A Multi-Region Brain Model to Elucidate the Role of Hippocampus in Spatially Embedded Decision-Making

We sincerely thank the reviewer for their precious time, and their comprehensive feedback. We deeply appreciate their recognition of the significance and clarity of our work. In summary, the reviewer raised an insight regarding the role of hyperparameters, and made additional comments to help us enhance clarity. We share the hyperparameter tuning results and CAN implementation, which are added to the appendix. Together with the discussion below, does this address the reviewer’s questions?

It would be helpful…how hyperparameters for model training were chosen…A few extra sentences in appendix A.1 should be sufficient. how much would tuned hyperparameters have helped for models that used default hyper parameter configurations?

Thank you for attention to this detail. M0 and M0+ used a different learning rate due to gradient issues (line 681). We share the result on hyperparameter tuning on learning rate (LR) [0.001, 5e-4, 1e-4, 5e-5] (here’s an anonymous colored version: https://imgur.com/a/Ve7B3Mo).

The current set of hyperparameters largely ensures fairly optimized performance, except a slower LR of 1e-4 improves M4 instability in Fig 2. However, none of them changed the claims made in the paper. The table includes mean [success rate]/[exploration time] +- sem at the terminating episode across 3 trials. The highest success rate and the lowest exploration time are bolded for each model.

We also provide an updated Fig 2 with the optimized LRs. The changes are a LR of 5e-5 for M0+ and 1e-4 for M4. This doesn’t alter the conclusion in Section 5.1 regarding M5’s learning efficiency & fast exploration: https://imgur.com/a/U0OVo2H. We'll include this in the appendix.

It would be helpful if the authors could include more equations in the paper, likely in an appendix. For example, the CAN equations...

Thank you for pointing this out. We agree that including more equations would enhance the clarity. If accepted, we will include below in the appendix in the camera-ready version. Specifically, we implement $CAN()$ in Eq. (1), based on the Vector-HaSH repo [1]:

$g(t+1) = \textsf{CAN}[g(t), v(t)] = \mathbf{M} g(t),$

where $\mathbf{M}$ denotes a shift matrix depending on the velocity signal $v$. For simplicity, suppose we have two grid cells with periodicities 3 and 4 and use a single dimension instead of two dimensions (our case). Then, $\mathbf{M}$ is defined as a shift matrix in each grid module as follows:

$M = U = \begin{bmatrix} 0 & 1 & 0 & 0 & 0 & 0 & 0 \\\\ 0 & 0 & 1 & 0 & 0 & 0 & 0 \\\\ 1 & 0 & 0 & 0 & 0 & 0 & 0 \\\\ 0 & 0 & 0 & 0 & 1 & 0 & 0 \\\\ 0 & 0 & 0 & 0 & 0 & 1 & 0 \\\\ 0 & 0 & 0 & 0 & 0 & 0 & 1 \\\\ 0 & 0 & 0 & 1 & 0 & 0 & 0 \\\\ \end{bmatrix}$

if $v$ shifts the bump activity to the right, otherwise $U^T$.

Formally, $M_{i,j} = 1$ if $(j - X_{k-1}) \mod \lambda_k \equiv (i + \text{velocity} - X_{k-1}) \mod \lambda_k$, where $X_{k-1} < i, j < X_k \forall i, j, k, X_k = \sum_{l=1}^{k} \lambda_l$. Otherwise, $M_{ij} = 0$.

2D Vector-HaSH is a simple extension of this to two-dimensional grid states and velocities.

code release.

We appreciate the reviewer’s emphasis on reproducibility and agree accessible code is important for advancing the field. We're finalizing documentation and ensuring the code is well-organized and user-friendly. We remain committed to releasing the full codebase upon acceptance (w/ the camera-ready version).

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[1] https://github.com/FieteLab/VectorHaSH

We sincerely thank the reviewer for their precious time and comprehensive feedback. We deeply appreciate their recognition of the significance of our work. In summary, the reviewer raised an insightful question regarding experimental v.s. model data comparison to strengthen our claims, and our interpretation of task performance, for which we discuss the implication of M5 for studying lapses. We provide results for when we shrink the number of trainable parameters of baselines to match that of M5, which do not alter our conclusion. We have fixed the typos on our end. Together with the discussion below, does this address the reviewer’s questions?

The authors compute the mutual information…in Fig. 6. could they do the same with the hippocampal data from Nieh et al. (2021) and compare the distributions? Something to make it more quantifiable…would strengthen this claim.

Thanks for the insight. We’d like to first refer to Figs S2b, c in Nieh et al., which plot mutual information (M.I.) of hippocampal data, the same as our Fig 6. We share it here for convenience: https://imgur.com/a/acEavag.

