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Under review as a conference paper at ICLR 2027

Aligning cognitive and neural mechanisms in tiny recurrent neural networks

Abstract

A central goal of computational neuroscience is to develop models that both accurately predict behaviour and reveal the cognitive and neural mechanisms that generate it. Tiny recurrent neural networks (RNNs) with few hidden units have helped reconcile these demands, combining predictive flexibility with interpretable dynamics. However, although choice logits and their update dynamics are reproducible across fits, this does not imply reproducibility of the internal mechanisms that generate them. Here we show that tiny RNNs fit to subtly different training data (e.g. different cross-validation folds) can yield very different internal update mechanisms and hidden state trajectories, despite near-identical choice logits. This precludes using internal variables from tiny RNNs as candidate mechanisms underlying cognitive and neural computations. Here, we characterise this problem across tiny RNNs trained on behavioural data from mice performing a probabilistic reversal learning task, then demonstrate how a series of biologically inspired constraints can greatly improve mechanistic reproducibility without compromising behavioural predictions. We were then able to interpret these mechanisms to explore possible computations in fronto-striatal circuits. Our results highlight mechanistic reproducibility as a complement to predictive accuracy and interpretability, and provide a framework for using RNN-derived variables to explore hypotheses about behavioural and neural dynamics during flexible decision-making.

Primary area:
applications to neuroscience & cognitive science
Keywords:
computational neuroscience, recurrent neural networks, cognitive modelling, interpretability, mechanistic reproducibility, biological constraints

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_JdVnOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

The paper attempts to highlight a particular issue which faces cognitive (computational) neuroscientists when fitting small models to data. As an example they fit tiny (1–2 unit) gated RNNs to the choices of mice performing a probabilistic reversal-learning task. It shows that, across different data folds, standard GRUs can produce near-identical choice logits while their weights and hidden-state trajectories differ (solution degeneracy, in the words of the authors). This effectively shows that these models cannot be used out of the box for research in which one attempts to treat hidden variables as useful readouts for cognitive mechanisms. The authors then propose the introduction of biological constraints and model restrictions, ultimately arriving at “monoGRU”: a GRU unit with ReLU activations, an energy penalty, a weight sparsity inducing mechanism, no reset gate, a single scalar update gate and no decoder bias. They report that its weights and hidden states are much more similar across fits with no loss of predictive performance, allowing more clear interpretation of it’s hidden states in terms of cognitive mechanisms.

Critical strengths

First, the setup of the problem in the Introduction and the first half of Section 2 (up to Table 1) gives a clear and good reasoning for how one cannot treat trainable algorithms with a high degree of expressivity and necessarily expect that they will find a consistent solution across folds. It also helps to illuminate this very important problem in cognitive computational neuroscience: the danger of fitting overly expressive models to data and then interpreting them in a mechanistic fashion.

Second, the manner in which comparisons are made, via nested cross-validation and within vs between subject statistical testing appears appropriate and well constructed and well presented.

Critical weaknesses

First, when shifting from posing the problem to posing a solution (in the final form of monoGRU) the work passes through an undesirably handtuned, non-generalizable, and non-rigorous process. The authors introduce a range of interventions on the model (biological constraints (BC), decoder bias (DB) removal, and light vs mono GRU) without much of an explanation as to why these are the set to choose over or how another practitioner could hope to make similar choices. Furthermore, the choices of biological restrictions and simplifications are not organised, ordered, or rigorously searched. The appendix shows that a specific subset of combinations were checked but even these do not cover all possible options (e.g. lightGRU+BC−DB is missing, as is monoGRU−DB-BC among others). Therefore it is not possible to isolate which interventions are responsible for the effects seen. In effect this leaves the results of this model search as seeming to be a random set of uninterpretable choices which cannot be guaranteed to produce the same effect if applied to an alternate task’s data.

