided in Appendix section A3 and we have added a reference to this in the text. We apologize that this reference previously pointed to an incorrect section of the paper.

Quality

1. We agree that the space of plasticity rules is hard to specify and sample in its entirety. We’d like to clarify two related issues.

   • First, we acknowledge that when choosing plasticity rules to simulate ground-truth data, we emphasized canonical models that have been “hand-designed” by the computational neuroscience community due to their properties and biological relevance. Their simplicity reflects the current state of understanding in the field. However, we also simulated a large number of other rules in the Appendix (Table 2) excluding the unstable rules. We chose this naive sampling of plasticity rules because the field does not yet have the knowledge to know what class of rules are most relevant. Given this, a better approach was not clear to us as that the space of simulated rules cannot be sampled exhaustively.

   • Second, we’d like to note that our framework and fitting procedures were designed with the goal of leveraging large-scale biological data to help move beyond hand-designed rules. Our paper’s main assumption is that the plasticity rule is a function of only presynaptic activity, postsynaptic activity, reward, and the current weight value. Our fitting procedures are designed to estimate this unknown function from data. There are multiple ways to parameterize functions, and we consider two parameterizations with complementary strengths. First, we use a low-order polynomial, which can be taken as estimating the Taylor series for the function and is easy to interpret as it relates simply to the canonical rules. Second, we use a multilayer perceptron, which sacrifices interpretability for expressivity. In either case, we’re providing a general parameterization that can reveal unexpected results when fit to biological data.

2. The Reviewer is correct that our method sometimes infers plasticity rules that poorly approximate the weight, activity, and/or behavioral trajectories (Table 2). This isn’t surprising because plasticity rules are nonlinear dynamical systems, and their predictions may show sensitivity to parameters and initial conditions. We would contend that no inference method will be able to perfectly recover an arbitrary plasticity rule. The intention of Table 2 is to merely illustrate the range of possibilities. Nevertheless, we hypothesize that the rules implemented by biology are less unwieldy than some possibilities in Table 2. Indeed, our method works very reliably on the canonical rules that were designed to capture biological phenomena. We hope that using our framework to fit real data will help us to identify novel, well-behaved rules without necessitating laborious hand design.

3. As explained above, we acknowledge that we’ve emphasized tests against simple, plausible learning rules. However, the suite of learning rules in Table 2 include a wide range of ground-truth plasticity rules with nonlinear (polynomial) dependencies among the terms. We agree that applying our method to real data is a productive path forward, and found it very encouraging that the method already uncovered something novel and interpretable in the Drosophila data. We anticipate more discoveries with richer datasets and models.

4. The reviewer’s comment regarding connectomics is addressed in the general response to reviewers.

5. We believe this comment on the simplicity of the synthetic rules has been adequately addressed by our earlier responses.

6. We have added text to Section 3.1 to clarify the interpretation of our choice of ablation experiments. This was guided by the kinds of incomplete information we would likely deal with when applying our model to biological data. Often neural recordings are noisy and even the most state-of-the-art recording tools suffer from not being able to record entire populations of interest. Our ablation experiments quantify how resilient our approach is to these sources of error that are often present in real data.

Limitations

1. We have changed our response to the societal impact question of the NeurIPs checklist and provide a justification for why this is not discussed in the main text. While we have discussed our paper’s impact within the field of neuroscience, the larger societal impact will likely only be revealed as the method is used more widely to understand specific neural systems and their plasticity rules. As an immediate societal impact is exceedingly unlikely, we did not dedicate a section to discuss these issues.

2. A description about the scalability of our approach has been provided in the general rebuttal to all reviewers.