This qualitatively matches the results of M3-M5 in Fig 6, showing models with both position and evidence encoded in grid cells give rise to higher ExY M.I. than when one variable is randomized. This makes sense for M4 because M.I. is not a metric for localization. However, as shown in Fig 4, M4 does not match experiments in having choice-specific neurons.

We don’t expect a quantitative match in M.I, because

1. Our environment is discretized;
2. We don’t have the same level of noisiness as the experiments;
3. Real neurons exhibit higher redundancy;
4. The real data is smoothed but we didn’t apply smoothing, hence the scale of M.I. is different. The smoothing also influences the localization in HPC maps.

M0, M0-star, and M4 all solve the task at around 70% at around by the end of training…subsequent results provide additional support for M3/M5…but discussing this aspect of performance (that the mice did not perform the task as well as M3/M5) is important I think.

Indeed, the lapses phenomenon in mice (low performance) is an important ongoing research direction.

While early literature proposed lapses could be due to perceptual noise, more recent work like Ashwood et al., Nat Neurosci., 2022 pointed out that mice might be leveraging different strategies characterized by different states, while Pisupati et al., eLife, 2021 proposed the mice are potentially balancing exploration and exploitation when making mistakes. These statistical models have specific parameters to account for lapses based on their hypotheses and are evaluated based on how well they fit the data. While we find the lapses literature important, we don’t think the low performance of M0, M0+, & M4 would be informative for understanding lapses, as you carefully noted that they are limited in reproducing experimental findings.

While studying lapses is beyond our scope, future studies on lapses could leverage M5, validated as being able to reproduce experimental findings. It’d be interesting to investigate what the key ingredients are to observe lapses while preserving the properties we observed. To our knowledge, a mechanistic model for lapses would be fairly novel. We will include this in our discussion.

Could one reason models M0 and M0-star not perform as well until later in training be due to the fact that they have more weights to optimize over? How does the number of training able parameters differ between M0/M0-star and the other models?

This is a fair point. We focused on an equal number of neurons as a fair baseline for expressivity. Here we found the number of parameters trained by back prop doesn't play a key role:

Assume the total number of parameters in an RNN w/ input size $I$, hidden size $H$, and output size $O$, w/ bias, is $(IH + HH + H) + (HO + O) = H^2 + H(I+O+1) + O,$ then M5 has ~$26,755$ back-prop-trainable parameters. We can apply similar reasoning to M0 and M0+, with $1,172,843$ and $1,174,995$ gradient-trainable parameters. To match M5, M0 would have $H \approx 158$ and M0+ would have $H \approx 157$.

We ran these mini-models for 3 trials each: the conclusion in the main paper stays the same. Plz see the anonymous results here with mini-M0 & mini-M0+ (red and orange, w/ learning rate of 1e-5), in comparison with M5 and original M0 and M0+: https://imgur.com/a/Qr5MmT4

Supplement: mini models w/ other learning rates, no change of conclusions: https://imgur.com/a/vCD2HRG

We notice our use of M0-star & M0+ interchangeably; we will use “M0+” consistently.

Other Comments

Thanks! We'll ensure a consistent notation h. We’ll modify “lacunae” to gaps and correct the sentence.

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Ashwood, Zoe C., et al. "Mice alternate between discrete strategies during perceptual decision-making." Nature Neuroscience (2022).

Pisupati, Sashank, et al. "Lapses in perceptual decisions reflect exploration." Elife (2021).

We deeply appreciate the reviewer’s precious time & comprehensive feedback. We sincerely thank them for recognizing the significance & clarity of our work. The reviewer raised questions on the support for our claims, method novelty, and the biological grounding of models. Here we clarify with the relevant content in the paper. Together with the discussion below, does this address the reviewer’s concerns?

The model is largely an adoption of the Vector-HASH+... I do find the neural predictions and hypotheses interesting, but…limited in terms of methodological novelty.

Thanks for acknowledging our findings. The architecture is based on Vector-HaSH (VH, Chandra et al., Nature, 2025), but the “+” part is our original development (lines 215-218). We emphasize our application-driven work is among the first to apply VH systematically, with appropriate adaptation (e.g., the “+” part), to understand spatial decision-making w/ experimentally verifiable predictions. Similar studies exist w/ RNNs but lack the necessary bio details in modeling multi-region circuits.

...I accredit the authors' mechanistic attempt, but I personally find many claims made in the paper to be ungrounded, and no sufficient ablations exist to support...

Our M1-M5 are ablations of multiple hypothesized multi-region interactions. We refer to VH (Chandra et al., 2025) for the detailed bio grounding as they’ve substantially addressed them. We ensured further claims are supported w/ evidence. We address below the reviewer's specific concern on the sensory criticality claim, but happy to elaborate on other claims if needed:

The authors make claims about the criticality of sensory inputs from lEC in driving efficient learning and spatial navigation. However, I cannot draw such conclusion from Fig 5. The lack of qualitative comparison with M3…undermines the validility of the authors' claim.