Second, it is unclear whether the statistics and approaches used might favour the models selected in the end. Models trained with Tanh non-linearities are allowed permutations and sign-flipping when finding equivalent parameterizations. This is equivalent to allowing their input weights to be permuted or to be sign reversed only. ReLUs are instead allowed permutations and scaling. However, scaling of ReLUs allows for a much greater degree of tuning of the alignment between models than tanh can possible achieve. This leaves me, as a reader, unsure if the alignment statistics might be skewed toward ReLU non-linearities from the outset. Furthermore, some alignment statistics are being computed for weights and update gates, however are these not of different shapes depending upon the model’s construction (GRU vs monoGRU)? If so, how can alignment be compared across these methods?

This leads to a third and final consideration which is missing: the models are never compared in parameter matched cases. When simplifying from a GRU to a monoGRU or light GRU the number of parameters in the model change. This is already a reduction in the level of overparameterization of these models. Parameter matched model comparison is a norm in machine learning and neuroscience when comparing methods, therefore it seems that some of these comparisons might be unfair from the outset.

Questions for authors

Did you also test a range of regularization methods in isolation? Regularization is also a method which is commonly used to restrict the set of solutions found by trained models (linear or otherwise).

Do you think the alignment of your models might have also (independently) gotten better with more data? One common effect in model training is the effect of an underdetermined solution if there is insufficient data.

Was your search over models principled in anyway? How did you make choices about what to ablate or remove from models and what to add to the objective function when searching for a model without such degeneracy?

Note, there are a few textual issues with your work including:

  • Citations missing brackets throughout the paper (see L134/L135/L177/L280-281 etc)
  • “Hidden units accumulate integrate reward history” (L265) is not a parsable sentence
  • L288-289 use of a colon is weird
Reviewer_DXvBOpenReview ↗
Rating
1
Confidence
4
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

This paper investigates whether recurrent neural networks fitted to the reversal-learning behavior of mice can develop reproducible internal variables when trained independently. While standard two-unit GRU models can produce highly similar choice logits, their weights and hidden-state trajectories often differ significantly. The authors propose a monoGRU model, characterized by non-negative hidden-state activity, a regularization mechanism, a shared update gate, and the absence of both a reset gate and a decoder bias. In experiments involving 11 mice, the monoGRU model demonstrated greater consistency in weights and hidden-state trajectories compared to the standard GRU, with comparable choice-prediction performance in the reported comparison. The authors interpret the difference between the two hidden-unit activations as action preference and their sum as recent reward history. Furthermore, they link these variables to behavioral initiation latencies, as well as to dopamine photometry signals recorded from the medial frontal cortex and the nucleus accumbens.

Critical strengths

This paper examines a significant failure mode in interpretable behavioral models: high consistency in predicting behavioral choices does not necessarily imply reproducible internal states. Accounting for the inherent symmetries of the model, the study compares independent fits derived from different data folds and individual experimental mice.

Critical weaknesses

The submitted files contain several unresolved inconsistencies and incorrect cross-references that impede verification of the proposed mechanism and training protocol: (i) Lines 256–264 of the main text conflict with Appendix B.3. (ii) The definitions of the energy coefficients and the sparsity coefficients are inconsistent between Equation (2) in the Supplementary Material and Table 3. (iii) The main text references an "Appendix D" that does not exist (line 272), and several other citations to figures and appendices point to the wrong content (e.g., Figure 5 is incorrectly cited as Figure 6, and references to training loss point to A.4 instead of A.3). (iv) The final paragraph breaks off mid-sentence. While any one of these issues might be attributed to editorial mistake, their cumulative presence raises serious concerns: Is the manuscript complete? Can the mechanisms and training protocols described therein be reliably interpreted or reproduced? 2. The robustness of the neural conclusions across alternative behavioral-model fits has not been established. The core of the issue is that distinct internal variables can yield similar predictions regarding choice behavior. Appendix C derives the dopamine-regression predictors from a single two-unit monoGRU fit per mouse (inner fold 9, outer fold 10). Although three-fold cross-validation is used to select the Lasso penalty, the neural analysis is not repeated across alternative RNN fits to assess the stability of the results. The researchers extrapolated the reproducibility of certain internal variables—observed during behavioral model fitting—to the interpretation of neural data, without verifying whether the directionality, temporal dynamics, and statistical significance of these variables remained consistent across different model fits. Moreover, Figure 5 presents coefficient trajectories rather than the incremental explanatory power—relative to task history or a simple reinforcement learning baseline—on held-out data. While these results establish correlations, they fail to distinguish whether a specific neural mechanism is at play, or if the findings merely reflect a constrained representation of the relevant behavioral history.