The sensory criticality claim is made for efficient navigation & low-d representation, not for learning. The navigation aspect is evident in Fig 2B (M3 vs M5) & lines 304-314; low-d representation aspect is in Fig 5, w/ M3 in Appendix E, referred to in line 413. Joint grid code is critical to efficient learning (M3 & M5 in Fig 2A, lines 299-303).

The authors assumes direct projections from lEC and mEC consistutes the firing of place cells. How could the authors enforce sparsity and spatial selectivity in place cells?

Relevant bio groundings are inherited from & addressed in VH (Fig 6 in Chandra et al., 2025), so we didn’t reiterate. We'll include these details in the appendix:

Sparsity: Per line 200, $W_{hg}$ is a random projection matrix generated by standard Gaussian distribution (Method in Chandra et al. (2025)), so half of the activation is 0 on expectation. The input is sparse as the firing of each grid module is one-hot per model inductive bias (line 208). ReLU is applied to h (eqns 2 & 3) to also enforce sparsity.

The number of unique grid states ($\prod \lambda^2_i$) is much smaller than the number of unique activated HPC states ($2^{N_h}$), so only a small number of HPC cells are >0.

Selectivity: Each sensory state is associated w/ a specific grid state by updating $W_{hs}, W_{sh}$, so each sensory state is only associated with certain HPC states.

…M0 and M0+ models do not yield good performance could due to poor implementation of the recurrent structure. I can imagine a recurrent networks designed for temporal integration…will be able to perform the task whilst not requiring the complicated EC-HPC network...think this is an unfair comparison...

Vanilla RNN is fairly powerful & extensively studied, e.g., Yang et al., Nat Neurosci, 2019 & Driscoll et al., Nat Neurosci, 2024 applied RNNs to NeuroGym tasks with temporal components.

And, our goal is to assess the added value of the structured EC-HPC networks, not to benchmark arbitrary network classes; changing the recurrent structure of baselines necessitates changing M1-M5’s RNN for fair comparison. This would be unnecessary and defeat the purpose of isolating the inductive bias introduced by EC-HPC circuits.

Our work highlights the utility of leveraging VH as a hypothesis-generating testbed to study the entorhinal-hippocampal-cortical network. A task-optimized recurrent structure misses the necessary bio details.

...useful to apply the model to other tasks…validity of the model...two-armed bandit...

The validity of the model is grounded in Chandra et al. (2025), and we emphasize the depth, not breadth, of results since

1. Our scope is spatially embedded decision-making with phenomena specific to HPC & related circuits. e.g., two-armed bandit task doesn't study the spatial aspect of HPC.
2. The tower task is justified for many reasons noted in lines 36-63, e.g., we focus on this task to integrate our findings into a larger cohesive narrative that transcends the inherent scope limitations of stand-alone studies on arbitrarily chosen tasks.

We sincerely thank the reviewer’s precious time and comprehensive feedback. We deeply appreciate their generous recognition of the significance of our work. The reviewer shared an interesting insight regarding comparison with advanced AI models, and had a clarifying question on how our setup and findings compare with the biology. Here we address both. Together with the discussion below, does this address the reviewer’s questions?

One major limitation is that the work is mostly biologically driven, as it claims to an efficient brain-inspired reinforcement learning rule, while it does not directly compare with existing models in artificial intelligence sides.

Thanks a lot for the insights, and we agree having some comparison with advanced AI models could be quite interesting to see if brain-inspired models could perform SoTA in the standard machine learning benchmark (e.g, image classification, Atari). However, our main focus is to design a biologically-inspired model that can be applied to explain neuroscience experiments. This objective is aligned with previous neuroscience-application studies that only use simple RNNs as baselines published in top ML venues (e.g., Miller et al., NeurIPS, 2023; Valente et al., NeurIPS, 2022).

Any model designs do not directly follow biological constraints, or findings are not aligned with experimental discoveries?

We think the biological constraints can be assessed through

1. the information flow among regions, and
2. the representation produced by the model.

While there are not sufficient neuroscience experiments (to the best of our knowledge) revealing the exact information flow among regions in the context of spatially-embedded decision-making tasks, M1-M5 are all reasonable hypotheses of (1) given the current neuroscientific understanding (elaborated in Section 4). However, as presented in our paper, M1, M2, M4 did not produce experimentally aligned representations (e.g., Figs 4, 8).

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Miller et al. "Cognitive model discovery via disentangled RNNs." NeurIPS. 2023.

Valente et al. "Extracting computational mechanisms from neural data using low-rank RNNs." NeurIPS. 2022.