Questions for authors
  1. For each mouse, if the dopamine regression analysis is repeated across ten outer-fold monoGRU model fits , how stable are the results? Please report across-fit variability in effect sizes, signs, and temporal profiles, and explain why inner fold 9 / outer fold 10 was used for the reported analysis.
  2. The model is updated on each trial based on the cue, action, and outcome, without taking elapsed time as an explicit input. Consequently, while the sum of two hidden states can track recent rewards per trial, it cannot, on its own, distinguish between scenarios where the sequences of trials are identical but the rates at which they occur in real time differ. Since the vigor argument invokes average reward per unit time, does the sum correlate with a past-only, time-normalized reward-rate estimate, and does it explain initiation latency beyond that estimate? If not, please explicitly define the reward rate, rather than equating it with a time-based metric as understood in average-reward theory.
  3. Please reconcile the action-row ordering and hidden-unit labels across the text, figures, and appendix. Explain the inconsistency between the main text and Appendix B.3. Furthermore, in the context of the actual experiment, which parameter represents the energy penalty? Clarifying these points is essential for interpreting and replicating the proposed mechanism.
Reviewer_SKWgOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper fits 1–2 unit GRUs to the probabilistic reversal learning behaviour of 11 mice, and reports that logits are more reproducible than weights and hidden states, with the largest gap in the across-subject comparison. It then applies minimal biological constraints, reduces gating to a single scalar update gate and removes the decoder bias, obtaining a 2-unit, 22-parameter monoGRU, and reports that this greatly improves similarity across fits without compromising behavioural predictions. It interprets h1−h2h_1-h_2 and h1+h2h_1+h_2 as action preference and reward history, and relates them to mFC/NAc dopamine.

Critical strengths
  1. The paper compares the similarity across fits of logits, weights and hidden states in tiny RNNs fitted to behavioural data (pp. 2–3); the means in Table 1 show logits above weights and hidden states. The paper then uses minimal biological constraints and architectural simplification to obtain monoGRU, and reports improved reproducibility without compromising prediction (p. 2, pp. 4–5). This allows "getting the prediction right" and "getting the mechanism right" to be assessed separately on the same set of fits, and provides a concrete architecture that can be reused directly.
Critical weaknesses
  1. Architecture selection and the similarity test in Table 1 share the same source. monoGRU was selected by similarity across fits from the same family of candidates (p. 4), and Table 1 performs the GRU vs monoGRU test on the same set of similarities. The three similarity measures (aligned-weight cosine, and the Pearson correlations of hidden states and logits) are not the same ruler, and the paper provides no null or ceiling, so the magnitude of the cross-architecture weight-similarity comparison cannot be judged.
  2. The abstract's wording and the reported readings do not align. The abstract gives "different cross-validation folds" as its example, whereas the largest gaps in Table 1 come from the across-subject rather than the within-subject across-fold comparison; "without compromising" has only one inferential support, a paired test.
Questions for authors
  1. monoGRU was selected from the same family of candidates by "highest similarity across models, both within and across subjects", and Table 1 tests GRU vs monoGRU on the same similarity measure, while the inner criterion in A.2 is the negative log-likelihood on free choice trials. Can the authors provide a validation independent of model selection (for example, comparing GRU and monoGRU similarity on subjects or outer folds that took no part in architecture selection), or state whether one of the existing 10 folds was held out for the architecture-level test; if so, does the similarity difference persist under that held-out comparison, and by how much?
  2. What readings support "can greatly improve mechanistic reproducibility" for the update gate and the reset gate? The scalar update gate is the core of this architectural simplification, yet in Table 1 the Update Gate has no stars in either column (the text also states "no significant difference"), and the reset gate is removed rather than improved. If the claim were restricted to weights and hidden states, how would the abstract's wording change?
  3. The abstract gives "different cross-validation folds" as its example of the source of variability, whereas the large gaps in Table 1 for weights and hidden states appear in the across-subject comparison (GRU: within-subject 0.77/0.87 versus across-subject 0.49/0.64); what are the effect sizes of the two sources of variability, the same subject across folds and across subjects?
  4. The introduction already cites the solution-degeneracy line (Huang et al., 2025; Maheswaranathan et al., 2019; Turner et al., 2021), but without a quantitative comparison: relative to these quantified accounts of degeneracy, what does the "same subject, different cross-validation folds" source of variability add?
  5. For "without compromising behavioural predictions", can the authors provide an equivalence test (TOST), an effect size with confidence intervals, or an upper bound on the difference in negative log-likelihood? What power does this paired 2-unit test have at n=11n=11 for a pre-specified effect size, and what is the smallest effect it could detect?
  6. The latency regression in Figure 5a contains only h1+h2h_1+h_2, ∣h1−h2∣|h_1-h_2| and their interaction, whereas the dopamine regressions in Figure 5b/c simultaneously include rewardtreward_t, rewardt−1reward_{t-1}, contralateral choice, forced choice, the previous hidden-state sum and the chosen-action logit (defined in Appendix C as the signed Li−1L_{i-1}). Is there a methodological reason for the different covariate sets? If the same task events were added to 5a, would the latency coefficients change?
  7. The mFC and NAc samples are 9 and 10 mice respectively (behaviour n=11n=11). What determines inclusion in the neural analyses (for example recording availability, signal-quality thresholds, or task-performance criteria)?
  8. The caption on p. 6 states that hidden units are "aligned across subjects according to their decoder contributions favouring A1 or A2"; if h1/h2h_1/h_2 were assigned using the Frobenius-norm-minimising alignment of A.4 (a model-to-model weight alignment) instead, would the axis-aligned representation in Figure 4a (miscited as Figure 3a on p. 6) still be supported?
  9. The weight similarity in Table 1 depends on the alignment enumeration of A.4: the enumeration is exhaustive for the tanh of GRU at H=2H=2 (2!×222!\times 2^2), but only discretized for the positive rescaling of monoGRU's ReLU. Is the cross-architecture weight cosine comparable under this enumeration? If a continuous positive-rescaling alignment were used for ReLU, how much would monoGRU's weight similarity change?
  10. In the neural analyses of Figure 5, each mouse contributes only one monoGRU fit (inner fold 9, outer fold 10), and the Lasso λ\lambda is chosen on the same neural data by three-fold CV with shuffled trial splits (a random partition of trials); are the coefficients in Figure 5b/c stable under other folds or under nested λ\lambda selection? The pp values of non-overlapping groups of three adjacent 50 Hz bins are combined with Fisher's method, which assumes independence. Is there evidence that neighbouring bins are independent (for example residual correlations between bins), and how would the reported significance change under a combination that does not assume independence?

Comments on the paper

1 comment

We would like to thank the reviewers for their detailed and constructive feedback. We have decided to withdraw the submission at this stage, but your comments will be valuable in updating the work for a future submission. 

We note that the previous upload was not reflective of the finished manuscript; this was an editorial mistake made during upload. We have since replaced this with the revised manuscript that both addresses the comments made relating to this, as well as the vast majority of all three of the reviewer’s comments.

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

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